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    1. Author response:

      The following is the authors’ response to the original reviews.

      Reviewer #1 (Public review):

      Summary:

      The authors aim to characterize Huntingtin (HTT) aggregates in various cells and tissues and propose that mutant polyQ HTT (mHTT) assembles at the Golgi apparatus, thereby impairing Golgi organization and function. They further suggest that such Golgi defects might contribute to disease pathology, including neurodegeneration.

      Strengths:

      The study spans a wide range of disciplines, including genetics, cell biology, neuroscience, and systems biology, and employs diverse methodologies such as iPSC, 3D SIM microscopy, omics approaches, organoid culture, electrophysiology, and antisense depletion.

      Weaknesses:

      While the breadth of techniques is impressive, the central premise of the work-the structural and functional relationship between polyQ assemblies and the Golgi apparatus-is not supported by sufficiently rigorous cell biological evidence.

      A major concern is that much of the cell biology data remains descriptive and lacks mechanistic depth. The findings are fragmented and not integrated into a coherent molecular or cellular model. Instead of building a logical progression of experiments, the study presents a collection of observations that appear disconnected and, at times, driven more by technical capability than by hypothesis-driven design.

      Critically, the key claim that polyQ HTT functionally disrupts the Golgi (Golgipathy) is not convincingly demonstrated. Many observations could be more simply explained by the polyQ HTT localization to the Golgi and known Golgi sensitivities to perturbations (e.g., starvation or Brefeldin A treatment), rather than by a specific mechanistic role of polyQ HTT.

      The manuscript also suffers from issues in organization and clarity, including imprecise descriptions and figures that are difficult to interpret.

      We thank the Reviewer for their time, valuable comments, and recognition of our technical expertise and resources. With our specialized background in pathology and super-resolution microscopy, our research heavily relies on structurally precise histological methods to address these fundamental biological questions. Furthermore, our laboratory maintains one of the largest repositories of patient-derived and healthy control fibroblasts, as well as iPSC lines, within the Huntington's disease (HD) research community. Because these patient-derived and engineered cell models express endogenous mutant HTT (mHTT) within an authentic genetic background, they provide a uniquely powerful system for decoding HD pathogenesis.

      We appreciate the Reviewer’s comment regarding hypothesis-driven design. Classically, a hypothesis-driven approach relies on well-established, highly stable experimental platforms. However, a key finding of our study is the highly fragile and volatile nature of polyQ assemblies, particularly when subjected to post-fixation and oxidative stress. Because these structures can behave unpredictably under stress, we utilized an unbiased, data-driven approach leveraging our high-resolution imaging pipeline to explore polyQ assemblies in both healthy and HD cells.

      Importantly, hypothesis-driven and data-driven methods are complementary rather than mutually exclusive. For instance, if a real-time tracking method were developed to label native HTT in living cells endogenously, it would open the door for direct hypothesis testing regarding polyQ assembly mechanics. Despite the current technical limitations of the field, our study successfully overcomes these challenges to reveal the spatial tomography and unique dynamics of polyQ assemblies directly within patient-derived cells. We fully discussed the limitations of this research in the discussion section.

      We appreciate the Reviewer’s critical assessment regarding the functional disruption of the Golgi apparatus (Golgipathy). To rigorously investigate this phenomenon, we employed a comprehensive suite of methodologies ranging from live-cell imaging to single-cell RNA sequencing. In the revised version, we evaluated the glycosylation levels of the Golgi apparatus in HD fibroblasts and brain organoids, and the results revealed that the glycosylation of the HD Golgi is deficient compared with healthy cells (please refer to Fig. S2G-I and Fig. 6G, H in the revised version). Our findings also build directly upon a well-established body of literature. We previously demonstrated that mutant huntingtin (mHTT) disrupts Golgi function within the neural tubes of human cortical organoids (hCO) (Liu et al., 2024), aligning with broader neurodevelopmental defects observed in HD (Barnat et al., 2020).

      Furthermore, prior independent studies have confirmed that both HTT knockdown and the presence of mHTT impair Golgi-to-plasma membrane trafficking, notably in primary fibroblasts from homozygous Htt<sup>140Q/140Q</sup> knock-in mice (Brandstaetter et al., 2014); mHTT also affects post-Golgi trafficking of proteins (del Toro et al., 2006). Backed by this literary consensus and our own multi-modal data and our additional data in the revised version, which Reviewer 2 also noted as sufficient, we are confident that our manuscript provides a robust, multi-layered demonstration of mHTT-induced Golgipathy. In this study, we found that polyQ assemblies and the Golgi form a Golgi-polyQ complex mediated by ARF1 and ARFIP2. Thus, the structural coupling of polyQ assemblies with the Golgi apparatus under starvation and during the cell cycle is rational. Based on the reviewer's suggestion, we have completely revised the entire manuscript. Hopefully, this revision meets the requirements of smoothness and clarity.

      Major Concerns:

      (1) Golgi localization

      The localization of polyQ HTT relies entirely on the antibody 3B5H10, which is foundational to the study. However, previous reports using the same antibody have described predominantly cytosolic localization. This discrepancy must be addressed rigorously by independent validation using alternative antibodies or tagged, exogenously expressed polyQ HTT constructs that should be shown to colocalize with 3B5H10 signals.

      Despite historical inconsistencies across existing publications (Barnat et al., 2020; Hickman et al., 2022; Shen et al., 2019; Tousley et al., 2019), we noticed that the immunostaining results of multiple HTT antibodies are consistent with our data (DiFiglia et al., 1995; Ko et al., 2001; Velier et al., 1998; Wheeler et al., 2000). Although these pioneering studies lacked modern 3D high-resolution imaging and standardized staining protocols, their reported 2D distribution patterns heavily resemble our results. For instance, transmission electron microscopy (TEM) immunolabeling originally revealed that HTT localizes along Golgi cisternae (DiFiglia et al., 1995) and forms organized and parallel fibrils (DiFiglia et al., 1997). Furthermore, immunostaining with a panel of distinct antibodies, including MV2, 3, 4, 5, 6, and 1F8, demonstrated characteristic Golgi-like distribution patterns for HTT (Ko et al., 2001). In addition, our polyQ antibody immunostaining in human fetal brain, which is reflective of polyQ assembly, is nearly identical to the staining results of Barnat et al., publication in Science (Barnat et al., 2020).

      We have carefully checked two early publications, which reported that 3B5H10 only binds expanded polyQ but does not bind normal polyQ (non-disease-causing), which displays a part of a neuron that has a cytosolic diffuse pattern of HTT in 3B5H10 staining (Legleiter et al., 2009; Miller et al., 2011). Based on our extensive experience with HTT immunohistochemistry, we hypothesize that this diffuse signal may reflect nonspecific background artifacts, often caused by high antibody concentrations, poor tissue fixation, inadequate post-incubation washing, or the presence of effete cells, or premature fragmentation of the polyQ tract prior to staining. Interestingly, Miller et al. utilized a rapid tissue-perfusion and sectioning protocol originally published in Brain Research Bulletin (Ko et al., 2001), which is optimized to preserve intact polyQ assemblies. When reviewing the original Brain Research Bulletin study (Ko et al., 2001), we noted that the immunostaining profiles for polyQ-containing HTT peptides (specifically using antibodies MW2, MW3, MW4, MW5, and 1F8) are entirely consistent with our data, yet completely diverge from the patterns reported by the Muchowski group (Legleiter et al., 2009; Miller et al., 2011) (please refer to the following images). Furthermore, contrary to the Muchowski group's claims, subsequent biophysical evidence by Owens et al. (2015) independently confirmed that 3B5H10 binds to both normal and expanded polyQ sequences in huntingtin exon 1 fusion proteins (Owens et al., 2015). Together, these observations strongly support the validity of our staining profiles.

      Several antibodies, including MV1, 1C2, and 3B5H10, were previously reported to recognize the expanded, pathogenic polyQ tracts of HTT (Khoshnan et al., 2002; Miller et al., 2011; Wang et al., 2008). However, emerging studies reveal that these antibodies actually bind both short and long polyQ sequences (Klein et al., 2013; Owens et al., 2015). Because a standard antibody Fab epitope typically spans only 5 to 15 amino acids (or 3 to 4 sugar residues), and normal HTT polyQ repeats range from 18 to 24, it is theoretically impossible for an antibody to exclusively target expanded polyQ while sparing normal polyQ.

      We previously noticed that 3B5H10 antibody immunostaining signals are located in the long projections of striatal neurons. As we did not notice an intact neuron in the two publications, we have no idea about the 3B5H10 antibody signals in the neuronal projections of those images that you mentioned.

      We investigated whether the polyQ assemblies detected by the 3B5H10 antibody contain full-length or large fragments of huntingtin (HTT). To test this, we selected two distinct HTT antibodies: EM48, which binds the first 256 amino acids (excluding the polyQ stretch), and 3E10, which targets the HDA region (amino acids 1171–1177). In patient fibroblasts, the immunostaining patterns for both EM48 and 3E10 were nearly identical to those observed with 3B5H10. These results demonstrate that the polyQ assemblies in fibroblasts are primarily composed of HTT proteins (see Author response image 1). We have included the results of EM48 and 3E10 immunostaining in the revised version.

      Author response image 1.

      (A) GFAP and EM48 antibody staining of the astrocytes derived from HD patient and healthy sibling iPSCs showed polyQ assembly in the astrocytes derived from iPSCs. (B). The spindle of polyQ assembly formed a dent on the nuclear surface of astrocytes. (C, D) Co-immunostaining of GM130 antibody with 3E10 or EM48 antibody in fibroblasts revealed that polyQ assemblies contain a large amount of HTT. The middle and right panels are sectional views of the boxed region (D), and the boxed region is the magnified or rendered part (C, D).

      We also checked whether the transfected exogenous HTT fragment of the first exon can be recruited into polyQ assemblies. We transfected fibroblasts with three vectors of the HTT first exon containing 19, 23, and 74 CAGs, respectively. The exogenous HTT fragments of the first exon did not significantly recruit into endogenous polyQ assemblies-Golgi complexes of fibroblasts (please refer Figure 1-figure supplement 1F-G). We also included this part in the revised version.

      In the cover letter, we told the editor that we have been studying this structure for over ten years. The results have been stable for over ten years.

      Furthermore, the Golgi is identified solely using GM130, a cis-Golgi and ER exit site marker. This raises ambiguity: does polyQ HTT associate with the entire Golgi or only recruit GM130? Could the observed signal correspond to a sub-Golgi compartment?

      Thank you for highlighting the precise sub-Golgi localization of GM130 as resolved by electron microscopy. We agree that transmission electron microscopy (TEM) demonstrates GM130 is restricted to the cis-Golgi network, intercisternal regions, and tubular structures, and is absent from the trans-Golgi (Nakamura et al., 1995). Given that individual Golgi cisternae measure approximately 20 nm in width, resolving cis- versus trans-Golgi sub-compartments exceeds the physical resolution limits of our microscopy system. Consequently, GM130 was utilized here as a robust, widely accepted pan-Golgi marker rather than a tool for sub-compartmental differentiation. To specifically evaluate the trans-Golgi network (TGN), we tracked Clathrin+ vesicles, which actively sort at the TGN (Klumperman, 2011). Our Clathrin staining confirms that polyQ assemblies localize to both the cis- and trans-Golgi compartments, as clearly demonstrated in the new lateral view projections provided in revised Figure 4C.

      If polyQ HTT is indeed Golgi-associated, several key observations become expected rather than novel. For example, in Figure 4I-M, sensitivity to Brefeldin A is unsurprising, as Golgi structure collapses upon such treatment; in Figure 4N-O, co-fragmentation with the Golgi is expected under Golgi-disrupting conditions.

      We agree that our data demonstrate the formation of a functionally coupled polyQ assembly–Golgi complex. Physically and structurally, the dynamics of polyQ assemblies are intrinsically linked to Golgi dynamics under distinct physiological states, including cell cycle progression and energy deprivation. This structural coupling is mediated by ADP-ribosylation factor 1 (ARF1). Specifically, the polyQ tract of HTT interacts with ARFIP2, which is one of the key effector proteins that physically bind active ARF1. Mechanistically, ARF1 is recruited to the Golgi membrane upon GDP-to-GTP exchange catalyzed by guanine nucleotide-exchange factors (GEFs). Consequently, treatment with Brefeldin A (BFA)—which inhibits ARF1 activation—effectively decouples the polyQ assemblies from both intact and fragmented Golgi structures.

      Regarding the question of novelty, we define experimental novelty based on generating entirely unprecedented, empirical data that either confirms or redefines biological expectations, rather than evaluating conceptual expectations themselves. We believe the uncovering of this real-time, stimulus-responsive coupling mechanism provides fundamentally novel insights into HTT biology.

      (2) 3D rendering

      The extensive use of 3D rendering appears unnecessary and, in some cases, misleading. The rendered images do not provide additional insight beyond conventional 2D fluorescence images. Serial 2D fluorescence sections should be more objective in representing the 3D organization.

      Thanks for pointing out the 3D rendering. While 3D rendering provides an essential spatial approximation of fluorescently labeled architectures, it offers significantly more precise structural information than conventional 2D or serial section imaging alone (Cao et al., 2023; Han et al., 2021; Hexige et al., 2015). A primary objective of our study was to evaluate these subcellular features within their intact, native three-dimensional context rather than relying solely on two-dimensional cross-sections. Crucially, without complete volumetric rendering, it is mathematically and visually challenging to accurately delineate complex morphological features, such as the nuclear gorge or true intranuclear accumulation. Consequently, 3D volumetric analysis and rendering are indispensable for the accurate interpretation of the structural data presented in this study.

      In Figure 2A and Figure 5A, red line features in 3D beige polyQ HTT structures resemble unrelated biological structures, such as vasculature, which is inappropriate.

      We would like to clarify that there is no vasculature present within the referenced 3D rendering. The features the reviewer is highlighting are artifacts of the pseudo-coloring used exclusively to mask and visualize the surface tomography. In volumetric 3D rendering, pseudo-colors are assigned strictly to enhance visual clarity and contrast for the reader; they carry no intrinsic biological meaning or cellular identity. Furthermore, from a structural standpoint, the narrow red features in the rendered image are orders of magnitude smaller than true microvasculature. Functional microvessels possess a minimum diameter of 6 to 45 micrometers and exhibit a defined vascular lumen, endothelial cells, a basement membrane, pericytes, and a tunica intima. Therefore, based on both the scale of the image and established histological criteria, these features cannot biologically or structurally represent vasculature.

      There is also an inconsistency in rendering. For example, fine mesh-like structures are shown in some figures (e.g., Figure 2A, Figure 4A), whereas others appear as amorphous aggregates (e.g., Figure 5A, Figure S2B), without explanation.

      The selection of opacity and color masks in our 3D volumetric reconstructions is systematically chosen to optimize the visual clarity and spatial relationships between intersecting sub-cellular structures. For example, as shown in the fourth and fifth panels, an opaque blue mask was applied to define the outer surface tomography clearly. Conversely, in the third panel, a semi-transparent blue mask was utilized for the nucleus. This transparency is methodologically necessary because a subset of polyQ fragments is embedded within or localized directly inside the nuclear envelope; a transparent mask allows for the unambiguous visualization of these internal structures. Similarly, the inset in Figure 5A illustrates the distinct intranuclear occupancy pattern of polyQ, which also necessitates a transparent nuclear boundary. Collectively, these volumetric rendering strategies provide critical spatial and structural depth that cannot be captured by conventional 2D cross-sections or unconstructed serial imaging.

      (3) Quantification of area and volume

      The manuscript extensively quantifies the area and volume of polyQ assemblies (e.g., Figure 2B, C and Figure 3B, C, E, G, H). These measurements are not reliable. First, the structures appear filamentous and likely below the diffraction limit. Second, fluorescence signals are broadened by the point spread function (PSF), artificially inflating measured dimensions. Last, even with 3D SIM (~100 nm resolution), fine structural details remain unresolved. Thus, these quantitative measurements lack physical meaning and might not be used to support conclusions.

      We appreciate the reviewer’s thoughtful critique regarding the quantification of area and volume. Our measurements are derived from immunofluorescent signals captured via structured illumination microscopy (SIM) and confocal imaging. If the reviewer's concern is that antibody-labeled structures do not perfectly match the absolute physical dimensions of native polyQ assemblies due to the linkage error of the primary-secondary antibody complex, we agree conceptually.

      However, our imaging pipeline is optimized to minimize these discrepancies. Our SIM resolution reaches approximately 64 nm. Given that the total observed thickness of the fluorophore-labeled polyQ assemblies exceeds 200 nm, these structures reside well within the detectable range of our super-resolution system, minimizing diffraction-induced overestimation. Regarding the point spread function (PSF) and optical distortion, we emphasize that all comparative quantifications across experimental groups were conducted under identical imaging parameters and thresholds, ensuring a standardized baseline. Furthermore, our acquisition systems (Leica, Nikon, and Zeiss) utilize advanced deconvolution algorithms specifically designed to mitigate PSF-related blur. While we observed that deconvolution yielded negligible baseline improvements when using high-numerical-aperture objectives (63x or 100x, oil immersion), it validates that our raw high-resolution scanning was already highly optimized.

      We acknowledge that an immunolabeled complex is not structurally identical to a naked, pure polyQ tract. Nonetheless, indirect immunofluorescence remains the most robust method to evaluate spatial distribution in situ. Indeed, cryo-EM studies have highlighted that native polyQ tracts are highly flexible and structurally dynamic, making them exceptionally difficult to resolve in their native state (Guo et al., 2018). Intriguingly, we observed that antibody-bound polyQ assemblies remain structurally stable for several weeks with minimal fragmentation, suggesting that antibody binding may structurally stabilize these highly flexible regions. Consequently, indirect immunolabeling provides an indispensable framework for capturing these assemblies within the cellular environment.

      (4) Interpretation of structural features (Figure 2A)

      Descriptions such as "parallel spindles" and "ring-like assemblies" are not clearly supported by the data. The terminology is ambiguous, and the claimed structures are not discernible. The use of the term "interaction" with the nuclear membrane is also inappropriate. At best, the data suggest colocalization, which itself is not convincingly demonstrated.

      Please refer to Fig. 2A (middle upper), Fig. 2F, and Fig. 4C for “parallel spindles”. Please refer to Fig. 5I, J, and Fig.S3C (right panel) for additional clear “ring-like assemblies. Due to the unique spatial distribution of the 'ring-like assemblies,' observing multiple rings within a single spindle is technically challenging. Accordingly, we have tempered our statement in the revised manuscript to reflect this limitation accurately. Furthermore, it is important to note that the visualized structures represent the fluorescent signal from secondary antibodies rather than direct imaging of the proteins themselves. Consequently, we cannot definitively confirm whether this immunostaining pattern precisely replicates the native state of polyQ assemblies within the cellular environment.

      (5) Mitotic fragmentation (Figure 2E)

      The conclusion that polyQ assemblies fragment during mitosis lacks proper controls. It is unclear whether these cells exhibited intact "fabric-like" assemblies during interphase, or the observed structures were already fragmented prior to mitosis.

      We thought that we had displayed enough non-mitotic cells in this study (Fig. 2A, D, Fig. 4A, F). Most of the cells in this study are non-mitotic cells (G1+S+G2). Thus, we consider the control of non-mitotic cells to be redundant here.

      (6) Fixation-induced fragmentation (Figure 2F)

      The claim that fixation-induced fragmentation reflects a unique dynamic property of polyQ assemblies is likely an overinterpretation. This phenomenon may simply represent a fixation artifact. Therefore, it cannot be used as evidence for in-cellulo structural dynamics.

      By definition, a laboratory artifact refers to any unintended structural detail, distortion, or error introduced by experimental equipment or the preparation process. We contend that the observed phenomenon represents a native chemical characteristic of the HTT polyQ domain inside cells following paraformaldehyde (PFA) fixation, rather than a technical artifact. Similar structural features have been documented by other investigators in tissue samples (Ferrante et al., 1997). A classic textbook example of an artifact is the lamina lucida of the basal lamina, which is artificially generated during electron microscopy tissue processing and does not exist in living tissue. In contrast, the fragmentation of polyQ assemblies occurs naturally both in living cells subjected to stress and during post-fixation processing.

      (7) Nuclear localization claims (Figure 5A)

      The assertion that polyQ assemblies "almost completely occupy the nucleus" is not supported. The images are more consistent with perinuclear localization, typical of the Golgi region. There is no clear evidence for nucleoplasmic distribution.

      Please refer to the rendering image in the upper-left inner insert of HD neurons (the blue [transparent] is the nucleus and the pink/white is polyQ). The almost complete occupation of the nucleus is crystal clear in these images (rendered inner inserts, upper left). In iPSC-induced HD neurons, it is not only distributed in the nucleus but also in the cytoplasm. Based on your description, you might be referring to the cytoplasmic polyQ assemblies but not the nucleus in the rendering image in the upper left (left panel). We have added a label in the revised version for clarity (white arrows for nuclear accumulation). In this manuscript, we have enough figures that clearly show the nuclear accumulation. Please also refer to Fig. 7 and Fig. S2 for additional images of nuclear accumulation.

      (8) Drug treatment and data interpretation (Figure 3D-E)

      The x-axis in Figure 3E is non-linear, which is inappropriate unless explicitly justified. Furthermore, the rationale for using Onjisaponin F is unclear. What is its known mechanism? Does it affect the Golgi organization? Without this context, observed effects may reflect Golgi perturbation rather than specific effects on polyQ assemblies.

      We appreciate the reviewer pointing out Figure 3E. In this experiment, Huntington's disease (HD) fibroblasts were cultured in a low-glucose medium for the first 72 hours, which accounts for the linear trend observed across the first four data points. Following these 72 hours, the cells were switched to a high-glucose medium and cultured for an additional 48 hours to evaluate subsequent dynamic changes in the polyQ assemblies. To improve visual clarity, we have color-coded these distinct treatment conditions in the revised manuscript, using red to denote low-glucose treatment and green to denote high-glucose treatment.

      Regarding the choice of Onjisaponin treatment (a concern also raised by another reviewer), Onjisaponin is an active component derived from Radix Polygalae (Yuan Zhi). Previous literature indicates that Onjisaponin B enhances autophagy, accelerates the degradation of mutant α-synuclein and huntingtin in vitro, and activates the AMPK-mTOR signaling pathway (Wu et al., 2013). To optimize our experimental model, we screened multiple variants—specifically Onjisaponin B, D, and F. We determined that Onjisaponin F exhibits remarkably low cytotoxicity while maintaining a robust autophagy-enhancing capacity in both human fibroblasts and iPSC-derived neurons. Consequently, Onjisaponin F was selected for our human cell line experiments (please refer to Author response image 3). While we did not previously assess Golgi apparatus alterations under Onjisaponin F treatment, we recognize the value of this metric. We are currently evaluating changes to both the Golgi apparatus and neuronal firing rates following Onjisaponin F exposure, and this new dataset will be integrated into our revision.

      Reviewer #2 (Public review):

      Summary:

      In this study, the authors report the hitherto unobserved types of HTT assemblies observed in human fibroblasts and iPCS-derived neurons in 2D and 3D culture, applying a state-of-the-art confocal microscopy imaging with near 64 nm resolution to decode their structures. They further demonstrate that these assemblies closely contact with various types of Golgi ribbons, stacks, vesicles, and Golgi-derived clathrin-coated vesicles but not mitochondria. They also used single-cell RNA-seq to show some interesting findings that supported the suggested defects in Golgi-related function, specifically by downregulation of various cellular processes related to Golgi and vesicle transport functions. They also replicate mHTT nuclear accumulations in striatal neurons, which is considered to be a hallmark of HD pathology, by using long-term neuronal culture. Furthermore, the assemblies showed differential responses to glucose starvation and to autophagy enhancer treatment by onjisaponin F for mutant HTT assemblies, but not for the healthy siblings, in fibroblasts and neurons. Onjisaponin F treatment did not reverse nuclear deposition. They also showed that ASO shortens these polyQ assemblies but does not change neuronal firings that are detected by HD-MEA. Notably, they also used human brain samples to show the existence of polyQ assemblies in fetal and child brain samples. This part is impressive.

      Overall, this work reports a novel polyQ assembly, which was previously reported as a pathogenic factor, has not been reported before for HTT, is related to Golgi activities and vesicular transport, and is dismantled in HD patient cells. The intensive immunostaining and super-resolution scanning are impressive and definitely strengthened by the impact of the findings. The scRNAseq data adds another layer to the observed Golgi impairments and their suggested relationship to Golgi function. The drug testing for polyQ assemblies, especially polyQ assemblies in HD cells, is preliminary. However, the data in this study are enough to support the existence of polyQ assemblies in human cells and their specific relationships with the Golgi apparatus.

      We sincerely thank the reviewer for their time, dedication, and insightful evaluation of our manuscript. We agree that the drug screening component represents an initial phase of discovery, and we appreciate the opportunity to clarify this in our text. As the reviewer notes, executing high-throughput or exhaustive drug screenings in human brain organoids is exceptionally resource- and time-intensive due to prolonged culture requirements. We will provide more mechanistic and physiological details of these drugs in the future.

      Strengths:

      In this study, the authors used the cells from a large HD family and fetal/child brain samples to decode the structure of endogenous polyQ assemblies. This part is impressive. The intensive staining and super-resolution scanning are amazing. The spatial relationships of polyQ assemblies with the Golgi apparatus and mitochondria are well illustrated.

      Weaknesses:

      Although they used healthy sibling cells as a control, an isogenic control (genetic correction of the mutant gene) is lacking. Based on the Golgipathy of mHTT, they did a drug screening. The drug testing for polyQ assemblies is preliminary. More rigorous validation, such as scRNA-seq and proteomic analysis, etc., is necessary to reach a systemic conclusion.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      Figure-specific concerns:

      (1) Figure 4A: Claimed phenotypes are not clearly visible.

      We have addressed the comment in the previous section. Please refer to the response to Reviewer#1 comment 7 and the rendering image.

      (2) Figure 4C: The significance of the reduced clathrin signal is unclear.

      We have improved the images in the revised version. We provide a lateral view image in the revised version (please refer to Figure 4D).

      (3) Figure 4E: Discrepancy between N- and C-terminal HTT staining raises concerns about antibody performance.

      We thank the reviewer for highlighting the discrepancy between the N- and C-terminal HTT staining within the polyQ assemblies. In mitotic cells exhibiting a fragmented polyQ-Golgi complex, as well as along the ruffling membrane and larger vesicle-like structures, the N- and C-terminal HTT antibodies colocalize completely (please refer to Fig. 2E [right panel], and Fig. S1A, B), However, the C-terminal antibody displays a noticeably scattered pattern specifically on the denser polyQ assemblies. To understand this discrepancy, we consulted with several structural biologists at Fudan University. Based on these discussions, we have formulated three potential explanations:

      (1) Steric Hindrance due to Assembly Core Localization: The C-terminus of HTT may be sequestered within the internal core of the polyQ assemblies. The restricted spatial localization could physically prevent the C-terminal antibody from accessing its target epitope.

      (2) Conformational Masking: The unique quaternary conformation or dense packing architecture of the HTT polyQ assemblies might mask or distort the specific antigen epitope, hindering antibody-epitope recognition.

      (3) Heterologous Protein Co-aggregation: There are at least eight other polyQ-containing proteins in human cells—including Atrophin-1, Androgen Receptor, Ataxin-1, -2, -3, -7, and the α1A subunit of the voltage-gated calcium channel—whose expansion triggers neurodegenerative diseases (Paulson et al., 2000). If any of these heterologous polyQ-containing proteins co-aggregate and participate in building these macromolecular assemblies, their incorporation could alter the overall structural topography and displace or dilute the C-terminal HTT antibody signal.

      We have incorporated a discussion of these structural possibilities into the revised manuscript to address this intriguing observation.

      (4) Figure S2A: The "nuclear gorge" observation lacks statistical support and does not demonstrate structural rigidity. Alternative approaches should be employed to demonstrate and probe the rigidity.

      We thank the reviewer for highlighting the presence of the nuclear gorge. We agree that this irregular structure is highly intriguing; however, accurately quantifying a variable, irregular cleft on an already irregular nuclear surface presents significant technical challenges. Currently, our laboratory lacks the specialized, high-resolution image analysis software required to precisely measure and map these specific structural parameters. Given these technical limitations, and because a detailed investigation of this nuclear phenotype falls outside the immediate scope of our current study, we have chosen not to expand upon this observation further in the present manuscript. We hope the reviewer understands this practical limitation.

      The polyQ structures might not be the cause of the nuclear gorge; they simply park at the space created by the nuclear gorge.

      The mechanism of nuclear gorge formation suggested by the reviewer is indeed a compelling possibility. Because the nuclear envelope is highly dynamic and mechanically compliant, external physical forces can readily deform and reshape the nucleus. In our observations, pronounced nuclear gorges were strictly associated with, or in close proximity to, polyQ assemblies; they were entirely absent in nuclei lacking nearby aggregates. This spatial correlation leads us to hypothesize that the growth or accumulation of polyQ assemblies exerts mechanical stress on the nuclear surface, thereby inducing the gorge. However, we acknowledge the alternative possibility that a pre-existing nuclear indentation could create a favorable microenvironment or spatial niche that facilitates the localized assembly of polyQ proteins. Given the current limitations of static imaging, it remains challenging to distinguish between these biophysical models definitively.

      Reviewer #2 (Recommendations for the authors):

      (1) In this study, the author used an unreported agent, onjisaponin F, which dramatically increased autophagy in both human fibroblasts and neurons. Does the author test the cellular toxicity of onjisaponin F in human fibroblasts, cell lines, or induced neurons? How does onjisaponin F affect the neuronal firing in induced HD neurons? If the author counted the LC3B-positive dots in fibroblasts or neurons?

      To evaluate the safety profile and autophagy-enhancing capacity of Onjisaponin F, we performed several validation assays. Cell viability was assessed via a CCK-8 assay, which demonstrated minimal cytotoxicity in both patient-derived and healthy sibling control fibroblasts, maintaining approximately 75% viability even after exposure to a high concentration (100 µM) for 24 hours. Furthermore, immunostaining for Cleaved Caspase-3 revealed that the apoptotic cell fraction remained below 2% across all tested doses (10 µM, 20 µM, and 40 µM) at 24 hours. To monitor autophagy induction, we quantified LC3B puncta across five distinct fibroblast lines (three Huntington's disease patients and two healthy siblings), as well as in induced striatal neurons (day 35) following a 48-hour treatment with 20 µM Onjisaponin F. The results confirmed that 20 µM Onjisaponin F significantly upregulates autophagy in these induced striatal neurons.Given the tight scope and length constraints of our manuscript, we opted not to include these characterization datasets in the main text (Author response image 2). However, because eLife publishes the author responses alongside the article, this valuable validation data will remain fully transparent and easily accessible to readers.

      Author response image 2.

      Onjisaponin F is a low-toxic autophagy enhancer in human fibroblasts and neurons. (A). CCK8 data showed that onjisaponin F has low cellular toxicity. (B). Caspase-3 antibody staining of the HD and healthy sibling fibroblasts treated with 20 µM onjisaponin. Scale bar, 50µm. (C). Ratio of caspase-3+ cells under different dosages of Onjisaponin treatment (HD, N=3; Healthy, N=2). Data, means±s.e.m. (D). Counts of LC3B puncta in the fibroblasts of HD patient and healthy sib-ling after different dosages of onjisaponin treatments. Data, means± s.e.m. (E). LC3B western blotting after different dosages of onjisaponin F treatment in N2a cells. (F). Representative images of LC3B and 3B5H10 immunostained HD patients and healthy siblings' neurons treated with 20µm onjisaponin F. (G). LC3B-positive region in HD patient and healthy sibling neurons treated by 20µm onjisaponin F. (H). Comparing the count of TUNEL+ positive cells in neurons of HD patient with healthy sibling differ-entiated for 45 days treated with 20µM onjisaponin F.

      (2) The author showed that polyQ assemblies are degraded after fixation in both cell lines and organoids. This phenomenon was reported by another group (Ferrante et al., 1997). The Reviewer wants to know how long the polyQ was undetectable after fixation. This information is extremely important for other groups who want to stain polyQ in cells and tissues.

      Thanks for pointing out the staining protocol. We have shown the results of staining here (please refer to Author response image 3). The diminishing of signals is consistent with the publication by Ferrante et al.

      Author response image 3.

      Comparing 3B5H10 antibody immunostaining in different protocols. (A) Co-immunostaining of 3B5H10 with IBA-1 or Ki67 antibody in the VZ and SVZ regions of human brain samples. The fresh brain tissue samples were fixed in PFA for 72 hours and sectioned into 50 µm slices. After sectioning, the slides were dried at room temperature for 48 hours and stored in -80°C for long-term preservation or stained within 72 hours after sectioning. (B) Immunostaining of 3B5H10 antibody in the VZ and SVZ regions of human brain organoids. The fresh brain organoid samples were fixed in PFA for 24 hours and sectioned into 25 µm slices. After sectioning, the slides were dried at room temperature for 24 hours and stained within 24 hours (upper panel) or stained after 7 days (lower panel; the samples were stored at 4°C).

      (3) The author displayed the relationship of polyQ assembly with the nucleus, mitochondria, and Golgi. Multiple studies revealed that mHTT affects rER function (for example: https://doi.org/10.1038/s41467-021-21637-y; DOI: 10.1016/j.brainres.2016.03.034). Does the author detect the relationship between rER?

      We have previously stained rER tracer with 3B5H10 antibody. The rER rarely colocalized with 3B5H10-stained polyQ assembly in fibroblasts. Rer tracer is easy to photo-bleach. Thus, we have no idea if the rER signals fully cover the rER region in fibroblasts.

      Author response image 4.

      (A) rER-tracker and 3B5H10 antibody co-staining in the fibroblasts of HD patients (CAGS, 49) and healthy siblings. 3D rendering revealed the spatial relationships of polyQ assemblies with rER. Rendering was done by IMARIS.

      (4) The Reviewer is curious about whether the transfected first exon fragments incorporate into the endogenous polyQ assemblies. This is critical to revisit the result of exogenous polyQ in cells (https://doi.org/10.7554/eLife.17056).

      We have transfected the first exon fragments tagged with EGFP in healthy sibling fibroblast. We noticed that the first exon fragments tagged with EGFP did not sufficiently incorporate into Golgi apparatus stained by GM130 (Figure 1-Figure Supplement 1F- G)

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    1. Author response:

      The following is the authors’ response to the original reviews.

      Reviewer #1 (Public review):

      Summary:

      This manuscript uses a valuable dataset of simultaneous LC single-unit recordings and pupillometry in awake monkeys to examine one aspect of the relationship between LC activity and pupil diameter: whether baseline LC activity predicts evoked pupil and whether baseline pupil predicts evoked LC. These relationships are largely absent in the present dataset, and the authors conclude that this type of prediction is not reliable.

      Strengths:

      This is a valuable dataset of simultaneous LC single-unit recordings and pupillometry in awake monkeys, the within-modal and within-epoch analyses are sound. The new results further caution the use of pupil diameter to infer LC activity.

      Weaknesses:

      There is an obvious rationale for asking whether baseline LC relates to baseline pupil or evoked LC relates to evoked pupil. It is also obvious to ask about the relationship between baseline and evoked LC activity, and between baseline and pupil responses. However, the rationale for the cross-modal and cross-epoch analysis is not clear. Why should one expect baseline LC to predict evoked pupil, or baseline pupil to predict evoked LC? What is the biological importance of such predictions? These analyses simultaneously change the modality and the temporal domain.

      We have substantially revised the Introduction to clarify the rationale for this cross-model and cross-epoch comparison, especially the new third paragraph:

      “Despite these findings, many questions remain about the reliability with which pupil measures can be used to infer LC activity. Baseline pupil size is particularly difficult to interpret because it depends on camera position, ambient lighting, and other factors that can vary considerably over hours of recording and across sessions (Mathôt et al. 2018). In contrast, transient responses, which are measured relative to a local baseline, are less vulnerable to these confounds and thus used more often. Some studies have gone further, using evoked pupil responses to infer baseline LC activity, which is central to theories of LC function but difficult to measure (Koss 1986; Gilzenrat et al. 2010; Eldar et al. 2013; Unsworth and Robison 2018). This cross-modal, cross-epoch inference relies on an assumed parallelism between the two measures: in both cases, evoked responses tend to diminish as baseline increases (Aston-Jones and Cohen 2005; Gilzenrat et al. 2010). Thus, a small evoked pupil response is taken to indicate high baseline LC activity (tonic mode), and a large evoked pupil response is taken to indicate moderate baseline activity (phasic mode).”

      Furthermore, some recent studies, which are not referenced in this manuscript, showed variability in the relationship between pupil and LC within the same epoch, and that tonic and phasic pupil responses could be regulated by different inputs to LC. Given that the pupil-LC coupling is readily imperfect and potentially controlled by different cellular and circuit mechanisms, it is not surprising that their cross-epoch relationship is even more variable.

      We agree that it is important to point out variability in the within-epoch coupling in our dataset. This point is now addressed through the predictive analysis (based on the reviewer’s recommendation, detailed below). We include an additional citation documenting such variability in other species (line 294) and text in the discussion suggesting that this variability results, in part, from multiple neuromodulatory systems, inputs, and/or functional subdivisions that may contribute to the control of pupil diameter (lines 308-314).

      One main analysis that correlated baseline pupil with evoked LC showed statistically different results between the two monkeys, raising the question of to what extent a general claim for the cross-modal cross-epoch analysis can be made.

      We agree and now use greater nuance when interpreting this result (lines 144-155). We emphasize that, despite differences in the statistical significance between monkeys, this effect is small in magnitude and limited to a small number of units. This small effect is consistent with our cross-validation test for the cross-modal and cross-epoch linear models, which performed quite poorly (new Table 1).

      Reviewer #1 (Recommendations for the authors):

      If the authors want to establish that pupil cannot be used to infer LC mode, a prediction/generalization-type analysis would be more informative than correlation analysis.

      We agree and now report results based on linear regression models using leave-one-out cross-validation. The findings recapitulate the correlation-based analyses and suggest that the cross-modal and cross-epoch models do a poor job of generalizing across trials. We have added a table (Table 1) that summarizes the results of this analysis and corresponding text at lines 166-175.

      The heterogeneity in the cross-modal, cross-epoch analysis in Figure 2 might be more informative than the population-level null result. Would this heterogeneity be explained by any measurable quantities?

      We agree that this heterogeneity evident in the cross-modal, cross-epoch analyses is potentially interesting. However, as we now document more thoroughly, the effect sizes that comprise this heterogeneity are quite weak. We therefore do not believe that additional measurable quantities from this dataset will be more enlightening about these effects. We include in the Discussion an expanded treatment of the factors that are influencing the measured relationships and therefore limit the ability to use pupil size as a non-invasive proxy for LC’s activation mode.

      Reviewer #2 (Public review):

      Summary:

      The manuscript by Thompson and Gold reported that, although baseline and evoked LC activity were positively correlated with baseline pupil size and evoked pupil dilation, respectively, there were no reliable cross-epoch relationships between LC activity and pupil size - that is, between baseline LC activity and evoked pupil dilation or between baseline pupil size and evoked LC activity. A major strength of the study is its large dataset, comprising recordings from more than 100 LC single units collected across 83 recording sessions in two monkeys. The authors further strengthened their conclusions by performing several control analyses to rule out potential confounds, including whether the findings were influenced by (1) the use of residuals in the main analyses, (2) the possibility that the auditory stimulus failed to evoke the full dynamic range of LC activity and pupil responses, and (3) nonlinear cross-epoch relationships between LC activity and pupil size.

      These findings are important because they remind researchers to exercise caution when assuming that non-illuminance-mediated fluctuations in pupil size can reliably serve as a proxy for LC activity under all experimental conditions

      With that being said, I have two suggestions that I believe would further strengthen the manuscript.

      (1) Previous studies have suggested that the LC is organized into functionally distinct subpopulations (e.g., PMID 28920933 and PMID 40770025). It is therefore possible that a subset of the LC neurons recorded in this study does not participate in controlling pupil size. I encourage the authors to discuss this possibility in the Discussion. In addition, this possibility could be tested by repeating the cross-epoch relationship analyses using only LC units that exhibit a strong correlation with pupil size (the darker points in the last column of the top two rows of Figure 1?).

      We agree and now include this important point in the Discussion. We also now include new analyses restricted to the subsets of neurons with significant baseline LC-pupil relationships and observe similar null results (lines 141-150), suggesting that our results were not driven by neurons that do not participate in controlling pupil size. We have incorporated the referenced work into our broader discussion on the dynamic coupling between the LC and pupil size (lines 296-298 and 308-314).

      (2) The manuscript would benefit from a clearer visualization of the analyses addressing the possibility that the auditory stimulus failed to evoke the full dynamic range of LC activity and pupil responses. A supplemental figure illustrating the distributions or ranges of LC activity and pupil responses, together with the corresponding control analyses, would help readers better understand this important point.

      We have added an additional supplemental figure (now Supplemental Figure 1) that illustrates the relationship between evoked LC/pupil ranges and the corresponding correlation. Notably, the effect was significant for only one animal, which showed a relatively weak negative trend between evoked pupil range and the Spearman Correlation capturing the relationship between evoked pupil and baseline LC activity.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      The manuscript by Hernandez-Nunez et al. provides a comprehensive characterization of how heart-brain circuits develop in a vertebrate brain, namely the zebrafish. The characterization is performed using a combination of modern and sophisticated imaging and neural manipulation techniques and achieves unprecedented clarity and detail in how the heart-brain communication develops early in life. The paper describes a three-stage program, where first an efferent-circuit from the motor vagus to the heart develops, followed by sympathetic innervation, and lastly sensory neurons innervate the heart.

      Strengths:

      The paper is very clearly and nicely written. The findings are novel and of high quality and relevance. The presentations are very clear and nicely interpreted. The analyses are well presented and applied.

      Weaknesses:

      From the heart rate traces, heart rate variability seems to be prominent and changes across days post-fertilisation (dpf). That would be a useful dependent variable, considering that the variation captured by the models does not fully explain heart rate, both for sympathetic and parasympathetic efferents. Given the strong auto-rhythmicity of nodal tissue in neurogenic hearts, modulatory inputs could potentially predict heart rate variability with higher precision.

      We thank Reviewer #1 for their generous assessment of the manuscript. We are grateful that the reviewer found the work clearly written, novel, technically strong, and relevant, and that they viewed the analyses and interpretation as clear and appropriate.

      The reviewer’s main suggestion concerned heart-rate variability and the possibility that developmental changes in variability may provide an additional readout of autonomic circuit maturation. We thank the reviewer for this insightful comment. The developmental change in baseline cardiac variability was indeed apparent in the heartrate traces, and the reviewer’s observation prompted us to examine it directly. This analysis added a useful component to the revised manuscript by showing that the maturation of heart–brain circuits is accompanied not only by changes in stimulus-evoked cardiac control, but also by a marked developmental change in the temporal variability of the cardiac rhythm.

      We therefore quantified variability in the sequence of interbeat intervals during prestimulus baseline periods. We measured short-timescale variability using the root mean square of successive differences between interbeat intervals, or RMSSD, and normalized this value to the mean interbeat interval to allow comparison across developmental stages with different baseline heart rates. Normalized RMSSD increased 2.66-fold between 4 and 5 dpf and remained elevated at 7 and 12 dpf (bootstrap 95% CI, 2.04–3.27; new Supp. Fig. 2 A, B). The coefficient of variation of interbeat intervals showed the same developmental pattern (new Supp. Fig. 2D).

      We also tested whether this increase could be explained solely by developmental differences in mean heart rate. It could not. The best-supported mixed-effects model included an interaction between developmental stage and mean interbeat interval, indicating that the relationship between average cardiac timing and interval-to-interval variability itself changes across development (new Supp. Fig. 2C). We now describe these results in the last paragraph of the first result section and provide the full analysis and statistical procedures in the new Methods subsection “Analysis of developmental cardiac variability.”

      We also clarified the relationship between this new analysis and the neural prediction models. Each value in the cardiac signal used in those models was derived from one interbeat interval and therefore already contained the beat-resolved variability present in the cardiac recordings. The models consequently test whether neural activity predicts fluctuations in that beat-resolved cardiac signal. However, the cardiac and neural measurements have different temporal bandwidths: the cardiac recordings resolve millisecond-scale differences between successive intervals, whereas calcium indicators integrate neural activity over substantially longer timescales. The models therefore recover the component of cardiac variation that evolves over timescales accessible to both measurements.

      We are grateful to the reviewer for drawing our attention to this feature of the data. This new analysis helped clarify that cardiac innervation coincides with a substantial increase in heart rate variability. Thus, the resulting analysis strengthens the developmental physiology presented in the manuscript while also clarifying the temporal relationship between the cardiac recordings and the calcium-based neural models.

      Reviewer #2 (Public review):

      Hernandez-Nunez et al. investigate the development and function of neural circuits involved in the regulation of heart rate in larval zebrafish. Using conserved genetic markers, they identify neural pathways involved in the bidirectional control of heart rate and in providing sensory feedback, potentially enabling more precise tuning. The main observation is that the different elements of this circuit are laid down in a developmentally staggered manner.

      At 4 days old, the heart rate is invariant to a range of sensory stimuli, and the vagal motor or sympathetic pathways could not be seen to innervate the heart. Progressively through development, the heart is first innervated by the vagal motor pathway, whose axons are cholinergic, before the formation of phox2bb+ intracardiac neurons (ICNs). At this stage, before the first ICNs are observed, activation of the vagal motor pathway by optogenetic activation of a localized population of cholinergic hindbrain neurons leads to bradycardia. After the vagal motor innervation begins, the sympathetic pathway innervates the heart, which could be visualized in the form of TH+ fibers from the anterior paravertebral ganglia (APG). The activity of the TH+ APG neurons was diverse and showed proportional, integral, and derivative-like relationships to the heart rate, suggesting a role in more precise tuning of the rate than what could be achieved through the vagal pathway alone. The sensory vagus innervation of the heart was identified to be the last stage to develop; however, neurons in the nodose ganglion exhibited diverse responses tuned to the heart rate well before the innervation reached the heart. The authors attribute this to the fact that other indirect sensory cues from the gills or vasculature could be used to sense heart rate prior to innervation.

      This study identifies key components of the control loop required for the regulation of heart rate in zebrafish. The control mechanism appears to be independent of the cues that trigger heart rate changes, indicating that the circuit is indeed part of an interoceptive pathway for heart rate control. Evidence for the staggered development of the vagal-motor, sympathetic, and sensory pathways is conclusive, and as the authors discuss, this phenomenon progressively allows for finer-grained control of the heart rate. This could be achieved through proportional-integral-derivative-like control properties emerging in a diverse set of neurons in the APG and sensory feedback of the state of the heart. In line with these findings, the baseline variability of heart rate prior to innervation at 4 days old appears to be comparatively lower than the later stages (Figure 1C, D, Supplementary Figure 1C-F) and increases over development. Based on this observation and the time courses of the kernels identified by the GLMs, I would expect heart rate fluctuations of a finer time scale, ultimately limited by the time course of GCaMP6s, to be captured by the models in Figures 3, 5, and 7, in addition to the stimulus-locked changes that are highlighted. While the models yield valuable insight in the form of the activation kernels and their potential roles, in one instance, this captures the potential contribution of either the motor vagus or the APG to the change in heart rate. This makes it challenging to identify where it falls short and the potential functions of pathways that are yet to be discovered.

      Lastly, the proposed anatomical connectivity of the heart-brain circuit is based on tracts observed in this study as well as those inferred from function and from previous studies.

      (1) It is not clear from the images presented here whether the VSNs send feedback projections to the brainstem VPN.

      (2) Do the brainstem neurons identified by their functional roles send efferent projections via the motor vagus nerve? This is unclear from the results presented and needs to be clarified in the text.

      (3) Add appropriate clarifying annotations to Figure 9 and a section of text discussing the potential unknowns in the proposed circuit diagram.

      We thank the reviewer for the thoughtful and constructive review. We greatly appreciate the careful synthesis of the developmental sequence described in the manuscript. The comments were particularly helpful in prompting us to clarify the temporal scope of the neural models, to quantify developmental changes in baseline cardiac variability, and to distinguish more explicitly between anatomical connections directly observed in this study, functional relationships supported by our experiments, and connections inferred from prior work. We have revised the manuscript and figures accordingly.

      Developmental changes in cardiac variability and the temporal scope of the neural encoding or decoding models

      We agree with the reviewer that baseline cardiac variability is lower at 4 dpf and increases at later developmental stages. To quantify this observation, we analyzed the sequence of all interbeat intervals during pre-stimulus baseline periods. We measured the root mean square of successive differences between cardiac intervals, or RMSSD, and normalized this value to the mean interbeat interval to permit comparison across stages with different baseline heart rates. Normalized RMSSD increased 2.66-fold between 4 and 5 dpf and remained elevated at 7 and 12 dpf (bootstrap 95% CI, 2.04– 3.27; new Supp. Fig. 2 A, B). The coefficient of variation of interbeat intervals showed the same developmental pattern (new Supp. Fig. 2 D). We also tested whether this increase could be explained solely by developmental differences in average heart rate. The best-supported model included an interaction between age and mean interbeat interval, indicating that the relationship between average cardiac timing and interval-to-interval variability itself changes across development (new Supp. Fig. 2 C).

      We now describe this result in the revised Results section and provide the full analysis in the new Methods subsection, “Analysis of developmental cardiac variability.” We are grateful to the reviewer for drawing our attention to this feature of the data, as the resulting analysis provides an additional quantitative description of the developmental change in baseline cardiac dynamics.

      We also agree that it is important to clarify what temporal features can be captured by the generalized linear models. Each value in the cardiac time series used in the models was calculated from the duration of an individual cardiac interval. The modeled cardiac signal therefore already contains the beat-resolved variation present in the recordings, including stimulus-locked and spontaneous fluctuations. The models are not limited to fitting only the mean stimulus response.

      However, the cardiac and neural measurements have different temporal bandwidths. The cardiac recordings resolve millisecond-scale differences between successive intervals, whereas GCaMP6s integrates neural activity over substantially longer timescales. The models therefore recover the component of cardiac variation that occurs over timescales shared by the cardiac and calcium measurements. We have clarified this point in the revised Results and Methods.

      We further revised the text to clarify the purpose and limits of the models. The models identify predictive relationships between the recorded neural populations and cardiac dynamics; they are not intended to provide an exhaustive causal decomposition of all sources of heart-rate variation. Unexplained variation may reflect the intrinsic autorhythmicity of pacemakers, endocrine or paracrine influences, metabolic state, or temporal information not recoverable from calcium imaging. We now discuss these possibilities explicitly.

      (1) Do viscerosensory neurons project to the VPN?

      We thank the reviewer for identifying this gap in the anatomical presentation. In the original manuscript, we showed the developing viscerosensory ganglia and their later peripheral innervation of the organs, but we did not show clearly that these neurons also extend central projections into the hindbrain.

      We have now added a new supplementary figure showing the right and left viscerosensory ganglia at 2, 3, and 4 dpf. At each of these stages, labeled axons can be seen extending dorsally from the developing ganglia and entering the hindbrain, including at stages that precede detectable peripheral innervation of the organs (new Supp. Fig. 8). These observations demonstrate that the central projection of the sensory vagus is established early, while the ganglia are still forming and before completion of their peripheral organ innervation. We have clarified in the discussion that our data do not resolve whether these afferents form direct synaptic contacts with the specific functionally identified VPN described in this study.

      (2) Do the functionally identified brainstem neurons project through the motor vagus nerve?

      We agree that this distinction needed clarification. We have revised the text to distinguish the descending motor vagus pathway from the functionally defined cholinergic hindbrain locus identified in Fig. 3. Our data show that activity in a medial cholinergic hindbrain locus predicts cardiac inhibition and that targeted activation of this region elicits bradycardia, indicating that it engages descending vagal cardiac control. However, because the functionally identified neurons were not individually traced, this locus may include motor vagus neurons, premotor neurons upstream of the motor vagus, or both. We have clarified this point in the Results and Discussion.

      (3) Clarification of Figure 9 and unresolved elements of the proposed circuit

      We thank the reviewer for this suggestion. We have revised Figure 9 to make the evidence of each proposed interaction explicit. The updated legend now distinguishes functional relationships supported by an observed anatomical connection, functional relationships for which the anatomical connection was observed in fewer than 50% of animals, and functional relationships for which no anatomical connection was observed at the developmental stage examined. The revised figure therefore no longer presents all arrows as equivalent or as evidence of direct synaptic connectivity.

      We have also added a paragraph to the Discussion clarifying the principal unresolved aspects of the model. Specifically, we now state that the functional relationships identified through encoding, decoding, and perturbation experiments do not by themselves establish direct synaptic connections; that the peripheral structures through which viscerosensory neurons detect heart-rate-related dynamics remain unknown; and that, although viscerosensory neurons project centrally into the hindbrain, their postsynaptic targets have not yet been identified.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      (1) Figure 3: Given that the paper is arguing for cells with an inhibitory coupling to heart rate to be major contributors to cardiac rate among cholinergic neurons in the early phase, it would be useful to report the outcomes of a GLM model with just the C1 cluster as input.

      We thank the reviewer for this helpful suggestion. We performed the recommended analysis by retraining the heart-rate decoding model using only the calcium traces from neurons assigned to the C1 kernel class, while preserving the same model architecture and cross-validation procedure used for the original C1+C2 model. Because C1 and C2 represent opposing kernel polarities in our current notation, we also trained a complementary C2-only model. These analyses are now included in the new Supplementary Fig. 4.

      At 5, 7, and 12 dpf, both cluster-restricted models retained substantial cross-validated predictive performance. We detected no significant differences in cross-validated R</sup>2</sup> between the C1-only, C2-only, and combined C1+C2 models at any age examined. These results indicate that heart-rate-related predictive information is present in both kernel classes and that either class alone captures much of the signal recovered by the combined model.

      (2) Figure 3J: A magnified version of the figure with larger time scales would help visualize the relationships more clearly.

      We thank the reviewer for this helpful suggestion. We have revised Fig. 3J by magnifying the time axis and increasing the temporal scale of the displayed traces as much as possible.

      (3) Figure 3: It would be useful to show the performance of the model at 4 dpf as a negative control for the argument that vagal drive is the key regulator of heart rate in the early window.

      We agree with the reviewer that 4 dpf provides an important negative-control stage. However, we did not train the heart-rate decoding GLM at 4 dpf because the slower heart-rate dynamics that define the neural relationships at later ages are not yet detectable at this stage. The cardiac recordings nevertheless contain beat-to-beat interval variability, but much of this variation occurs on millisecond timescales that cannot be meaningfully related to GCaMP6s signals. Thus, low decoding performance at 4 dpf would conflate the absence of the slower cardiac dynamics accessible to the model with the temporal bandwidth of calcium imaging, rather than provide an interpretable negative control for vagal coupling.

      (4) Figure 3: C1 and C2 neurons seem to be organised rostrocaudally at 5 dpf. Since C2 neurons have also been shown to encode signatures of cardiac events, along with C1 neurons, optogenetic activation of the rostral and caudal areas of hindbrain cholinergic neurons at 5 dpf would provide additional insights into downstream regulation.

      We agree with the reviewer that spatially restricted activation of different rostrocaudal cholinergic hindbrain regions would be an informative experiment. We attempted this approach at 5 dpf; however, the C2 neurons are sparse and are not defined by an independent molecular marker, making it difficult to selectively activate this functionally defined class without also stimulating neighboring cholinergic neurons. In practice, broader activation of these regions frequently evoked variable motor contractions or struggling, which introduced motion artifacts that confounded simultaneous heart-rate and calcium measurements. We therefore do not think these experiments provide an interpretable test of the specific role of C2 neurons and have not included them as evidence.

      (5) For both the vagal efferent decoding model and the sympathetic efferent decoding model, could noise terms be introduced based on the intrinsic variability of firing at 4 dpf, where no coupling is presumed and presumably governed by nodal tissue? From the model, firing of anterior sympathetic ganglia and heart rate is seen to be coupled at 5 dpf, despite the lack of direct anatomical innervation. The response to the stress test provides corroborative evidence.

      We thank the reviewer for this astute suggestion. The proposed control would be informative only if we could measure the same vagal and sympathetic neuronal populations at 4 dpf, before they become functionally coupled to the heart, and use their activity to define the expected performance of an uncoupled model. We cannot do this reliably. In the later recordings, the neurons included in the decoding models are identified by their location and by reproducible relationships between their calcium activity and heart-rate dynamics. At 4 dpf, the corresponding neurons cannot yet be assigned to these functional classes because the slower heart-rate fluctuations used to define the kernels are not detectable. The remaining differences between individual cardiac intervals occur on millisecond timescales and therefore cannot be related meaningfully to GCaMP6s signals. A noise term derived from 4 dpf would consequently come from an arbitrary set of neurons, not from an identifiable uncoupled version of the populations modeled at later stages.

      We agree that the relationship between anterior paravertebral ganglion activity and heart rate at 5 dpf is especially informative because sympathetic fibers have not yet reached the heart. We interpret this as coordinated recruitment of the APG and the cardiac response by a broader stress-related program. Our stress-test and optogenetic experiments support this interpretation by showing that APG neurons are already responsive at 5 dpf, whereas direct sympathetic control emerges later, together with TH-positive cardiac innervation and optogenetically evoked tachycardia. We have clarified this distinction in the revised manuscript.

      (6) In the discussion and in the summary diagram, the autorhythmicity of the SA node should be highlighted. The possibility of other contributory variables, like endocrine and paracrine signals and metabolic cues, should be discussed. From the model, firing of anterior sympathetic ganglia and heart rate is seen to be coupled at 5 dpf, despite the lack of anatomical innervation. However, the model performance is comparably lower. This could be potentially due to the effects of stress hormones, given that the hypothalamic-pituitary-interrenal axis is functional at 5 dpf. The response to the stress test provides corroborative evidence.

      We thank the reviewer for this important suggestion. We have revised the manuscript and the Fig. 9 legend to state explicitly that the larval heart is intrinsically autorhythmic and that the neural pathways described in this study modulate an ongoing rhythm rather than generate each heartbeat. We also now acknowledge that cardiac dynamics may be influenced by endocrine, paracrine, metabolic, and other non-neuronal physiological signals that are not represented in our neural recordings.

      As the reviewer notes, this distinction is particularly relevant to the 5 dpf sympathetic results. At this stage, APG neurons respond to visual stress and their activity covaries with heart-rate dynamics, yet TH-positive cardiac innervation is not detectable and optogenetic activation of the APG does not evoke tachycardia. We therefore interpret that APG activity and the cardiac response may be recruited in parallel as components of a broader stress-related physiological state. As the reviewer notes, endocrine stress pathways, including the hypothalamic–pituitary–interrenal axis, are plausible contributors at this stage, although our experiments do not directly test their involvement. We have clarified the broader stress-related interpretation in the revised manuscript.

      (7) In the discussion section, a brief mention of cardiac interoception and its relevance to arrhythmias, heart failure, and myocardial infarction would strengthen the clinical perspective.

      We thank the reviewer for this helpful suggestion. We have added a brief clinical perspective to the Discussion linking the developmental assembly of cardiac interoceptive pathways to arrhythmias, heart failure, and myocardial infarction. This perspective is particularly important because current neurocardiac therapies predominantly target cardiac tissue or the efferent mechanisms that regulate heart rate, contractility, and vascular tone, whereas the sensory pathways that communicate cardiac state to the brain are rarely targeted directly. Defining how these afferent circuits are organized may therefore reveal an underexplored point of intervention for maladaptive autonomic responses following cardiac injury or dysfunction.

      (8) Line 31: Though the findings and the mode of encoding are novel, the idea that vagal sensory neurons might encode heart rate information has been suggested. The following papers (or others) would be useful to cite.

      - Nosaka, S., Murase, S., Murata, K. and Inui, K., 1995. 'Aortic baroreceptor' neurons in the nucleus tractus solitarius in rats: convergence of cardiovascular inputs as revealed by heartbeat-locked activity. Journal of the autonomic nervous system, 55(1-2), pp.69-80.

      - Hayward, L.F. and Felder, R.B., 1995. Cardiac rhythmicity among NTS neurons and its relationship to sympathetic outflow in rabbits. American Journal of Physiology-Heart and Circulatory Physiology, 269(3), pp.H923-H933.

      We thank the reviewer for pointing us to these relevant studies. We agree that prior work has shown heartbeat-locked activity and cardiovascular convergence in central brainstem neurons, including neurons in the nucleus tractus solitarius. We have added these citations to the Discussion. We have also revised the text to more clearly distinguish those observations from the encoding described here. Heartbeat-locked activity reflects neural modulation at the timescale of individual cardiac cycles, whereas our analysis identifies vagal sensory neurons whose calcium dynamics track slower changes in heart rate over seconds. Thus, the novelty of our finding is not that cardiac signals can influence vagal or brainstem circuits, but that heart-rate dynamics are represented in vagal sensory neurons by a stimulus-invariant, phase-shifted temporal kernel across spontaneous, sensory-evoked, and optogenetically induced cardiac fluctuations.

      Reviewer #2 (Recommendations for the authors):

      (1) The introduction will benefit from a section on the current understanding of the development of the motor and sensory innervations of the heart and their functions.

      We thank the reviewer for this helpful suggestion. We have revised the Introduction to include a brief overview of the current understanding of cardiac autonomic innervation during development. In this new section, we summarize that the heart is intrinsically autorhythmic before neural control is established, that parasympathetic/vagal, sympathetic, and sensory innervation mature over development, and that most prior functional work has focused on adult or late-stage preparations rather than the initial emergence of these circuits in intact animals. This addition provides context for why larval zebrafish offer a useful system for resolving when motor and sensory heart–brain circuits first become functional.

      (2) Figure 1 B: Why is the dilated ventricle brighter and the contracted ventricle darker in the reflected IR image?

      We thank the reviewer for asking us to clarify this point. The contrast in Fig. 1B arises from near-infrared transmission through the cardiac chamber. When the ventricle is dilated, the density along the optical path is lower and/or spread over a larger volume, allowing more NIR light to reach the detector; the chamber therefore appears brighter. During contraction, the ventricular contents are compressed into a smaller volume, increasing optical density along the imaging path and reducing transmitted light, so the chamber appears darker. We have clarified this point in the figure legend.

      (3) Include a scale for time in Supplementary Figures C-F.

      We have added a scale for time.

      (4) Figure 1 I: Add a panel showing the number of ICNs at each developmental stage. Insufficient information to infer the distributions from panel I.

      We have added a new panel to Supplementary Fig. 1 showing the distribution of reliably countable intracardiac neurons at 12 dpf. Because individual somata within the intracardiac ganglion are often densely clustered and overlapping, we did not assign exact ICG neuron counts across all animals. Instead, the new panel reports the number of countable ICNs outside the ICG, including neurons associated with the SAP and AVP, for each individual fish. This provides the distribution requested by the reviewer while avoiding false precision in cases where individual neurons within the ganglion could not be reliably resolved.

      (5) Figure 2F: a) Not referenced in text. b) Same comment as above. Include a panel showing the labeled ICN numbers.

      We thank the reviewer for pointing this out. We have now referenced Fig. 2F explicitly in the Results. We have also revised the figure legend to specify the number of distinguishable labeled ICNs observed in each fish. Because adjacent labeled somata can be difficult to separate unambiguously in this dataset, we report these values descriptively in the legend rather than as a separate quantitative panel.

      (6) Figure 3 K, O: The labeling of C1 and C2 is inverted with respect to panel G and text.

      We thank the reviewer for catching this labeling error. We have corrected the C1/C2 labels in Fig. 3K and Fig. 3O so that they are now consistent with Fig. 3G and the corresponding text.

      (7) P14, line 36: Figure 4R should be Figure 5R.

      We have corrected this.

      (8) Include quantification of the effect observed in Figure 5 P-R and Supplementary Figure 5.

      We thank the reviewer for this suggestion. We have added quantification of the APG optogenetic activation experiments shown in Fig. 5O–Q and Supplementary Fig. 7. Because cardiac imaging was interrupted during optogenetic stimulation, we quantified the post-stimulation response rather than the stimulation period itself. For each fish, heart rate was averaged during a 12 s pre-stimulation baseline window and a 12 s post-stimulation response window after excluding the stimulation artifact. Responses were normalized to baseline and averaged across trials within fish. The new quantification shows the developmental emergence of APG-evoked tachycardia and confirms that propranolol reduces the response.

      (9) Figure 5 P-R, Supplementary Figure 5: Annotation showing the stimulus window occludes the traces.

      We thank the reviewer for pointing out this potential source of confusion. The stimulus window annotation does not occlude recorded data. During optogenetic activation in these experiments, cardiac imaging could not be acquired concurrently because the stimulation light interfered with data acquisition. The gap in the trace therefore reflects the absence of recorded data during the optogenetic stimulation period, rather than graphical occlusion by the stimulus annotation. We have revised the figure legend and annotation to clarify that no concurrent heart-rate measurements were acquired during the stimulation window.

      (10) Figure 5 P-R, Supplementary Figure 5: Annotation showing the stimulus window occludes the traces.

      We thank the reviewer for pointing out this potential source of confusion. The stimulus window annotation does not occlude recorded data. During optogenetic activation in these experiments, cardiac imaging could not be acquired concurrently because the stimulation light interfered with data acquisition. The gap in the trace therefore reflects the absence of recorded data during the optogenetic stimulation period, rather than graphical occlusion by the stimulus annotation. We have revised the figure legend and annotation to clarify that no concurrent heart-rate measurements were acquired during the stimulation window.

      (11) Could the authors comment on the large negative dF/F signals in Figs 5 and 7? Are these neurons expected to be tonically active?

      We thank the reviewer for raising this point. The negative ΔF/F values in Figs. 5 and 7 reflect decreases in fluorescence relative to the baseline period used for normalization. We do not interpret these signals as direct evidence that the neurons are tonically active, because calcium fluorescence reports activity relative to the chosen baseline and does not by itself establish absolute firing rate or tonic spiking. Rather, these negative responses indicate that, during the relevant behavioral or cardiac epoch, fluorescence in some neurons fell below their pre-stimulus baseline.

    1. Author response:

      The following is the authors’ response to the original reviews.

      We thank the Reviewing Editor and both reviewers for their careful evaluation of our manuscript. We appreciate the reviewers’ recognition of the strength of the in vivo studies and of the evidence identifying E-selectin as a driver of vincristine-induced peripheral neuropathy (VIPN).

      In revising the manuscript, we have focused on clarifying the experimental rationale, strengthening the connection between the different experimental systems, providing additional methodological detail, and ensuring that our conclusions accurately reflect the scope of the data. In particular, we have clarified the distinction between (i) the established requirement for NLRP3–IL-1β signalling in VIPN, demonstrated previously using genetic and pharmacological approaches, and (ii) the new mechanistic question addressed here: whether E-selectin functions upstream of this pathway by regulating macrophage recruitment and amplifying inflammatory signalling.

      Public Reviews:

      Reviewer #1 (Public review):

      (1) The initial experimental paradigm looks at the DRG neurons, which are located by the spine, and from there the foot pad is examined in subsequent experiments. It would be relevant to show whether the foot pad is altered in the vincristine-treated mice and whether the infiltration of myeloid cells that was demonstrated at DRGs is also observed in the foot in the vincristine model. Otherwise, the mechanism being investigated in the vincristine model, which might have similar functional results (paw withdrawal), but the mechanism behind both could be completely different.

      We thank the reviewer for raising this point. We have revised the manuscript to clarify the anatomical relationship between the tissues examined and the distinct purpose of the intraplantar E-selectin experiment.

      The cell bodies of primary sensory neurons innervating the hind paw are located in the dorsal root ganglia (DRG). Their axons travel within peripheral nerves, including the sciatic nerve, and terminate as sensory endings in the plantar skin. Thus, the DRG, sciatic nerve and footpad represent different compartments along the same peripheral sensory pathway. Examining the DRG and sciatic nerve therefore assesses inflammation surrounding the somatic and axonal compartments of the sensory neurons whose peripheral terminals mediate withdrawal responses from the hind paw.

      Following systemic vincristine administration, we observed increased F4/80-positive immune-cell accumulation in both the DRG and sciatic nerve. This response was attenuated by pharmacological blockade or genetic deletion of E-selectin, demonstrating E-selectin-dependent inflammation at multiple sites along the peripheral sensory pathway. We also assessed the footpad for structural neuropathy following repeated systemic vincristine treatment and found no significant loss of intraepidermal nerve fibres. However, we did not quantify F4/80-positive cells in the footpad following systemic vincristine and therefore cannot determine from the present study whether immune-cell accumulation also occurs around the peripheral sensory terminals.

      Importantly, the mechanistic relationship between systemic and local vincristine administration has previously been examined directly in our laboratory. Both systemic intraperitoneal and local intraplantar vincristine produced mechanical allodynia (Starobova et al., 2021; PMID: 33656514, Starobova et al., 2019; PMID: 31316337). Hypersensitivity induced by either route was attenuated by disruption of the TLR4-NLRP3–IL1β pathway, including genetic deletion of Tl4r or Nlrp3 and, e.g. pharmacological inhibition of NLRP3 with MCC950. These findings demonstrate that systemic and intraplantar vincristine converge on a shared NLRP3-dependent neuroimmune mechanism, despite the different initial distribution of vincristine exposure.

      The intraplantar E-selectin experiment in the present study was designed to determine whether E-selectin is sufficient to initiate immune-dependent hypersensitivity locally within the peripheral tissue innervated by DRG neurons. Intraplantar administration restricts exposure to one hind paw, allowing the local effects of E-selectin to be distinguished from its systemic endothelial functions. Local E-selectin administration caused unilateral mechanical hypersensitivity and increased F4/80-positive immune-cell accumulation in the injected footpad. This response required functional E-selectin ligands and was attenuated by depletion of phagocytic cells. In addition, E-selectin promoted the adhesion of bone marrow-derived macrophages but not DRG neurons. Together, these findings demonstrate that locally presented E-selectin is sufficient to recruit or retain phagocytic cells and produce hypersensitivity in the peripheral territory of DRG neurons.

      We have revised the Discussion to explain this anatomical and experimental relationship. We now clarify that the intraplantar E-selectin paradigm tests the local sufficiency of E-selectin-dependent immune signalling rather than reproducing the precise anatomical distribution of inflammation following systemic vincristine.

      “Primary sensory neurons innervating the hind paw have their cell bodies in the DRG, axons within peripheral nerves including the sciatic nerve, and sensory terminals in the plantar skin. Analysis of these tissues therefore examines distinct compartments along the same peripheral sensory pathway. Systemic vincristine increased F4/80-positive immune-cell accumulation in both the DRG and sciatic nerve, demonstrating inflammation surrounding the somatic and axonal compartments of peripheral sensory neurons. Although we did not quantify immune-cell accumulation in the footpad following systemic vincristine, repeated systemic treatment caused no detectable loss of intraepidermal nerve fibres. Moreover, previous work directly comparing systemic and intraplantar vincristine demonstrated that both routes produce mechanical allodynia through a shared NLRP3–IL1β-dependent mechanism, with hypersensitivity attenuated by Nlrp3 deletion or pharmacological NLRP3 inhibition with MCC950 [8,18].”

      “The intraplantar E-selectin paradigm used here was designed to determine whether E-selectin is locally sufficient to induce immune-dependent hypersensitivity within the peripheral territory innervated by DRG neurons. Intraplantar administration restricts E-selectin exposure to one hind paw, allowing its local effects to be distinguished from its systemic endothelial functions. Local E-selectin administration caused unilateral mechanical hypersensitivity and increased F4/80-positive immune-cell accumulation in the injected footpad, with both responses dependent on functional E-selectin ligands and phagocytic cells. Together with the preferential adhesion of bone marrow-derived macrophages rather than DRG neurons to E-selectin, these findings demonstrate the local sufficiency of E-selectin-dependent immune signalling. This paradigm should therefore be interpreted as a mechanistic sufficiency experiment rather than as an anatomical reproduction of systemic VIPN.”

      (2) The rationale of performing spatial sequencing on DRG neurons isolated from vincristine mice is unclear. It is likely that more information could have been obtained from looking at sections from these animals, and there would be a better link to the experiments on BMDMs which follow afterwards. Indeed, the spatial data does not seem to play a key role in the study. There is not a clear link between it (which was carried out on DRGs) and the later focus on macrophages and indeed the NLRP3 inflammasome.

      We appreciate this comment and regret if the rationale linking the spatial transcriptomic analysis to the subsequent mechanistic experiments was insufficiently explicit.

      We first note an important clarification: spatial transcriptomics was not performed on isolated DRG neurons. Intact DRG sections containing neuronal, immune, Schwann-cell, fibroblast, pericyte and other cellular populations were analysed using Visium spatial transcriptomics followed by SPOTlight deconvolution. The experimental design specifically preserved the multicellular DRG environment.

      The rationale arose directly from the preceding experiments. Despite robust mechanical hypersensitivity and increased F4/80-positive immune-cell accumulation, we observed no detectable loss of intraepidermal or myelinated fibres. We therefore used spatial transcriptomics to ask whether functional neuropathy was associated instead with molecular stress and altered communication between neuronal and non-neuronal cells, and whether these responses were modified by E-selectin blockade/deletion. This rationale is already reflected in the Results but has now been made more explicit.

      Importantly, the spatial analysis provides the bridge to the macrophage experiments rather than representing an independent component of the study. The analysis identified immune and stromal populations as prominent signalling hubs, while sensory-neuron populations predominantly occupied receiver roles. Furthermore, E-selectin deletion suppressed inflammatory/interferon-associated transcripts predominantly within immune-cell populations. These observations motivated the subsequent reductionist experiments examining whether E-selectin directly modifies macrophage inflammatory signalling. We have revised the Results accordingly:

      “Given the absence of detectable structural nerve damage despite robust mechanical hypersensitivity and immune-cell accumulation (Fig. 2E–H), we used spatial transcriptomics of intact DRG sections to identify molecular signatures of neuronal stress and altered multicellular signalling underlying VIPN. This approach also enabled us to determine how genetic deletion or pharmacological blockade of E-selectin alters these responses and to identify the cellular compartments most affected by E-selectin perturbation. DRGs were collected following a single vincristine (0.5 mg kg<sup>-1</sup>, i.p.) or saline injection from C57BL/6J mice, Sele<sup>-/-</sup> mice, and C57BL/6J mice pre-treated with E-selectin-neutralising antibody, and analysed for gene-expression changes and spatial signalling patterns.”

      (3) The authors suggest that the E-selectin is enhancing NFkB-induced priming of the NLRP3 inflammasome. LPS+vincristine increased IL-1b release from BMDMs in vitro, which was elevated in the presence of E-selectin. E-selectin also increased ASC speck formation by approx. 20% in vitro. The ASC speck formation in vitro was blocked by MCC950, a specific NLRP3 inhibitor, but the authors went on to use anakinra in vivo using the E-selectin i.pl model. It is really unclear why the switch to anakinra occurred for the in vivo work, as blocking IL-1b is central to many inflammatory pathways, not just NLRP3. Use of MCC950 would have been more appropriate to demonstrate that negative effects on mechanical function are mediated by the NLRP3 inflammasome. As there were no readouts of NLRP3 inflammasome activity measured in any of the mice in vivo (e.g. local ASC specks, IL-1b release, western blot of typical inflammasome components such as IL-1b, caspase-1, ASC or gasdermin D) either at the DRG site or the foot, we cannot say that the cell culture data mimics or models the in vivo conditions at this time.

      We agree with the reviewer that anakinra establishes a requirement for IL-1 signalling, rather than uniquely identifying NLRP3 as the upstream source of IL-1β in the intraplantar E-selectin model. We have therefore revised the manuscript to avoid interpreting the anakinra experiment alone as evidence of NLRP3 activation in vivo.

      However, we respectfully note that the role of NLRP3 in vincristine-induced neuropathy itself has already been established directly in our previous work. Starobova et al. demonstrated that vincristine-induced mechanical allodynia and gait abnormalities are prevented in Nlrp3<sup>-/-</sup> mice and attenuated by systemic MCC950 treatment, and that anakinra prevents VIPN. This study additionally established macrophages as the source of NLRP3-dependent IL-1β in this model (Starobova et al., J Exp Med, 2021; PMID: 33656514), and that anakinra prevents mechanical hypersensitivity that occurs downstream of NLRP3 activation via Il1b release.

      The purpose of the current study was therefore not to re-establish whether NLRP3 is required for VIPN, but to identify an upstream regulator of this previously established pathway.

      The present experiments provide several complementary pieces of evidence:

      (1) E-selectin adhesion enhances ASC-speck formation in vincristine-treated macrophages.

      (2) This enhancement is completely abolished by MCC950.

      (3) E-selectin increases IL-1β release under the same conditions.

      (4) E-selectin enhances NF-κB p65 activation.

      (5) E-selectin-induced mechanical hypersensitivity is attenuated by IL-1 receptor blockade with anakinra.

      (6) E-selectin-adhered, LPS+VCR-treated macrophages produce greater hypersensitivity when transferred into the paw than equivalently treated control-adhered macrophages.

      The ASC-speck/MCC950 and IL-1β experiments are already reported in the manuscript.

      We agree, nevertheless, that without direct measurement of ASC specks/caspase-1/GSDMD in the E-selectin intraplantar model, the manuscript should not state that this experiment independently demonstrates NLRP3 activation in vivo.

      We have therefore changed wording such as:

      “E-selectin-mediated enhancement of NLRP3-driven IL-1β release contributes to the development of VIPN in vivo.”

      to the more precise:

      “E-selectin amplifies NLRP3-dependent IL-1β release from vincristine-stimulated macrophages in vitro, while IL-1 receptor signalling contributes to E-selectin-induced mechanical hypersensitivity in vivo”

      We also added a paragraph to discussion:

      “Although previous genetic and pharmacological studies establish NLRP3 as a critical mediator of VIPN [8,14], NLRP3 activation was not directly measured in vivo following local E-selectin administration in the present study. Thus, our in vivo data establish dependence on IL-1 receptor signalling, whereas the specific amplification of NLRP3 activation by E-selectin is demonstrated directly in macrophages.”

      (4) Additionally, the reliance on the E-selectin administration models for the second half of the paper is curious. It would have been relevant to test whether the immune-modulating inhibitors could also attenuate the vincristine-induced effects on mechanism hypersensitivity, to better link the E-selectin model with the vincristine one.

      We agree that this connection should be made clearer. However, the requested experiment has, in large part, already been performed and published.

      The purpose of the present study was to define how E-selectin is mechanistically linked to VIPN. A critical first question was whether E-selectin could contribute to hypersensitivity through a direct effect on sensory neurons. This cannot readily be resolved within the systemic vincristine model because vincristine has multiple concurrent effects on sensory neurons, immune cells and the vasculature, making it difficult to isolate any direct neuronal effect specifically attributable to E-selectin. Intraplantar administration provided the clearest functional test because it exposes peripheral sensory terminals, where sensory transduction occurs, directly to E-selectin and permits measurement of the resulting unilateral mechanical response. Combining this approach with phagocyte depletion and IL-1 receptor blockade allowed us to determine whether E-selectin-induced hypersensitivity persisted in the absence of immune-cell signalling. Electrophysiological studies in dissociated DRG neurons could provide complementary information, but in the absence of a defined neuronal target or predicted electrophysiological effect, it is unclear which parameters would provide a definitive test.

      Our results support an immune-mediated rather than direct sensory neuron mechanism. E-selectin promoted adhesion of bone marrow-derived macrophages but not DRG neurons. Moreover, intraplantar E-selectin produced unilateral mechanical hypersensitivity and increased F4/80-positive immune-cell accumulation in the injected footpad, while E-selectin-induced hypersensitivity was attenuated by phagocyte depletion and IL-1 receptor blockade with anakinra. Thus, even when E-selectin is administered directly into tissue containing peripheral sensory terminals, its effect on mechanical sensitivity depends predominantly on immune cells and downstream IL-1 signalling.

      Having established this, the second objective was to determine how E-selectin-dependent immune activity is linked to sensory hypersensitivity in VIPN. The downstream immune-modulating experiments proposed by the reviewer have already been conducted in the vincristine model. In our earlier study, macrophage depletion prevented vincristine-induced neuropathy; NLRP3 deficiency prevented vincristine-induced mechanical allodynia and gait abnormalities; MCC950 attenuated VIPN; and IL-1 receptor blockade with anakinra prevented VIPN (Starobova et al., 2021; PMID: 33656514).

      Repeating these experiments would therefore not independently test a new biological question.

      Instead, the present study determines how E-selectin intersects with this established macrophage–NLRP3–IL1β pathway. We demonstrate that pharmacological blockade or genetic deletion of E-selectin prevents vincristine-induced mechanical hypersensitivity and reduces F4/80-positive immune-cell accumulation in the DRG and sciatic nerve, directly establishing a requirement for E-selectin in the systemic vincristine model. We then show that E-selectin adhesion enhances vincristine-induced NF-κB activation, NLRP3 inflammasome assembly and IL1β release in macrophages, with inflammasome activation abolished by MCC950. Finally, the finding that anakinra attenuates intraplantar E-selectin-induced hypersensitivity demonstrates that E-selectin and vincristine converge functionally on IL-1 receptor signalling in vivo.

      Together, the previous and present studies interrogate successive components of the same mechanism. The earlier work established that macrophages and NLRP3–IL1β signalling are required for vincristine-induced neuropathy. The present study demonstrates that E-selectin is required for vincristine-induced immune-cell accumulation and hypersensitivity, acts predominantly through immune cells rather than directly on sensory neurons, and enhances vincristine-induced NLRP3–IL1β signalling in macrophages. The intraplantar E-selectin experiments therefore provide a mechanistic bridge between E-selectin-dependent immune activity and sensory hypersensitivity rather than representing a separate model unrelated to VIPN.

      We have revised the Discussion to make the rationale for these experiments and their mechanistic connection to the systemic vincristine model explicit.

      We have now explicitly connected the two studies in the Discussion:

      “These findings extend our previous demonstration that macrophage depletion, genetic or pharmacological inhibition of NLRP3, and IL-1 receptor antagonism protect against vincristine-induced neuropathy [8,14]. Here, we sought to define how E-selectin is mechanistically linked to this established macrophage–NLRP3–IL1β pathway and to sensory hypersensitivity. A critical component of this question was whether E-selectin acts directly on sensory neurons or indirectly through immune cells. Intraplantar administration exposed peripheral sensory terminals directly to E-selectin while permitting assessment of a local, unilateral mechanical response. However, E-selectin promoted macrophage but not DRG neuron adhesion, and E-selectin-induced hypersensitivity was attenuated by phagocyte depletion and IL-1 receptor antagonism. These findings support a predominantly immune-mediated mechanism rather than direct sensitisation of sensory neurons.”

      “Together with the protection afforded by E-selectin blockade or deletion in the systemic vincristine model, our findings position E-selectin at the point of convergence between immune-cell recruitment and inflammatory signalling in VIPN. E-selectin facilitates macrophage accumulation within peripheral neuronal tissues while also enhancing vincristine-induced NF-κB activation, NLRP3 inflammasome assembly and IL1β release. E-selectin thereby couples immune-cell recruitment and activation to IL1R-dependent sensory hypersensitivity.”

      (5) Details are missing from the figure legends and the methods. The concentrations of compounds used in cell culture and exposure times are not clear.

      We thank the reviewer and acknowledge that including these details in the figure legends rather than only the methods section improves clarity. The Supplementary Methods specify that BMDMs were primed with LPS (10 ng/mL) for 3 h, followed where indicated by MCC950 (10 μM; 30-min pretreatment), vincristine (100 μM; 6 h), doxorubicin (50 μM; 6 h), cyclophosphamide (100 μM; 6 h), or nigericin (5 μM; 45 min). E-selectin, P-selectin and IgG-coated surfaces were used at 5 μg/mL.

      We have revised the legends for Figures 4–6 and Supplementary Figure S5 to specify the concentrations and exposure times for all relevant in vitro treatments, including LPS, vincristine, nigericin, MCC950, doxorubicin and cyclophosphamide, as well as the concentrations used for E-selectin, P-selectin and control-coated surfaces. These additions ensure that the experimental conditions can be understood directly from the corresponding figures.

      Reviewer #2 (Public review):

      (1) Spatial transcriptomics

      The spatial transcriptomics data need to be improved in terms of visualization. The authors should plot genes that define the cell types in the sequencing dataset, and also show the cellular map on the cut, not only UMAPs. Can the authors not use the n=3 samples per condition to perform some statistical analyses? While the CellChat analyses are informative, they are difficult to read. Fold change over control when comparing conditions and pathways may be a better way of visualization.

      We thank the reviewer for these constructive suggestions and have clarified the presentation, statistical analysis and rationale of the spatial transcriptomic experiments.

      First, the n=3 biological replicates per condition were already used for statistical inference. Visium barcodes originating from each individual animal were aggregated to generate one pseudobulk count matrix per animal, thereby avoiding pseudoreplication of individual spatial spots. Differential expression was analysed using DESeq2 with a negative binomial model including batch as a covariate, followed by Wald testing and Benjamini–Hochberg correction. Differentially expressed genes were defined as adjusted P<0.05 and |log2FC| ≥0.585. We have revised the Methods and Results to make clearer that the three animals per condition represent independent biological replicates and that individual Visium spots were deliberately not treated as independent replicates.

      Second, cell populations were inferred using SPOTlight against an annotated single-cell RNA-seq reference. We have clarified the reference-guided annotation strategy and expanded the description of the defining neuronal and non-neuronal populations. The objective of the spatial analysis was not to generate a new DRG cell atlas, but to determine how vincristine-induced transcriptional responses are distributed across DRG cellular compartments and how these responses are altered by genetic or pharmacological perturbation of E-selectin.

      Importantly, the transcriptional responses identified here are consistent with several independent transcriptomic analyses of DRG following vincristine treatment. Our previous bulk RNA-seq study identified 368 differentially expressed genes following vincristine treatment, with cell-type and gene-set enrichment analyses demonstrating predominant effects on immune-system-associated genes (Starobova et al., 2020; PMID: 31260808). An independent study by Bernard et al. similarly identified substantial transcriptional changes in DRG following systemic vincristine, including inflammatory/immune and neuronal injury-associated processes (Bernard et al., 2022; PMID: 36559317). More recently, transcriptomic profiling of peripheral nervous tissue following vincristine alone and as part of the CVAD combination regimen demonstrated distinct, time-dependent and treatment-specific neuroimmune responses, with vincristine contributing prominently to the inflammatory phenotype (Starobova et al., 2026; PMID: 42294786). Together, these independent datasets support a reproducible vincristine-induced transcriptional response involving neuroimmune and neuronal stress pathways. The present spatial analysis extends these bulk-transcriptomic findings by resolving these responses across neuronal, immune, Schwann-cell and stromal compartments and determining how they are altered by E-selectin perturbation.

      Finally, we acknowledge that CellChat networks are information-dense. However, CellChat communication probabilities are model-derived measures of predicted intercellular signalling and are not directly equivalent to conventional gene-expression fold changes. Expressing these values as fold change over control could therefore imply a quantitative interpretation that is not appropriate for this analysis. We have consequently retained the pathway-specific sender/receiver/mediator/influencer representation and clarified the methodological basis and interpretation of the CellChat communication probabilities in the Methods.

      “To ensure that statistical inference was performed at the level of independent biological replicates rather than individual Visium spots, barcodes originating from the same animal were aggregated to generate one pseudobulk count matrix per animal (n = 3 biological replicates per condition). Individual Visium spots were not treated as independent biological replicates.”

      “Cell-type composition of Visium spots was inferred using seeded non-negative matrix factorization (NMF) regression-based deconvolution implemented in SPOTlight (v1.8.0) [29]. A harmonized cross-species single-cell RNA-seq dataset containing previously annotated neuronal and non-neuronal DRG populations was used as the reference [30]. Gene expression and metadata from the spatial transcriptomics dataset were used to construct a SpatialExperiment object, and marker-gene profiles from the reference clusters were used to generate cell-type-specific topic profiles. These profiles were projected onto individual Visium spots to estimate the relative contribution of each cell population. Thus, cell-type assignments represent reference-guided estimates of cellular composition rather than single-cell measurements and were used for spatial visualization and downstream cell-type-resolved analyses.”

      “Cell–cell communication analysis was performed using CellChat [31]. The merged spatial Seurat object was split by condition to generate separate CellChat objects, and ligand–receptor interactions were inferred using the mouse secreted signalling database. Communication probabilities were calculated using the tri-mean method, with interactions involving fewer than 10 cells excluded. Pathway-level communication networks were inferred and aggregated to compare signalling strength and interaction numbers across cell types. For selected pathways, CellChat-derived communication probabilities and network centrality metrics were used to identify predominant sender, receiver, mediator and influencer populations and contributing ligand–receptor interactions. As CellChat communication probabilities are model-derived measures integrating ligand and receptor expression across interacting cell populations, they represent predicted relative communication strength rather than conventional gene-expression values and were therefore not interpreted or presented as gene-expression fold changes between conditions.”

      (2) F4/80 DAB staining

      In Figure 1B, the % DAB is not easy to understand. It would be better to do the staining also via IF, and then maybe to count nuclei. The corresponding figures shown in the supplemental figure are not convincing. If F4/80 is not working well, Iba1 could be an alternative.

      We thank the reviewer and agree that the original label “% DAB” did not adequately describe the quantitative endpoint. We have clarified the Methods and figure legend and changed the axis label to “F4/80-positive area.”

      The endpoint represents the percentage of analysed tissue area occupied by DAB-positive F4/80 immunoreactivity. It is not intended to represent the percentage of macrophages or the percentage of nuclei that are F4/80 positive. Quantification of immunoreactive area and counting of labelled cells are alternative approaches to assessing macrophage accumulation, each with distinct advantages and limitations. Because F4/80 is expressed on the cell membrane and within the cytoplasm rather than the nucleus, nuclear counting would require additional staining and reliable assignment of individual nuclei to irregularly shaped F4/80-positive profiles. This can be particularly difficult in densely stained or morphologically complex tissue and would not necessarily provide a more accurate measure of macrophage burden.

      The detection and quantification method was selected to suit the endpoint. Chromogenic F4/80 immunohistochemistry provides permanent, spatially resolved staining that can be quantified across a defined tissue area using consistent thresholding. In our experience, immunofluorescence in formalin-fixed, paraffin-embedded neuronal tissue can introduce additional sources of variability, including tissue autofluorescence, background signal and sensitivity to imaging parameters. Changing to immunofluorescence would therefore alter the detection method without necessarily improving the biological measurement.

      Similarly, replacing F4/80 with Iba1 would introduce a different marker with a different expression profile rather than validate the same endpoint. The F4/80 assay used here produced specific and quantifiable staining, included appropriate isotype controls, and was performed using a previously optimised and validated protocol. Quantification was conducted by a blinded observer using an automated image-analysis workflow. We have therefore retained the established DAB-based F4/80 assay and clarified throughout the manuscript that the reported measure is F4/80-positive tissue area rather than macrophage number.

      “F4/80 staining was performed using a previously optimised and validated immunohistochemical protocol for mouse DRG [8,24,25]. Sections were stained with rat anti-mouse F4/80, developed using ABC/DAB, counterstained with haematoxylin, scanned, and quantified by a blinded observer using Visiopharm. Representative images are provided in Supplementary Figure S1.”

      “Fig. 1. Inhibition of E-selectin and VCAM-1, but not other adhesion molecules, attenuates vincristine-induced mechanical hypersensitivity and increased F4/80-positive area in the dorsal root ganglia and sciatic nerves. Effects of blocking antibodies against VCAM-1 (VCAM1ab; A, B), ICAM-1 (ICAM1ab; C, D), PECAM-1 (E, F), P-selectin (P-sel ab; G, H) and E-selectin (E-sel ab; J, K) on vincristine-induced mechanical hypersensitivity (A, C, E, G, J; PWT, paw withdrawal threshold) and F4/80-positive area in the dorsal root ganglia (DRG) and sciatic nerve (SN) (B, D, F, H, K). Black arrows indicate i.p. administration of blocking antibodies (10 mg/kg), isotype control antibodies (IgG2b or IgG1; 10 mg/kg) and vincristine (0.5 mg/kg). VCAM-1 and E-selectin blockade attenuated vincristine-induced mechanical hypersensitivity (A, J) and the associated increase in F4/80-positive area in the DRG and SN (B, K), whereas PECAM-1 and P-selectin blockade was partially effective (E–H) and ICAM-1 blockade had no effect (C, D). F4/80-positive area was quantified as the percentage of analysed tissue area occupied by thresholded DAB-positive F4/80 immunoreactivity and does not represent the percentage or number of F4/80-positive cells. Data are presented as mean ± SEM (n = 5–7 per group). Statistical significance (#P < 0.05) was determined using repeated-measures two-way ANOVA or one-way ANOVA with Šídák’s multiple-comparisons test.”

      (3) Mouse genetic backgrounds

      The authors should define the background of all the mice used. Have they been back-crossed to B6j mice? One cannot compare C57BL6J mice with full knockouts if they are not littermate controls. Especially immunological responses are completely dependent on the background of mice. See, e.g. PMID: 40568896.

      We thank the reviewer for raising this important point and have now clarified the genetic background and provenance of all mouse lines in the Methods. The Sele<sup>-/-</sup> and Fut4<sup>-/-</sup>/Fut7<sup>-/-</sup> lines were maintained on a C57BL/6 background. These strains have previously been reported to have been backcrossed onto the C57BL/6 background for at least 10 generations (Barbier et al., 2020; PMID: 32341362), and Fut4<sup>-/-</sup>/Fut7<sup>-/-</sup> mice have independently been characterised on a C57BL/6 background (Wang et al., 2013; PMID: 23562273). The ASC-citrine reporter line was generated and characterised as described by Tzeng et al. (2016; PMID: 27346360).

      We acknowledge that age-matched C57BL/6J mice, rather than littermate wild-type controls, were used for the knockout comparisons, and this has now been stated explicitly in the Methods. We therefore interpret the genetic experiments together with the complementary pharmacological experiments. Importantly, the phenotype observed in Sele<sup>-/-</sup> mice is independently supported by E-selectin-neutralising antibody experiments performed entirely in C57BL/6J mice, which similarly attenuated vincristine-induced mechanical hypersensitivity and the associated increase in F4/80-positive area. Thus, the pharmacological experiments provide an independent same-background line of evidence supporting the contribution of E-selectin to vincristine-induced neuropathy.

      “Behavioural and in vivo experiments were performed using 8–10-week-old male C57BL/6J, E-selectin-deficient (Sele<sup>-/-</sup>), fucosyltransferase 4/7 double-knockout (Fut4<sup>-/-</sup>Fut7<sup>-/-</sup>), and ASC-citrine reporter mice. The Sele<sup>-/-</sup> and Fut4<sup>-/-</sup>Fut7<sup>-/-</sup> lines were maintained on a C57BL/6 background and have previously been reported to have been backcrossed onto this background for at least 10 generations [15]. The C57BL/6 background of Fut4<sup>-/-</sup>Fut7<sup>-/-</sup> mice has also been independently reported [16]. ASC-citrine reporter mice were generated and characterised as previously described [17].”

      Although the genetic studies used age-matched C57BL/6J rather than littermate controls, the protective phenotype observed in Sele<sup>-/-</sup> mice was independently recapitulated by pharmacological E-selectin blockade in C57BL/6J mice, supporting an E-selectin-dependent mechanism while reducing the likelihood that the findings are attributable solely to genetic-background effects.

      (4) ICAM-2

      Could the authors comment on the role of ICAM2? Why was this not tested as well?

      We thank the reviewer for raising ICAM-2. Our initial panel was designed to sample major inducible endothelial adhesion pathways implicated in inflammatory leukocyte recruitment, including selectins and members of the immunoglobulin superfamily. ICAM-2 was not included because its endothelial regulation and function differ from those of ICAM-1, VCAM-1 and E-selectin. ICAM-2 is constitutively expressed on endothelial cells and participates predominantly in leukocyte adhesion/transendothelial migration, while inflammatory cytokines can decrease rather than increase endothelial ICAM-2 expression (PMID: 10223354; PMID: 10574717).

      We agree, however, that absence of ICAM-2 testing means that the manuscript should not imply that all relevant endothelial adhesion molecules were comprehensively excluded.

      “By examining representative members of major vascular adhesion-molecule families, we …”

      Additionally, ICAM-2 was not examined in the present study. Unlike inducible ICAM-1 and E-selectin, ICAM-2 is constitutively expressed on endothelial cells and has context-dependent roles in leukocyte transmigration; inflammatory cytokines can reduce endothelial ICAM-2 expression [42,43]. Thus, although our results identify E-selectin and VCAM-1 among the adhesion molecules tested, they do not exclude contributions from ICAM-2 or other endothelial adhesion pathways.

    1. Author response:

      Reviewer #1 (Public review):

      Summary:

      The authors describe clone-level dynamics of a SAR11 genomospecies in the Mediterranean, based on a dataset of LR-OBCs they previously generated. They distinguish 'consortia' of LR-OBC clones that co-vary/fluctuate together, primarily across depth. The authors find these consortia to be independent of phylogenetic origin within the genomospecies, concluding that their decoupling is evidence of a shift away from the current ecotype conceptual framework.

      This study provides valuable, detailed information about natural variation in SAR11 LR-OBCs within populations, but the conclusions reached are not supported by the data.

      Strengths:

      This is an exceptional dataset for studying this problem because of the sequencing depth and use of long-read technology.

      Weaknesses:

      The disconnect of LR-OBC phylogeny from species' phylogeny makes sense, for well-known reasons, but is not supported by statistical evidence for incongruent phylogenetic topologies. Also, this hypervariable genome region was described early, and evidence suggests it is transferred between strains by recombination. This work is not cited, and without this important background, it will be challenging for naïve readers to interpret this manuscript. It seems likely that the genome content and LR-OBCs are evolving independently because the latter are transferred by homologous recombination and are under selection related to viral predation.

      We are not sure to which incongruent phylogenetic topologies the reviewer is referring to, different OBCs cannot be compared because they do not share genes (Haro-Moreno et al., 2025). The few cases in which genes are shared the topology does follow the one of the core genome.

      It is true that OBCs can be exchanged between separate clones (glycotypes) but as proven there and in Enterobacteriales previously (Holt et al, 2020) the ANI among shared OBC genes is similar to the ANI between the core genomes, thus the exchanges are very unusual and old. The so-called serotypes (different OBC or capsular antigens) have been used in the clinical environment to predict pathogenicity of bacteria that often depends on genomic islands carrying the virulence factor genes.  Along similar lines we have used OBCs to predict the flexome and pangenome size (Haro-Moreno et al., 2025).

      I also struggle with the authors' definitions of clones (at 97% sequence similarity). I would expect clones to be near-100% identical. The differing 'ranks' across the subspecies level are not defined in the manuscript, so the discussion lacks clarity on what the novel discoveries really are.

      The average nucleotide identity of reads recruited to the reference OBCs was 99.65% — well above the 97% threshold. We set the threshold at ≥97% identity over a minimum of 90 nucleotides (see Methods) as a conservative lower bound to accommodate the short length of Illumina reads (≤150 nt) and their associated error rate, which is not corrected by coverage in this analysis. Crucially, we are evaluating the presence of genes that are part of the flexome i.e., we are detecting presence/absence rather than similarity. For this purpose, the threshold used is acceptable to identify OBC type representation in the metagenomes.

      Reviewer #2 (Public review):

      Summary:

      Martin Cuadrado and coauthors use O-chain biosynthesis gene clusters (OBCs) within metagenomes and SAGs to determine clone-level differences in distribution in the Mediterranean Sea. They observe two distinct consortia: one specific to surface samples (C1) and another to deep/winter samples (C2). In the discussion, the authors suggest that differences in carbon utilization capabilities in the ocean may drive this partitioning.

      Strengths:

      One of the main strengths of this paper is its use of specific clonal barcodes to analyze strain-level population structure, which allows researchers to discern distribution patterns through a different lens, with higher resolution than 16S genes. The work is important and could be a more widely used tool for examining SAR11 distributions in the ocean.

      Weaknesses:

      I feel the authors fall short in showing whether partitioning across consortia could be generalized beyond the Mediterranean Sea. If so, the work would be more impactful with additional data beyond the Mediterranean. Furthermore, the authors could have contextualized OCB sequence variability with other SAR11 clade genomes, such as those reported by Freel et al., 2025 (doi:10.1038/s41467-025-67043-6), to identify additional patterns that could explain differences between consortia; could these differences be functional? The authors invoke possible differences in the flexome of genomes within the identified consortia to explain this partitioning, but the hypothesis remains largely unexplored. For instance, the authors discuss differences in environmental context across consortia (nutrient availability, light intensity, etc.), which may in turn be associated with different functional capabilities. Is the incidence of genes related to efficient nutrient uptake systems or proteorhodopsin phototrophy increased in the surface consortium? The authors do not examine any specific functions in SAGs or whole genomes available in databases that may share the OCBs studied here. If those functions don't explain the changes, would viral specificity be the reason? I feel this discussion is needed, at least in the last section.

      The reviewer is right to note the geographic and taxonomic restriction of the current study. Extending the analysis to other regions and taxa is not straightforward: it requires long-read metagenomic coverage deep enough to recover hundreds of OBC sequences from a single genomospecies, and a reference OBC catalogue of comparable richness — conditions not yet met by available datasets. The novel SAR11 genomes described by Freel et al. 2025, while valuable, do not provide sufficient OBC sequence numbers for this type of population-level analysis. We acknowledge this limitation and frame the present work explicitly as a proof-of-concept that paves the way for broader surveys. We note that long-read metagenomics is currently the most practical approach to recovering population-level OBC diversity; species-sorted SAG campaigns are an alternative but are substantially more demanding and expensive. We will make this discussion of scope and future directions clearer in the revised manuscript.

      Regarding the specific genes that are variable between clone flexomes we have evidence showing that they are significantly biased towards metaparalogs (Molina-Pardines et al., 2025) (Rodriguez-Valera and Molina-Pardines 2026), largely transporters that produce an increase in the diversity in the number of substrates that the cells can use. The study of the specific SAGs analyzed here was beyond our scope, they are few and not complete and nothing indicates that differences with the paper cited above will be found.

      References

      Haro-Moreno JM, López-Pérez M, Molina-Pardines C, Rodriguez-Valera F. 2025. Large diversity in the O-chain biosynthetic cluster within populations of Pelagibacterales. mBio 16:e0345524. DOI: https://doi.org/10.1128/mbio.03455-24

      Holt KE, Lassalle F, Wyres KL, Wick R, Mostowy RJ. 2020. Diversity and evolution of surface polysaccharide synthesis loci in Enterobacteriales. The ISME Journal 14:1713–1730. DOI: https://doi.org/10.1038/s41396-020-0628-0

      Molina-Pardines C, Haro-Moreno JM, Rodriguez-Valera F, López-Pérez M. 2025. Extensive paralogism in the environmental pangenome: a key factor in the ecological success of natural SAR11 populations. Microbiome 13:41. DOI: https://doi.org/10.1186/s40168-025-02037-6

      Rodriguez-Valera F, Molina-Pardines C. 2026. On the biological meaning of the population pangenome. Trends in Microbiology 34:34–41. DOI: https://doi.org/10.1016/j.tim.2025.07.004

    1. Author response:

      We thank the editors and both reviewers for their careful reading of our manuscript and for their constructive and generous assessments. We are pleased that the reviewers found our knock-in HiBiT approach informative and the conclusions well supported. Below we provide provisional clarifications on several technical points and outline the revisions we plan to include in the revised version. A full point-by-point response will accompany the revised manuscript.

      Reviewer #1 (Public review):

      (1) Presentation of bar graphs: technical replicates versus independent experiments; apparent discrepancy between Figure 3B and Figure 4A.

      We apologise for the lack of clarity in our description of replication, and we are grateful for the opportunity to correct it here. Our statement that each experiment was performed “at least twice” was intended to mean that each experiment consisting of three independent biological replicates was itself repeated at least twice — that is, a minimum of six independent experiments in total. In the revised version we will state the experimental design explicitly and will re-plot the secretion data so that each symbol represents one independent experiment (the mean of its technical replicates), with the number of symbols corresponding to the number of independent experiments actually performed.

      Regarding the difference between Figure 3B and Figure 4A, we believe this reflects a difference in culture scale rather than inter-experimental variability per se. Figure 3 was performed in 10-cm dishes (3 × 10<sup>6</sup> cells in 10 mL of medium, and cultivate for 48 hours), whereas Figure 4 was performed in 1 well of a 12-well plate (5 × 10<sup>5</sup> cells in 1 mL of medium, and cultivate for 12 hours). The cell density and the cell-number-to-medium-volume ratio therefore differ substantially between the two sets of experiments, and we consider this the most likely explanation for the different relative distribution between the 10K and 100K fractions. We will describe this point carefully in the text and in the figure legends of the revised version so that readers can interpret the two figures appropriately.

      (2) Whether the attenuated CMV promoters used in Figure 5 were also used in Figures 6 and 7.

      This is a fair point, and we will address it experimentally. We plan to introduce the promoter-attenuation system into the KEAP1 expression constructs — generating approximately Δ3, Δ4 and Δ5 variants — and to measure the secretion rate of KEAP1 at these reduced expression levels. If the secretion rate is comparable to that obtained with the wild-type promoter, we will retain the existing data and state explicitly that expression level does not affect the interpretation. If instead the secretion rate changes with expression level, we will generate the corresponding mutants in the attenuated-promoter background and repeat the analysis. We will report the outcome either way in the revised version.

      (3) Missing technical detail on gel loading in Figure 4B, and the number of times this experiment was performed.

      We apologise for this omission. Loading was normalised as a percentage of total, so that the cell lysate and the pellet fractions derived from the supernatant are directly comparable; the band intensities shown can therefore be compared between fractions. We will add a full description of this normalisation to the Materials and Methods of the revised version.

      Regarding replication, this experiment uses the large-scale culture format and is accordingly not one that we repeat many times. We have, however, confirmed reproducibility, and we will state clearly in the revised version how many times the experiment was performed and that the result was reproducible.

      Reviewer #2 (Public review):

      (1) The exact form of secreted p62 was not further characterised.

      We agree that this is an interesting and important question. The amount of secreted p62 is extremely small, however, and further biochemical characterisation is beyond what we can achieve reliably at present. We intend to pursue this in follow-up work, including mass-spectrometric identification of co-secreted proteins, nanoparticle tracking analysis to compare particle size and distribution between fractions, and ion-exchange chromatography to probe the surface charge of the particles. We will report these analyses in a separate study, and we will state the limitation explicitly in the revised discussion.

      (2) Binding to other cargo receptors (e.g. NBR1 D50R) was not excluded.

      We appreciate this suggestion. p62 bodies contain a large number of molecules in a complex, highly interconnected assembly, and the factors within p62 bodies that influence p62 secretion are unlikely to be limited to a single protein; identifying all of them is not straightforward. We therefore consider this an important direction for careful future analysis rather than one we can resolve within the present manuscript, and we will say so in the revised discussion.

      (3) The supernatant fraction was not fully analysed.

      We agree that this point is important, and we plan to address it experimentally in the revised version. We will extend the analysis to all fractions, measuring the 100K supernatant, 100K pellet and 10K pellet for Δ5.0 p62-WT and p62-K7A/D69A in wild-type HEK293T cells and in ATG5 KO and FIP200 KO cells. We expect this to clarify how p62 oligomerisation affects the autophagosome-formation-dependent component of secretion, and in particular whether “soluble” p62 release is continuous, ATG5/FIP200-dependent, and sensitive to lysosomal inhibition.

      (4) Vesicle contents beyond p62 and KEAP1, including lipidated LC3 and other autophagy proteins.

      We have addressed this question in our previous work (Saito et al., FEBS Open Bio, 2026), in which we used LC3 HiBiT knock-in cells for a detailed analysis and also confirmed the secretion of NDP52 and OPTN. We will cite and describe these findings more explicitly in the revised version. As noted above, we recognise proteomic analysis of the secreted fractions as an important task for future work.

      (5) Apparent inconsistency between Figure 3C and Figure 4 in the absence of detergent.

      Reviewer #1 raised a related point, and we believe the same explanation applies: the two experiments differ in culture scale. Figure 3 was performed in 10-cm dishes (3 × 10<sup>6</sup> cells in 10 mL of medium, and cultivate for 48 hours), whereas Figure 4 was performed in 1 well of 12 well-plate (5 × 10<sup>5</sup> cells in 1 mL of medium, and cultivate for 12 hours). We will describe this difference carefully in the text of the revised version so that the two figures can be compared on the correct basis. We are grateful to the reviewer for noting that this does not affect the conclusions of the paper.

    1. Author response:

      The following is the authors’ response to the original reviews.

      eLife Assessment:

      This study provides important insights into how species-specific variation in oxytocin receptor regulatory architecture contributes to diversity in brain expression patterns and social behaviors. By generating multiple BAC transgenic mouse lines carrying the prairie vole oxytocin receptor locus and combining anatomical, molecular, behavioral, and chromatin-structure analyses, the authors present convincing evidence that distal regulatory elements constrain peripheral expression while permitting brain expression aligned with behavior. This study provides an experimental framework and a resource that are of value for dissecting how regulatory variation in neuromodulatory systems contributes to species differences in social behavior. This work will be of interest to those interested in social behavior, oxytocin, neuromodulation, and related conditions.

      We thank the Editors and Reviewers for their careful evaluation of our manuscript and constructive comments. We appreciate the recognition of the significance and novelty of our study, as well as the value of our experimental approach for understanding how species-specific regulatory architecture contributes to variation in oxytocin receptor expression and social behavior diversity. We have carefully addressed the reviewers’ comments and recommendations and have revised the manuscript accordingly. We are not looking for an updated eLife Assessment, and would be happy for the editors to assess the revised version without involving the original reviewers again. Our point-by-point responses to the reviewers’ comments are provided below.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      The manuscript by Tsukamoto et al. describes a compelling approach to understanding whether inter-species differences in social behavior might emerge from differential expression patterns of the oxytocin receptor (Oxtr) in the brain. To this end, they genetically engineer BAC transgenic mouse lines with insertions of a large construct incorporating prairie vole Oxtr gene and surrounding regulatory elements. They name these lines Koi lines. They first evaluate if prairie vole-like Oxtr expression is reproduced in the Koi mouse lines, and they find heterogenous patterns across different lines that do not depend on the number of insertions. While they found that Koi mice can reproduce vole-like expression in PFC, NAc, and BLA, the reproduction was never complete: one Koi line had NAc and mPFC expression, another had BLA expression, etc. They confirmed major expression patterns across 3 methods: crossing with LacZ reporter line, in situ hybridization, and ligand binding (autoradiography). To determine the expression pattern of the BAC insert but not endogenous Oxtr, the authors generated new mouse lines by crossing Koi lines with Oxtr -/- line. Importantly, they found that Oxtr expression pattern in the mammary gland was similar across all lines, and wild-type mice.

      The authors used Koi:Oxtr-/- lines to test social behavior, specifically partner preference (a behavior specific to prairie voles) and maternal behavior. They find that different Koi lines showed different changes in these behaviors compared to wild-type mice. Moreover, while some lines showed changes in partner preference, others seemed to show changes in maternal behavior. For one of the lines (Koi4), the partner preference and the maternal behavior were incongruent.

      The manuscript then hypothesizes that the Oxtr gene is positioned in different 3D chromatin structures across species and across tissues, leading to more rigid expression in the mammary glands, but more flexible expression patterns in the brain.

      Strengths:

      This study has major implications in the field of oxytocin research, and more broadly in the field of neuromodulation. It is novel, bold, and rigorous.

      Thank you for the thoughtful assessment of our study. We appreciate your recognition of the novelty and rigor of our approach, as well as the potential implications of our findings for understanding how species-specific regulatory architecture contributes to variation in oxytocin receptor expression and social behavior diversity. We also appreciate your detailed summary of our experimental strategy and findings.

      Weaknesses:

      (1) The expression in the brain and mammary gland (Figure 2) was not quantified, preventing a more objective conclusion that the brain has flexible expression and mammary gland expression is rigid.

      Thank you for raising this important point. In Figure 5 of the manuscript, we showed quantitative analyses of Oxtr expression across different brain regions of Koi lines. In the revised manuscript, we have additionally included quantitative analyses of Oxtr expression in the mammary gland (Supplementary Fig.5). Together, these analyses support our conclusion that Oxtr expression is more flexible in the brain, whereas its expression in the mammary gland is relatively rigid.

      (2) In Figure 7, a similar heatmap for the mammary gland is missing.

      Thank you for raising this important point. At the time of our original submission, no Hi-C dataset from mammary gland tissue of any species was available in public repositories. In the manuscript, we therefore analyzed Hi-C datasets from multiple peripheral tissues, which consistently showed TAD architectures that were distinct from those observed in brain-derived tissues. After submission of our manuscript, a human breast-tissue Hi-C dataset was published (Choppavarapu et al., 2025, Cell Reports). Although a mouse mammary-gland Hi-C dataset is still not available, we have now analyzed the Hi-C data generated from normal human mammary gland samples and included these analyses in the revised manuscript (see results and Supplementary Methods). Consistent with the pattern observed across the other peripheral tissues analyzed in our study, the OXTR locus in human mammary tissue is positioned within a pronounced TAD-boundary trough and shows no detectable long-range chromatin interactions (Supplementary Fig.6A). In contrast, the OXT locus lacks a canonical TAD organization (Supplementary Fig.6B). Together with our previous analyses of multiple peripheral tissues, these data provide additional support for the distinct 3D genomic organization of the OXTR locus between brain and peripheral tissues, including the mammary gland. They also further support the conclusion that the TAD landscape differs between the Oxtr and Oxt loci.

      (3) Partner preference in males was not tested.

      Thank you for raising this point. The sex of the animals used for the behavioral experiments was specified in the manuscript (see Results), although we did not explicitly describe our preliminary analyses of partner preference in males. We performed preliminary analyses in both sexes; however, we did not observe robust differences in partner preference among the Koi lines in males. Because reproducible effects were observed in females, we focused our systematic behavioral analyses on females, where the effects were consistent. We have now clarified this point in the revised manuscript (see Results).

      (4) It is unclear if in the behavioral testing the stimulus animals were the same genotype as the focal female or were wild-types. This could have an impact on the behavioral outcome.

      Thank you for this important clarification. In all behavioral experiments, the stimulus animals were wild-type mice. This design was chosen to minimize potential confounding effects arising from genotype-dependent interactions between stimulus and focal animals. Using standardized wild-type stimulus animals allowed us to more directly assess behavioral differences attributable to the genotype of the focal Koi animals. We have clarified this information in the revised manuscript.

      Reviewer #2 (Public review):

      Summary:

      This is a bold and important study and addresses an important question in the field: how species-specific variation in brain oxytocin receptor expression relates to differences in social behavior.

      Tsukamoto et al. generated eight independent transgenic mouse lines (Koi lines) carrying a bacterial artificial chromosome (BAC) encompassing the prairie vole Oxtr locus along with flanking intergenic regions, with the goal of probing the behavioral consequences of species-specific variation in brain Oxtr expression. Across these "volized" lines, the authors claim conserved Oxtr expression in the mammary gland but strikingly divergent patterns of brain expression, none of which fully recapitulate endogenous prairie vole Oxtr distribution, and instead exhibit expression patterns that diverge from both mouse and prairie vole brain Oxtr distribution. Nevertheless, some lines exhibit partial overlap with vole Oxtr expression pattern reported in the literature within specific brain regions, and one line displays partner preference behavior reminiscent of prairie voles. The authors further report line-dependent differences in maternal pup retrieval and crouching behaviors, which they interpret as evidence that variation in brain Oxtr expression can drive variation in social behaviors. Together with analyses of topologically associating domain (TAD) architecture, the authors conclude that brain, but not peripheral- Oxtr expression, is shaped by distal regulatory elements beyond the BAC insert, and propose that such regulatory flexibility underlies evolutionary diversification of social behavior.

      Strengths:

      A particular strength of the study is the generation of multiple independent transgenic lines, which provides a valuable resource for probing regulatory influences on Oxtr expression.

      Thank you for the careful and thoughtful evaluation of our manuscript. We appreciate your kind recognition of the importance of the question addressed in this study and, in particular, the value of generating multiple independent Koi transgenic lines as a resource for studying regulatory influences on Oxtr expression and mechanism underlying social behavior diversity.

      Weaknesses:

      While the study addresses an important question, I have several methodological and conceptual concerns regarding the study in its current form. Some aspects of the study fall outside my primary area of expertise, and I am therefore not in a position to fully evaluate the technical difficulty or rigor of those components, or to judge whether my suggestions would be feasible to implement. I defer to reviewers with relevant expertise for a more detailed assessment of these aspects.

      (1) Each independent Koi line exhibits a distinct brain expression pattern that differs from both wild-type mouse and prairie vole Oxtr expression, complicating the interpretation of the results. The manuscript does not include a direct comparison of brain Oxtr expression patterns in these transgenic lines with those of prairie voles. Instead, expression similarity is inferred primarily from regional localization and compared indirectly with prior literature (Figures 2-5). For those lines that show partial resemblance to prairie vole Oxtr expression patterns, the authors do not assess whether Oxtr-expressing neurons share comparable anatomical projections or transcriptomic identity with prairie vole Oxtr-expressing neurons. Quantification of expression remains largely descriptive, illustrating expression patterns (Figure 2), OXTR protein distribution (Figure 3; images are difficult to evaluate due to low contrast), or Oxtr mRNA levels across selected brain regions in Koi lines, wild-type mice, and mOxtr-/- mice (Figures 4-5), without directly testing similarity to prairie vole expression. In addition, whole-brain expression data are lacking, with analyses restricted to selected sections. While such analyses may be beyond the scope of the present study, these limitations nonetheless complicate interpretation of the central question - namely, whether the observed behavioral phenotypes arise from vole-like Oxtr circuits rather than from distinct, line-specific expression configurations.

      Thank you for this important comment. We agree that a direct comparison with endogenous prairie vole Oxtr expression would facilitate interpretation of the Koi expression patterns. To address this point, we have included representative autoradiographic images of prairie vole brain sections in the revised manuscript (see Supplementary Fig.4). In addition, a recently published study from Larry’s group using RNAscope provides a detailed reference for the cellular and regional distribution of Oxtr in the prairie vole brain (Kiyoshi et al., 2022). Together, these data provide direct visual references for the spatial distribution of OXTR in key regions, including the PFC, NAc, thalamus, and BLA. Because these datasets were generated using different species and experimental conditions, we have clarified in the figure legends that these comparisons are intended as qualitative assessments of spatial distribution rather than direct quantitative comparisons (see Supplementary Fig.4 Legend).

      Our initial goal was to determine whether prairie vole regulatory elements could reproduce vole-like Oxtr expression patterns in mice. The generation of multiple independent Koi lines revealed that the regulatory elements did not faithfully reproduce a single prairie vole-like expression pattern, but instead generated distinct and partially overlapping expression configurations across lines. This finding led us to a broader question: how can regulatory architecture generate diversity in Oxtr expression patterns, and how does this expression diversity influence social behavior? A major experimental advantage of the Koi system is that all independent Koi lines share the same mouse genetic background and differ primarily in their Oxtr expression configurations. This controlled genetic context allows us to examine the relationship between variation in Oxtr expression and behavioral phenotypes while minimizing the substantial differences in genetic background that exist between mouse and prairie vole. Thus, rather than using the Koi lines as attempts to reproduce the prairie vole brain, we use them as a controlled system to investigate how different spatial configurations of Oxtr expression can contribute to diversity in social behavior. Our findings demonstrate that distinct regulatory configurations can generate diverse Oxtr expression patterns within a common mouse genetic background, and that these different expression configurations are associated with distinct social behavioral outcomes. We have made this point clearer in the revised manuscript.

      We also appreciate the reviewer’s suggestion to determine whether Oxtr-expressing neurons in the Koi lines share comparable anatomical projections or transcriptomic identities with Oxtr-expressing neurons in prairie voles. We agree that such analyses would provide important information regarding circuit-level and cellular homology. However, these questions require additional approaches, such as whole-brain mapping of Oxtr expression and projection patterns, single-cell or spatial transcriptomic analyses, and functional manipulation of Oxtr-expressing circuits. These experiments are beyond the scope of the present study and will be important directions for our future investigation.

      We specifically examined the PFC, NAc, and BLA because these regions show notable species differences in social behavior-related circuitry and have been implicated in pair-bonding-related behaviors in prairie voles (Amadei et al., 2017; Walum and Young, 2019). The present analyses therefore provide a focused assessment of Oxtr expression in several behaviorally relevant regions. It would be interesting to constitute a whole-brain comparison or establish circuit-level homology between species in the future work.

      (2) The authors state that Oxtr expression in the mammary gland is similar across all Koi lines and the mOxtr-IRES-Cre knock-in line. However, the images presented in Figure 2 appear to show differences in anatomical detail across lines, and no quantitative analysis is provided to support the claim of equivalence.

      Thank you for this observation. We acknowledge that there are minor differences in staining intensity across mammary gland images in Figure 2. These variations are primarily attributable to technical factors, such as differences in LacZ staining penetration associated with variable lipid content in the mammary fat pad. Importantly, despite these intensity differences, the spatial distribution of LacZ signal is highly consistent across Koi lines, with similar ductal patterns observed throughout the mammary gland. In contrast to the brain—where both the regional distribution and expression levels of Oxtr vary substantially across lines—the mammary gland consistently exhibits robust and widespread expression across all Koi lines. We included quantitative analysis of Oxtr expression in the mammary gland using qRT-PCR (Supplementary Fig5), which shows comparable expression levels across different Koi lines.

      (3) The conclusion that integration site rather than copy number determines the observed BAC transgene expression patterns (Lines 202-203) is not fully supported by the data. First, the authors did not compare multiple copy numbers at the same genomic insertion site, making it impossible to disentangle copy-number effects from position effects. Second, BAC copy number does not necessarily scale linearly with expression; higher copy numbers can have a repressive effect on gene expression (Garrick et al, Nat Genet, 1998).

      Thank you for this important comment. We agree that the current study cannot fully disentangle the effects of integration site from those of transgene copy number. We also agree that BAC copy number does not necessarily correlate linearly with transgene expression, and that high-copy transgene arrays can lead to transcriptional silencing through mechanisms associated with repressive chromatin states. Importantly, the transgene copy numbers in our Koi lines ranged from 1 to 12 copies, which is substantially lower than the very high-copy arrays associated with transcriptional silencing in the study by Garrick et al. (1998). In that study, the silencing phenotype was observed in mice carrying transgene arrays containing hundreds of copies, and the high-copy arrays were associated with a more condensed and transcriptionally inactive chromatin state. Thus, although we cannot exclude an effect of copy number in our Koi lines, the strong repression associated with very high-copy transgene arrays is unlikely to directly account for the expression variation observed among our relatively low-copy Koi lines. Nevertheless, we acknowledge that the available data do not allow us to conclude that integration site is the sole determinant of the observed expression differences. The current data are consistent with genomic integration site being a major contributor to the variation in BAC transgene expression patterns observed among the Koi lines, while effects of transgene copy number cannot be excluded. We have therefore softened the statement in the revised manuscript (see Results) accordingly.

      (4) While I am not an expert in TAD analysis, the observed differences in 3D architecture around Oxtr are consistent with a role for long-range regulatory interactions. However, these analyses appear largely descriptive and correlative, and establishing a causal contribution of 3D chromatin organization to Oxtr regulation by distal elements would likely require direct perturbation of TAD boundaries or looping interactions. I recognize that such experiments may be beyond the scope of the present study, but clarifying this limitation in the interpretation would be helpful.

      Thank you for this thoughtful comment. We agree that our analyses of 3D chromatin architecture, while suggestive of a role for long-range regulatory interactions, are inherently correlative in nature. Establishing a causal contribution of TAD organization to distal Oxtr regulation would require a series of experiments including direct perturbation of chromatin structure, through targeted disruption of TAD boundaries or looping interactions using genome engineering approaches. As the reviewer noted, such experiments are technically demanding and beyond the scope of the present study. Accordingly, we have revised the Discussion (see Discussion) to more explicitly acknowledge this limitation. We clarify that our TAD analyses provide a correlative framework supporting the involvement of distal regulatory architecture in shaping brain-specific Oxtr expression, rather than definitive evidence of causality. These findings nonetheless generate testable hypotheses for future studies aimed at directly interrogating the causal role of chromatin architecture in Oxtr regulation.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      Koi4 line is the only one that replicates the partner preference of prairie voles. This line has low ligand binding in the NAc, unlike the strong expression in the Lac-Z, ISH, and qRT-PCR data. However, ligand binding was strong in the lateral septum and the thalamus. Koi1 and Koi3 also had ligand binding in LS, but not in the thalamus. Taken all together, could this mean that thalamic expression is perhaps what drives partner preference? Given that prairie voles express AvpR1 in the thalamus, and that there is ligand promiscuity between Oxtr and AvpR1a, could the authors speculate whether thalamus vasopressin modulation could play a more important role in partner preference?

      Thank you for raising this insightful point. The Koi-4 line showed robust transgene expression in NAc, as demonstrated by the Lac-Z reporter, RNAscope and qPCR analyses. Notably, strong Oxtr expression in the thalamus was consistently observed across all methods. Recent studies have highlighted important roles for several thalamic nuclei in social memory, social cognition, and the integration of sensory and motivational information (Chen et al., 2024; Rangel, Baldo, & Canteras, 2018; Wolff & Vann, 2019). Given that partner preference likely requires the coordinated engagement of social recognition, social memory, selective attention, arousal, reward processing, and multisensory integration, thalamic Oxtr expression in Koi-4 line may indeed contribute to the behavioral phenotype. Consistent with this possibility, our preliminary chemogenetic experiments suggest that activation of the Oxtr-positive thalamic neurons partially contributed to the parter preference phenotype observed in the Koi-4 line (unpublished data). Therefore, it is possible that vasopressin signaling with thalamic circuits may also contribute to partner preference. While our current data do not allow us to distinguish between vasopressin- and oxytocin- mediated effects, this represents an intriguing hypothesis that warrants future investigation.

      Reviewer #2 (Recommendations for the authors):

      (1) Lines 262-286 and 289-312: The description of the statistical analyses in the Results section is overly detailed and sometimes difficult to follow. The authors could improve clarity by leading with the main behavioral findings and reserving the full statistical reporting for the Methods section.

      Thank you for your helpful comment. We agree that presenting the main behavioral findings before the detailed statistical results improves the clarity and readability of the Results section. We have therefore revised the descriptions of the Partner Preference Test (see Results) and Pup Retrieval Test (see Results) to lead with the main behavioral findings, followed by the statistical results supporting those findings. We have retained the relevant test statistics, degrees of freedom, exact p-values, and post hoc comparisons for the key analyses in the Results section, while the statistical procedures and analytical approaches are described in detail in the Methods section (see Materials and Methods). These revisions make the main biological findings more readily apparent while maintaining complete statistical reporting.

      (2) The authors report quantitative differences in pup retrieval latency and crouching behavior in virgin females between two Koi lines with distinct Oxtr expression patterns. However, it is unclear how these behavioral differences relate to prairie vole phenotypes. Specifically, do prairie vole virgin females differ from mice in pup retrieval latency or crouching duration, and if so, which of the Koi lines more closely resemble vole behavior? Direct behavioral comparisons with prairie voles would have helped address this question. This comparison is important given the stated motivation for these experiments - that Oxtr expression in certain brain regions resembles vole patterns (albeit across separate lines) and is postulated to underlie vole-typical social behaviors. As currently presented, the manuscript appears to pivot from testing vole-relevant behaviors to testing whether different Oxtr expression patterns in mice produce different maternal behaviors, without clearly establishing how these behaviors map onto vole-specific traits. If these phenotypes are known to differ between species, a brief discussion of the relevant literature would help contextualize the findings.

      Thank you for raising this important point. We agree that direct comparisons of parental behaviors between prairie voles and mice would be informative for determining whether the Koi phenotypes resemble species-specific vole traits. However, such a comparison was not the primary objective of our experiments.

      Our initial goal was to determine whether the prairie vole Oxtr locus and its surrounding regulatory elements could reproduce vole-like Oxtr expression patterns in mice. The distinct and partially overlapping expression configurations observed across independent Koi lines led us to a broader question: how does variation in Oxtr regulatory architecture generate diversity in expression patterns and, consequently, social behaviors? Accordingly, the pup retrieval and crouching assays were designed to test whether distinct pvOXTR expression configurations are associated with quantitative differences in parental behavior, rather than to determine which Koi line most closely resembles a prairie vole phenotype. We have made this point clearer in the revised manuscript (see Introduction).

      (3) The partner preference test is a well-established assay; however, a direct comparison of behavioral phenotypes obtained in this assay between prairie voles and the Koi lines would be an important control. Such a comparison would help establish whether the behavioral patterns observed in the Koi lines meaningfully approximate prairie vole partner preference under identical experimental conditions.

      Thank you for this important suggestion. We agree that a direct comparison with prairie voles under identical experimental conditions would be valuable for determining whether the behavioral phenotypes of the Koi lines quantitatively approximate prairie vole partner preference. However, the primary purpose of the PPT in this study was not to establish a prairie vole-like behavioral phenotype in a particular Koi line, but to determine whether distinct pvOXTR expression configurations are associated with differences in social preference within the same mouse genetic background.

      Importantly, we do not intend to claim that Koi-2 or Koi-4 represents a behavioral phenocopy of prairie voles. Rather, our aim was to test whether divergent OXTR regulatory and expression configurations can generate divergent social behaviors. The contrasting partner versus stranger preferences observed in Koi-2 and Koi-4 provide evidence consistent with this possibility. We have clarified this rationale in the revised manuscript (see Introduction).

      (4) A recent study reported that prairie voles lacking oxytocin receptors, generated via CRISPR-mediated deletion, nonetheless exhibit largely intact social attachment behaviors, including pair bonding, parental care, and successful nursing to weaning (Brendenzen et al., Neuron, 2023). How do the authors interpret their findings in light of this study (i.e., intact social behavior in Oxtr knockout voles)? One plausible explanation is that constitutive deletion during development, as shown in Brendenzen et al., may engage compensatory or redundant pathways that restore behavior, while differences in Oxtr expression nonetheless contribute to the social variation observed between prairie voles and mice. A brief discussion of this possibility would help situate the present results within the broader literature in the field.

      Thank you for raising this important point. We agree that the findings of Berendzen et al. are highly relevant to the interpretation of our results. The apparent discrepancy may reflect an important difference between constitutive loss of OXTR signaling and variation in the spatial distribution of OXTR expression. In the CRISPR-mediated Oxtr knockout voles, OXTR signaling is absent from development onward, yet these animals retain pair bonding and parental behaviors (Berendzen et al., 2023). One possibility is that the absence of OXTR signaling during development allows compensatory or redundant mechanisms to develop. Consistent with this interpretation, Larry Young proposed that the timing of OXTR loss may be critical, with neural circuits potentially becoming dependent on oxytocin signaling through developmental exposure to the hormone.

      Our Koi system provides a complementary approach. Rather than eliminating OXTR signaling, the Koi lines preserve pvOXTR expression while generating distinct spatial expression patterns within the same mouse genetic background. We found that these divergent pvOXTR expression patterns were associated with distinct social behavioral phenotypes across the Koi lines. The divergent social phenotypes observed across these lines suggest that variation in the spatial organization of OXTR expression, rather than simply the presence or absence of OXTR signaling, may contribute to behavioral diversity. Thus, the intact social behaviors of constitutive Oxtr knockout voles do not exclude a role for OXTR expression patterns in shaping behavioral variation. We have added a discussion of this possibility and of the findings of Brendenzen et al. (2023) to the revised manuscript (see Discussion).

      Editor's note:

      Should you choose to revise your manuscript, if you have not already done so, please include full statistical reporting including exact p-values wherever possible alongside the summary statistics (test statistic and df) and, where appropriate, 95% confidence intervals. These should be reported for all key questions and not only when the p-value is less than 0.05 in the main manuscript.

      Thank you for this guidance. We had reported the test statistics, degrees of freedom, and exact p-values for the statistical analyses in the original manuscript, including both significant and nonsignificant results. Nevertheless, we carefully reviewed the statistical reporting throughout the manuscript and revised the Results section to ensure that the relevant test statistics, degrees of freedom, and exact p-values are consistently reported alongside the corresponding findings. We also reorganized the descriptions of the behavioral results to present the main findings more clearly before the detailed statistical results, as suggested by Reviewer #2.

    1. Author response:

      The following is the authors’ response to the previous reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      The main goal of this manuscript is to develop a mathematical model of the regulation of cortical dynamics by Cdk1 activity to explain why, in some embryos (e.g., Xenopus), surface contraction waves are believed to move in the same direction as Cdk1, while in other embryos (e.g., starfish) they are believed to move in the opposite direction.

      Strengths:

      (1) The paper addresses a very important question.

      (2) The mathematical model is sensible and suggests that the different relationship between Cdk1 and surface contraction waves might arise from the different behavior of the mitotic entry wave and the mitotic exit wave.

      (3) The authors propose a mechanism by which the wave observed at mitotic exit might not passively follow the trigger wave observed at mitotic entry'

      (4) The proposed mechanism is a potential explanation of the observed differences.

      (5) The proposed mechanism is centered on different dynamics between the nucleus and the cytoplasm, highlighting the potential importance of the nucleus (and nuclear size) in organizing cortical dynamics.

      We thank the reviewer for this positive assessment. The revision now makes the central question and the scope of the contribution more explicit: the individual Cdk1 and cortical modules were already previously established, while the present study asks how their coupling, together with cell geometry and nuclear Cdk1 content, can generate distinct wave-back dynamics and cortical responses. The revised manuscript now also foregrounds the mechanistic distinction between activation fronts and wave backs and uses this distinction to organize the Results and Discussion sections. See Abstract, Introduction, Results and Discussion.

      Weaknesses:

      (1) The proposed mechanism works if the activity in the nucleus is much higher than the high activity (high state of the bistable system) of the cytoplasm. So, as the wave propagates across the cytoplasm, the activity around the nucleus remains higher, which potentially causes a delay in the onset of Cyclin B-Cdk1 degradation in the region around the nucleus compared to the surrounding cytoplasm. This effect happens over a typical length scale, and if such a length scale is comparable to embryo size, this becomes the predominant mechanism. However, such a mechanism should exist near the nucleus independently of embryo size. So, it seems that for embryos where the wave back and wave front should travel together, nuclear activity must be adjusted not to be much higher than cytoplasmic activity. A better discussion of the discovered process and its implications would strengthen the paper. It requires careful reading to understand what, in hindsight, is a rather simple explanation. Is there any experimental evidence that the overall activity of Cdk1 is higher in the nucleus than in the cytoplasm?

      We agree that the mechanism needed a more intuitive explanation. The revised Results now separate two simultaneous processes. The activation front propagates outward with an approximately constant trigger-wave-like velocity, whereas excess active Cyclin B–Cdk1 associated with the enriched nuclear pool also spreads diffusively. This diffusive component exists locally around the nucleus irrespective of cell size. What depends on effective system size is whether that diffusive length scale is large enough, relative to the cell, to shape the wave back over a substantial fraction of the domain and ultimately at the cortex. This is why nuclear content and effective system size act together. The revised Fig. 2B and the accompanying text now explain this competition explicitly.

      To further address the reviewer's question regarding experimental evidence for elevated nuclear Cdk1 activity, we have additionally expanded the Discussion with evidence from live-cell studies demonstrating rapid, positive feedback-driven nuclear accumulation of Cyclin B–Cdk1 shortly before nuclear envelope breakdown (Gavet and Pines, 2010; Santos et al., 2012). In particular, Gavet and Pines (2010) reported an approximately 40-fold increase in the nuclear import rate of Cyclin B–Cdk1, providing mechanistic support for rapid nuclear enrichment. This complements the previously discussed observations that active Cyclin B–Cdk1 accumulates in nuclei before activation of the surrounding cytoplasm in frog egg extracts, that nuclei can specify where mitotic waves begin, and that Cyclin B enrichment near the nuclear region occurs in starfish oocytes. Together, these findings provide substantial experimental support for the biological plausibility of nuclear Cyclin B–Cdk1 enrichment. Nevertheless, the precise nuclear-to-cytoplasmic difference in active Cyclin B–Cdk1 concentration required for complete wave-back reversal remains to be quantified experimentally, as we now explicitly acknowledge in the revised Discussion. See Results, especially Fig. 2B and caption; Discussion (updated paragraph on nuclear Cyclin B–Cdk1 enrichment); Methods and Eq. 7.

      (2) While the fact that Cdk1 can enslave cortical dynamics is clearly shown in the model, this is expected from the literature. There are systems where the enslavement of cortical and bulk actomyosin contractility to Cdk1 activity has been more clearly demonstrated (Drosophila and zebrafish embryos), as well as shown to have clear functions (nuclear positioning and ooplasmic segregation).

      We agree. The revised manuscript no longer presents Cdk1 control of cortical dynamics as a novel result. We expanded the introduction to discuss Drosophila and zebrafish and to note the established functions of Cdk1– actomyosin coupling in nuclear positioning and ooplasmic segregation. We now frame the contribution of the present work as explaining how established Cdk1-to-cortex coupling can transmit geometry-dependent cytoplasmic waveforms into different cortical directionality and reactivation regimes. See Introduction and Discussion.

      (3) The writing could be improved. The authors make some claims of originality that seem a stretch, e.g., in the abstract, they say: "we develop a reaction-diffusion model of Cyclin B-Cdk1 signaling in spherical cells with localized nuclear activation", but they essentially use a previous model with a few numerical tweaks. The figures are sometimes mislabelled or not explained, and some of the units seem wrong.

      We agree and revised the framing throughout. The Abstract now states that we “couple established reaction– diffusion models of Cyclin B–Cdk1 signaling and the excitable Rho–actin cortex.” The Introduction similarly states that we are not developing a new model, and a dedicated Model section now gives the equations, assumptions, coupling, and original sources of the two modules. We also revised figure labels and captions, added schematic panels, corrected the diffusion units to μm<sup>2</sub>/s, corrected the conversion used for total active nuclear Cyclin B–Cdk1, and regenerated the affected plots. The control variable is now defined explicitly as total active nuclear content in Eq. 7 and reported in pmol. See Abstract, Introduction, Model, Fig. 1 and caption; Fig. 2 and caption; Methods, especially Eq. 7 and Table 1.

      (4) The authors give the existence of trigger waves as a fact. While the predominant view is that such waves exist in the first cycle of the Xenopus embryos (however, this is from measurement of the cortical contractions, so a bit circular for this paper), it is unclear if waves exist in the starfish embryo, so the potential explanation that the starfish embryo simply has different Cdk1 dynamics cannot be ruled out.

      We agree that the evidence is not equivalent across systems. The revised manuscript avoids treating a starfish intracellular Cdk1 trigger wave as an experimentally established fact and instead presents the cross-species comparison as an interpretation within the model framework. We distinguish the model prediction from the available experimental observations and explicitly state that the nuclear active Cyclin B–Cdk1 level required for complete wave-back reversal remains to be tested. Thus, different underlying Cdk1 dynamics in starfish are not excluded by our study. See Introduction, Results and Discussion.

      Reviewer #2 (Public review):

      Summary:

      Large oocytes show prominent waves of cortical contractions. Previous works combining experiments and computational modeling have shown that the waves are driven by gradients of CDK1 kinase activity that trigger excitable Rho activity patterns on the cortex. This present work combines two previously published mathematical models for CDK1 activation and Rho activation, respectively. They show that the models combined can explain diverse shapes of cortical contractions observed in different species and at various stages of development. This shows how the same molecular machinery can generate diverse patterns dependent on the size of the system and the size and position of the cell nucleus.

      Strengths:

      (1) Carefully done modeling work providing a simple and elegant explanation for a complex cellular behavior.

      (2) Very nicely illustrated, simulations can be directly compared to previous experimental observations.

      (3) Explains observations made in different model systems, providing a unifying model.

      We thank the reviewer for this assessment. We have revised the manuscript so that this scope is explicit from the outset: the model modules are established, while the contribution is the analysis of their coupling and the identification of geometry, total nuclear Cdk1 content, and cortical recovery kinetics as controls that generate qualitatively different behavior within one framework. Abstract, Introduction, Results and Discussion.

      Overall, I find this work important, as it shows that combining models of the CDK1 gradient and Rho activation modules can explain the surface contraction waves observed in oocytes. Strikingly, it elegantly explains the differences seen between different experimental systems. While previously these were considered a 'controversy', modeling shows that the differences are simply a consequence of the difference in the size of the oocytes. In addition, the model makes several intriguing predictions that can be tested in future experiments.

      We thank the reviewer. In revising the manuscript, we were careful not to reduce the mechanism to cell size alone: the model shows that directionality depends jointly on effective cell size and total nuclear Cdk1 content, which is set by nuclear size and nuclear concentration. We now mention this combination consistently and make the associated predictions explicit in the Discussion. See Results and Discussion

      Reviewer #3 (Public review):

      Summary:

      Using realistic mathematical models, Cebrián-Lacasa et al. address the relationship between waves of activation of Cyclin B-Cdk1 that propagate through the cytoplasm of large (~1 mm) oocytes and fertilized eggs and surface contraction waves (SCWs) driven by Rho GTPase activity in the cell cortex. They present numerical simulations of the underlying reaction-diffusion equations that account in broad strokes for both the expected behavior of 'fronts' of Cdk1 activation (that propagate at constant velocity from the nucleus-the source of Cdk1 activity-to the cell cortex) and the unusual behavior of 'backs' of Cdk1 inactivation (that may propagate either away from or towards the nucleus, or exhibit simultaneous inactivation throughout the cytoplasm). They also model Rho GTPase activity in the cortex as an excitable system that propagates SCWs (target patterns, spiral waves, and more complicated patterns). When Cdk1 is activated in the cortex, it phosphorylates and inhibits the RhoGEF, Ect1, which suppresses SCWs by reducing Rho GTPase activity. As the wave-back of Cdk1 inactivation moves across the cortex, Rho GTPase activity recovers abruptly, and SCWs reappear as 'phase waves' whose speed and directionality are determined by the underlying cytoplasmic Cdk1 signal.

      Strengths:

      As a theoretical examination of an interesting and puzzling aspect of early embryonic development, this study shares the same strengths and weaknesses as all mathematical and computational approaches to molecular cell biology. The mathematical models are precise formulations of the underlying assumptions of the authors (which are quite reasonable in this reviewer's opinion), and the analysis and computational results are dependable consequences of the molecular mechanisms the authors have in mind. The model is expertly analyzed, and the results are both reliable and intriguing. The results are discussed in light of experimental evidence. Because the authors' methods and results suggest novel-and sometimes counterintuitive-avenues for experimental research, this paper is likely to have a significant impact on the field of Rho GTPase signaling in oocytes and early embryos, and perhaps in other cells as well.

      We thank the reviewer for this thoughtful assessment. We have preserved the mathematical formulations and made the assumptions, mechanisms, and experimentally testable consequences easier to identify. In particular, the revised Results section emphasizes the distinct mechanisms governing the activation front and wave back, the revised figures provide a more intuitive visual explanation, and the Discussion separates experimentally supported observations from model predictions. See Model, Results and Discussion.

      Weaknesses:

      Like all mathematical models, the underlying assumptions can be critiqued as neglecting this -or-that 'crucial' effect (e.g., mechanical coupling via cortical tension or cytoplasmic flow, as the authors acknowledge), and the highly technical methods of analysis and simulation can be unfamiliar and off-putting to experimental cell biologists. The paper is a difficult read, even for an experienced theoretician. For those who take the time to understand this paper, it may change the way they think about the coupling of cell cycle control (Cdk1 activation and inactivation) and cell surface contraction waves.

      We agree on both accessibility and model scope. To improve accessibility, we added the core equations and parameters to the main text, introduced more qualitative descriptions of the dynamical regimes, and redesigned Fig. 2B to show the physical mechanism schematically. We also expanded the discussion of the limitations. We did not add mechanical coupling to the model in this revision; instead, the manuscript now states explicitly that showing biochemical signaling to be sufficient within the model does not demonstrate that cortical tension, cytoplasmic flow, or surface deformation are unnecessary in living cells. These effects are identified as additional important factors that can affect the dynamics and as targets for future perturbation experiments. See Model, Results, Fig. 2B and caption; Discussion and reference list.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      This manuscript by Laura Korobkova and Brian Dias describes an interesting study of the role of GABAergic neurons in the zona incerta (ZI) in incentive motivation for reward.

      The authors report that DREADD inhibition of ZI neurons reduced the effort breakpoint in a progressive ratio task, which measures the intensity of incentive motivation to obtain food rewards. In other tests, chemogenetic inhibition did not alter food consumption or memory.

      Conversely, DREADD excitation of ZI neurons increased incentive motivation in the progressive ratio task, expressed as a higher breakpoint for food rewards.

      Korobkova and Dias report that prior stress exposure to a series of stressors (e.g., forced swim & water submersion, restraint, mild foot shock) by itself reduced the breakpoint for food reward under vehicle, though it did not impair the ability to learn an instrumental response. However, DREADD excitation of ZI neurons in previously stressed mice increased the breakpoint to normal levels equivalent to the never-stressed group. This important finding indicates the ability of ZI stimulation to rescue the incentive motivational deficit induced by prior stress.

      In fiber photometry studies using vGAT-CRE mice to specifically identify GABA neurons, Korobkova and Dias report that ZI GABA neurons are excited by sensory signals, including neutral cues. However, after reward conditioning, ZI GABA neurons increase their activation to the CS+ cue that predicts reward, but not to the CS- cue that doesn't. ZI neurons also respond in an instrumental reward task during both lever press and reward delivery. The authors conclude that ZI neurons respond to sensory stimuli, but specifically code the motivational significance of reward-related stimuli.

      In optogenetic studies, the authors find that ZI GABA neuron stimulation during a reward CS+ enhances motivated responding to obtain reward, particularly in females, but not stimulation outside the CS+. This suggests the ZI stimulation in females may specifically enhance the incentive salience of the CS+, namely the cue's ability to trigger an increase in 'wanting' for the reward. However, that effect was not found here in males.

      Altogether, this is a fine contribution to the literature, and the authors deserve congratulations on their study and manuscript.

      Strengths:

      This is a powerful and creative set of studies that clarifies the roles of ZI neurons in sensory processing and especially in incentive motivation for rewards. The use of multiple methods and test situations to triangulate on reward motivation functions gives a well-rounded perspective on ZI function. The discovery of incentive motivation roles for ZI neurons is intriguing and improves understanding of ZI, which traditionally has been a relatively understudied brain structure. The finding that ZI stimulation may rescue stress-induced deficits in motivation is especially notable and may have therapeutic implications.

      Weaknesses:

      Minor: This version of the manuscript focuses the introduction and discussion specifically on ZI GABA neurons. The ZI may be primarily GABAergic, but also contains other neurons, and DREADD studies may have used the hSyn promoter, which would impact all types of ZI neurons. Other studies here did more specifically target GABA neurons using vGAT Cre mice and specific targeting. The manuscript might be slightly improved by distinguishing in the discussion a bit more clearly which effects implicate GABA neurons specifically, and which effects might include other neurons too, to more clearly parse out the relative roles of GABA vs broader neuronal populations in ZI.

      The current version of our manuscript notes “Our chemogenetic manipulations targeted all GABAergic ZI neurons, and emerging evidence suggests molecular heterogeneity within this population that may map onto distinct functional roles (Arena et al., 2024; Wilt et al., 2025). Future work to first profile the molecular heterogeneity of GABAergic cells in the ZI and then using intersectional strategies to target defined ZI sub-populations will be essential to providing a more nuanced view of ZI GABAergic influences on motivation.” Our revision will make sure to discuss newer literature demonstrating cellular heterogeneity of ZI and emphasize that this heterogeneity will provide more nuanced contributions of ZI cells beyond the studied GABAergic population on motivation.

      “Every manipulation and recording in this study used Cre-dependent constructs in vGAT-IRES-CRE mice, so all of the effects we report are attributable to vGAT-expressing GABAergic ZI neurons rather than to the ZI as a whole. Conversely, our data speak only indirectly to the non-GABAergic ZI populations, including the glutamatergic (vGluT2-expressing) neurons and the dopaminergic A13 cells. This caveat is not hypothetical: ZI dopaminergic neurons have been shown to encode motivational vigour during food seeking and to modulate feeding-related behaviour (Ye et al., 2023) so the ZI plausibly influences motivated behavior through more than one cell type, and our design isolates only the GABAergic contribution.

      Our chemogenetic and optogenetic manipulations targeted GABAergic ZI neurons as a single population, yet recent work makes clear that this population is molecularly, spatially and functionally fractionated. Emerging evidence suggests molecular heterogeneity within this population that may map onto distinct functional roles (Arena et al., 2024; Wilt et al., 2025). Using single-nucleus transcriptomics together with in situ hybridization, slice electrophysiology and viral circuit mapping,(Kast et al., 2026) resolved four genetically distinct GABAergic ZI populations that differ in spatial position, intrinsic physiology and efferent target. Convergent evidence from transcriptomic profiling of the rostral and medial ZI identified two further non-overlapping subtypes with dissociable functions: Ecel1-expressing rostral ZI neurons projecting to periaqueductal grey that drive self-grooming, and Pde11a-expressing medial ZI neurons projecting to the oral pontine reticular formation that promote sleep-to-wake transitions (Zhu et al., 2025) . Functional studies converge on the same conclusion. Activation of medial ZI GAD2 neurons drives novelty investigation and arousal (Ahmadlou et al., 2021), a defined ZI→SST population integrates multimodal dam-associated cues in pre-weaning pups (Li et al., 2024), and ZI GABAergic manipulations have been implicated in hunting (Zhao et al., 2019) and in fear discrimination (Venkataraman et al., 2019). This repertoire of behavior is unlikely to be supported by one homogeneous cell class.

      This molecular heterogeneity has direct bearing on the interpretation of our results. Our manipulation of GABAergic cells almost certainly spanned more than one of the transcriptomic subtypes described above and were distributed across the dorsoventral gradient along which those subtypes vary (Fig. S14); our effects are therefore best read as the consequence of shifting aggregate GABAergic tone in the ZI rather than as the signature of any one subtype. The motivational effects we report cannot yet be assigned to a specific efferent pathway, and it remains possible that different components of our findings are carried by different molecular subtypes of GABAergic cells in the ZI. The same inhibition that lowered progressive ratio breakpoints left cue-selective conditioned responding intact (Fig. 1D, Fig. 5C), and cue-locked but not temporally random activation enhanced effort (Fig. 6D). Such a pattern could be expected if distinct GABAergic ensembles carry tonic motivational gain and phasic cue-related signals. Resolving this will require intersectional strategies that manipulate and record from the now-defined ZI subtypes, together with projection-specific approaches. We expect such investigations to yield a considerably more nuanced account of ZI contributions to motivation than the population-level one we offer in our study. Identifying the specific downstream targets through which the ZI exerts its motivational effects will be critical for building a complete circuit model of ZI -associated motivational drive.”

      Reviewer #2 (Public review):

      Summary:

      This paper describes a study that uses a combination of observational and experimental techniques to investigate the hypothesis that the zona incerta is a neural loci where sensory information is integrated to interpret the motivational value of reward-associated cues. They show that manipulation of GABAergic neurons in this region bidirectionally modulates responding during a progressive ratio test, that activating these neurons recovers motivational deficits incurred by chronic stress, and that they fire in response to reward-associated visual or auditory cues. They also showed that activity in these neurons is not necessary for incentive salience of reward-associated cues, because inactivating them did not prevent Pavlovian-instrumental transfer. However, activating them did enhance responding during the presentation of reward-associated cues in females but not in males.

      Strengths:

      The study has a very systematic and elegant approach to assess how this region responds first to intrinsic motivation and then to motivation-enhancing effects of reward-associated cues.

      Weaknesses:

      Males and females are used throughout, but sample sizes are generally too small to make a meaningful interpretation of sex differences (which is not the focus of the study, but is worth bearing in mind). In the last experiment, the lack of discrimination between CS+ and CS- conditions across training for males confounds any interpretation of sex differences in the outcomes.

      The goal of our study was not to determine sex differences in motivation mediated by the ZI but rather demonstrate a general role of GABAergic cells in the ZI on motivation. As such, while all our experiments used male and female mice and our statistical analyses did not uncover any sex differences in most experiments, our sample sizes of each sex are too small to definitively make any statements about sex differences. As noted already in our Discussion, the sex-specific cue-utilization behavioral strategy in our optogenetic experiment warrants further investigation as a contributing factor to motivation that may or may not be influenced by GABAergic cells in the ZI. It bears mentioning that, to our knowledge, none of the recently published literature on the role of the zona incerta in learning, memory and appetitive behavior that is cited in this manuscript (including our own prior work) has uncovered sex differences in the contributions of the zona incerta to these behaviors.

      Sex was included as a variable in every experiment and in every statistical model, but the present study was neither designed nor powered to test sex differences, and this constrains how our one sex-divergent result should be read. Statistical models detected no main effect of sex and no sex interaction in the chemogenetic, stress-rescue, photometry or Pavlovian probe experiments, and we accordingly pooled across sexes for visualization where sex was non-contributory. It bears mentioning that, to our knowledge, the existing literature on ZI contributions to learning, memory and appetitive behavior has not reported sex differences in these functions.

      The ZI is known to be a region where there is notable convergence of neural inputs from a diverse and heterogenous range of sensory and other cortical inputs. To my knowledge, this is the first study that has directly tested whether it may serve to encode motivational/incentive properties of reward-associated cues. The outcomes are not definitive - it appears that they are sufficient but not necessary. However, this study represents an important first step - the ZI also has notable heterogeneity in the genetic identity of neurons, and properly dissecting the function of ZI microcircuits will likely require characterising function based on more than one molecular marker. This is addressed by the authors in the discussion.

      In summary, this study will have a significant impact on our understanding of how motivation is calculated based on complex environmental signals.

      Reviewer #3 (Public review):

      Summary:

      The authors investigated the role of the zona incerta in motivation and cue-reward associations. Using chemogenetic and optogenetic manipulations of the ZI, they altered motivation in cued and uncued variants of the progressive ratio task and rescued deficits in motivation induced by chronic stress. They further use fiber photometry to demonstrate that the ZI tracks the formation of cue-reward associations.

      Strengths:

      (1) The authors fill an important gap in the literature linking sensory input to motivation via the zona incerta.

      (2) The authors demonstrate that ZI tracks cue value rather than just tracking sensory input.

      (3) The authors demonstrate that the ZI excitation rescues stress-induced suppression of motivation.

      (4) The authors perform several important control tasks, demonstrating that their findings are not a result of alterations in locomotor activity, food consumption, or memory.

      Weaknesses:

      In Figure 1D and E (inhibitory vs excitatory DREADDS), the control groups in the Gi group appear to have more elevated breakpoints than the control groups in the Gq group, although a statistical comparison between the two is not reported. It is not clear if this is because the two groups were given a different reinforcement schedule, this should be made clearer.

      In our revision, we will be sure to insert language re-emphasizing that the Gi and Gq experiments were performed using different reinforcement schedules, FR3 and FR1, respectively.

      “The inhibitory and excitatory cohorts were run as two independent experiments and were trained on different fixed-ratio schedules prior to progressive ratio testing: mice in the hM4DGi cohort were trained on an FR3 schedule, whereas mice in the hM3DGq cohort were trained on an FR1 schedule. Because prior fixed-ratio training history shifts the absolute level of responding on a subsequent progressive ratio schedule, baseline breakpoints are not directly comparable across the two cohorts, and the GFP controls of the hM4DGi experiment accordingly show higher absolute breakpoints than those of the hM3DGq experiment. We therefore make no statistical comparison between the two experiments; all inferences are drawn within experiment, from the within-subject vehicle-versus-CNO contrast and from the comparison against the concurrently run GFP controls of the same cohort.

      In Figure 1E, it is important to note that although the authors found a significant planned comparison between Gq VEH and Gq CNO, the interaction was not significant, nor were comparisons to mice injected with control virus. Thus, activation of ZI GABA neurons appears to be a relatively weak effect.”

      In our revision, we will insert language to acknowledge that reducing motivation after inhibiting GABAergic ZI cell activity is stronger than increasing motivation seen after stimulating the activity of these cells.

      “Together, these results demonstrate that activity of GABAergic cells in the ZI bidirectionally and causally modulates motivational effort, though the two directions are not equally strong. Inhibition produced a significant treatment × group interaction and a CNO-induced reduction in breakpoint that was significant both against the animals' own vehicle sessions and against CNO-treated GFP controls. Activation produced a significant main effect of treatment and a significant within-subject vehicle-versus-CNO increase, but CNO-treated hM3DGq mice did not differ significantly from CNO-treated GFP controls. The enhancement of motivation by activating GABAergic ZI neurons in well-trained animals is therefore a weaker and less specific effect than the suppression produced by inhibiting them.

      This bidirectional control is asymmetric in magnitude. Removing GABAergic ZI output reliably and substantially reduced effort, whereas augmenting it in unstressed, well-trained animals produced a smaller increase that was significant within subjects but did not survive comparison against CNO-treated controls. Motivated responding in food-restricted animals working under a familiar PR schedule may already be near a behavioral ceiling, leaving little dynamic range for a further increase. Consistent with this, activation was markedly more effective where baseline drive had been lowered: in chronically stressed animals, whose breakpoints were significantly depressed, hM3DGq activation produced a large and specific restoration of effort (Fig. 2E). We therefore interpret ZI GABAergic output as setting a gain on motivational drive whose behavioral consequences are most visible when that drive is reduced, either by direct silencing or by chronic stress, and we are careful not to claim symmetric bidirectional control of equivalent effect size.”

      In Figure 5, the authors see what is likely a significant difference in lever presses during acclimation between the Gi and GFP groups, which they state is an expected difference. However, it is difficult to see why this would be expected. While Gi:CNO manipulation yielded lower breakpoints in Figure 1D, it did not yield lower FR1 responding for food in Fig S3 (although this was FR1 for food dispenser visits rather than lever press). One reason I ask is that the authors highlight the differences in CS+/CS- between groups, but the biggest difference between groups appears to be in acclimation, which may be driving the group x block interaction.

      In a revision, we will revise the language to state that the acclimation difference that is more pronounced in the GFP control group vs the Gi group is to be expected because we had already shown that inhibition of GABAergic cells in the ZI would reduce lever pressing. We will also report a planned comparison of CS+ versus CS− responding that omits the acclimation block, which shows discrimination between sound (CS+) and light (CS−) in the Gi group but not in the GFP group, confirming that the cue effect is not driven by the acclimation difference. We will also note that acclimation responding is non-reinforced and effortful, whereas FR1 dispenser visits (Fig. S3) are reinforced and low-effort, which is why the two measures dissociate.

      “Post-hoc comparisons (paired Wilcoxon signed-rank tests, averaged across presentations) showed that GFP controls decreased pressing relative to acclimation during both CS+ (V = 4, p = 0.011) and CS− blocks (V = 3, p = 0.009), with no difference between cues (V = 33.5, p = 0.57) (Fig. 5C). In contrast, Gi mice selectively increased pressing during CS+ blocks (CS+ vs acclimation: V = 106.5, p = 0.009; CS− vs acclimation: V = 48, p = 0.50) and pressed more during CS+ than CS− blocks (V = 112.5, p = 0.003). When the acclimation period was excluded from the model, the block × group interaction was no longer significant (F(3,75)=1.24, p=0.3; nor was the cue x group interaction when the wro presentations of each cue were modelled as repeated measures within animal (F(1,27) = 2.39, p = 0.13). Importantly, however, acclimation pressing did not moderate CS+/CS− discrimination (cue × acclimation, F(1, 26) = 0.01, p = 0.93), and within the Gi group the CS+ > CS− difference remained significant when acclimation rate was included as a covariate (F(1, 16) = 10.1, p = 0.006). A model of cue-block pressing including block position and cue identity as fixed effects confirmed that GFP responding declined progressively across the session (β = −1.9 presses per block, p = 0.040), with no effect of cue identity (p = 0.96), indicating a cue-independent decline (Fig. 5C). In Gi mice, we observed the opposite effect: no within-session decline (p = 0.43), but a significant increase in pressing during CS+ blocks (β = 5.2 presses, p = 0.004). Thus, discrimination in Gi mice was driven by cue identity, and was attributable neither to their low baseline nor to time in session.”

      In Figure 6, the authors demonstrate that optogenetic stimulation during cue light increases the breakpoint in females, but not in males. They suggest that this may be because the males did not sufficiently discriminate the cue light before optogenetic manipulation began. If this were the case, then the authors would need to use "cue discrimination" as a factor to determine if it is a better predictor than sex.

      In a revision, we will add an analysis that includes cue discrimination as a factor, to test whether it is a better predictor of the optogenetic effect on breakpoint than sex.

      “We also tested cue discrimination directly as a predictor of the optogenetic effect. We computed a per-animal discrimination index, DI = (rate cue-on – rate cue-off)/(rate cue-on + rate cue-off), from the final three training days, and quantified the effect as log(presses under cue-locked stimulation / mean presses under the no-stimulation and random-stimulation conditions). Across the full cohort, DI predicted the optogenetic effect (Spearman ρ = 0.74, p = 0.006, n = 13; regression β = 1.70, 95% CI [0.49, 2.91], p = 0.010). Because DI covaried with sex, we also examined each sex separately (Fig. S12). In females, DI tracked the magnitude of the effect closely (ρ = 0.96, p = 0.003, n = 7; ρ = 0.94, p = 0.017 after excluding the most influential animal), indicating that discrimination carries information about the optogenetic effect beyond sex alone. In males, no association was detectable (ρ = −0.37, p = 0.50, n = 6), although their DI values spanned roughly half the range observed in females (0.01–0.50 vs 0.03–0.90), so a relationship over a wider range cannot be excluded. The DI × sex interaction was not significant (F(1,9) = 2.84, p = 0.126), so we do not claim that the relationship differs formally between sexes Males pressed more during cue-on periods (final 3 days, V = 21, p = 0.031), but maintained substantially higher cue-off responding than females (W = 6, p = 0.035), yielding a lower discrimination index. Because DI was itself lower in males (W = 36, p = 0.035), DI and sex were collinear and explained essentially identical variance (R<sup>2</sup> = 0.464 for each; AIC 27.83 for each). In the repeated-measures model across all stimulation conditions, the stim × sex interaction remained better supported than stim × DI (F(2,26) = 5.28, p = 0.012, AIC = 510.8 vs F(2,26) = 1.71, p = 0.20, AIC = 520.3).”

      “To test whether cue discrimination or sex better predicted the optogenetic effect, a cue-discrimination index (DI) was computed for each mouse from the last 3 days of contingent FR1 training as (presses/min during light-on, lever-active periods − presses/min during light-off, lever-inactive periods) / (the sum of the two). The optogenetic effect was expressed as the log ratio of lever presses under [cue-locked] light stimulation to the mean of the no-stimulation and random-stimulation sessions, normalizing for individual differences in baseline responding. This effect was modelled by linear regression on DI alone, sex alone, and DI and sex together, and the models were compared using AIC and R<sup>2</sup>. The association between DI and the optogenetic effect was additionally assessed with Spearman rank correlations, pooled and within each sex, and a DI × sex interaction term was tested to determine whether the relationship differed between sexes.”

      The authors' work demonstrates that chemogenetic inhibition of GABAergic ZI cells reduces uncued motivation for reward but enhances cued responses under extinction. The authors state that this is a paradoxical finding that suggests that the ZI operates within a redundant motivation network. However, a critical difference between the two tasks is that one measures motivation for food while the other measures persistent responding under food extinction, which are not the same process. Thus, a simpler explanation is that ZI inhibition reduces motivation and impairs extinction.

      Our revision will include discussion of this important point and tie it into our previous work (Venkataraman et al. 2019 and 2021 – cited in this version) that included extinction-like protocols, albeit in classical (not operant) conditioning protocols.

      It is important to be explicit that the PR test and probe test do not measure the same thing. The progressive ratio test measures the effort an animal will expend for reward that is actually delivered, whereas the probe test measures responding that is maintained, and normally extinguished, in the absence of reinforcement. Cue-selective responding of the Gi group reflects the residual behaviour still under the control of the pre-established CS+ association. It is consistent with the involvement of the ZI in the updating and suppression of learned associations in other behavioural domains (Venkataraman et al., 2019, 2021).

      Reviewing Editor Comments:

      There are a number of places where the methods and the rationale behind the methodological design should be further described and clarified. This would help address some of the reviewers' question.

      Reviewer #2 (Recommendations for the authors):

      I only have a few minor suggestions:

      (1) The graphs in Figure 1 (D and E) use open circles/stripes to distinguish between control and HM3/4. The open circles look like data points. I suggest using a different format.

      Figure 1 has been modified to address this point.

      (2) It would be good to have figures that show viral spread and location of ALL injection sites/fibre placements - not just a single representative slice. This is important because the molecular identity and function of ZI neurons change systematically across ZI topography.

      We added new Fig. S13 and new Fig. S14 in the revised manuscript.

      (3) The analysis of the photometry signal (e.g., waveform analysis) would strengthen the interpretations of experiments reported in Figure 3.

      To determine whether GABAergic ZI neurons respond differently to sensory cues, we compared the waveform of peri-event calcium transients evoked by lever press, an auditory cue and a visual cue (Fig. S5) All three event types were analysed on an identical peri-event window (−0.5 to +1.0 s relative to event onset) so that latency and kinetic measures were directly comparable, and decay was quantified over a fixed 0.4 s interval following the peak, Responses differed in magnitude across event types (Kruskal–Wallis, H = 14.59, p = 0.0007): auditory-evoked transients were approximately twice as large as those evoked by lever press (median 1.36 vs 0.74 z, Mann–Whitney U = 0, p = 0.0002) or by the visual cue (1.36 vs 0.68 z, U = 52, p = 0.0016), whereas press- and light-evoked transients were of comparable amplitude (U = 29, p = 0.29). Latency to peak also differed across event types (H = 6.75, p = 0.034), but the difference was carried entirely by the visual cue. Decay was steepest for auditory-evoked transients (H = 7.71, p = 0.021; sound −1.62 z/s vs press −0.53 z/s, U = 54, p = 0.016; vs light −1.05 z/s, U = 8, p = 0.026). When decay was expressed as the fraction of the peak remaining after 0.4 s, an amplitude-independent measure, no difference across event types was detected (H = 0.45, p = 0.80), indicating that the steeper absolute decay of auditory responses reflects their larger amplitude rather than faster kinetics.

      Reviewer #3 (Recommendations for the authors):

      (1) Figures 1D, E: Having the CNO group have circles to denote their groups is very confusing since it looks like the individual data points.

      Figure 1 has been modified to address this point.

      (2) Figures S1-S3: It would be nice to have individual data points in these figures.

      Individual data points have been added to Figures S1-S3.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      The study by He and colleagues aims to investigate the molecular mechanisms driving key cell potency transitions, particularly the naïve-to-primed pluripotency transition. The authors explore the relationship between cell polarity and stemness using stem cell models combined with a comprehensive panel of experiments, including pharmacological inhibition and co-culture/conditioned medium rescue approaches. Overall, the study provides interesting observations and contributes to the understanding of the molecular mechanisms dynamically regulating stem cell differentiation.

      However, several conceptual and interpretational aspects could be strengthened:

      (1) First, the Introduction would benefit from being more focused on what is currently known regarding cell polarity during early embryogenesis and pluripotent stem cell transitions, rather than emphasizing later neurogenesis events. Such reorientation would better match the main topic of the manuscript and improve the conceptual coherence of the study.

      We thank the reviewer for this constructive suggestion. We fully agree that the Introduction should be more tightly focused on the current understanding of cell polarity during early embryogenesis and pluripotent stem cell transitions, rather than on later neurogenesis events.

      Accordingly, we have revised the Introduction in the following ways:

      (1) Deleted the part on later neurogenesis and move some of those details to the Discussion section where they more appropriate.

      (2) Expanded the background on early embryonic development and pluripotent stem cell transitions by citing key recent and classical references, including but not limited to: cell polarity establishment in the preimplantation embryo, apical–basal polarity during lineage specification, polarity remodeling in naïve-to-primed pluripotent stem cell transition, and the role of PAR complex in early mouse development.

      (3) Refocused the Introduction to clearly state what is known about polarity in early embryogenesis and pluripotent states, what remains unknown, and how our study addresses that gap.

      (2) Similarly, Figure 6, where the authors attempt to provide clinical relevance through neural organoid formation experiments, feels somewhat disconnected from the central theme of the naïve-to-primed transition. Although this section is interesting on its own, there is already extensive literature describing polarization and morphogenetic events occurring much earlier during pluripotent state transitions. Therefore, the developmental relevance of the neural differentiation phenotypes could be better contextualized in relation to earlier morphogenetic events associated with pluripotency progression.

      We thank the reviewer for this insightful comment. We agree that the neural organoid experiments in Figure 6 are somewhat disconnected from the central theme of the naïve-to-primed transition, and that extensive literature already exists on polarization events occurring earlier during pluripotent state transitions.

      During early embryonic development, the transition from naïve ICM to primed epiblast is accompanied by the establishment of apical-basal polarity(Brons et al., 2007), which is required for apical domain changes that drive neural plate folding and neural tube closure(Matsuda et al., 2023). During neural organoid induction in vitro, naïve ESCs transition to an epiblast-like state that lies between the naïve and primed states(Park et al., 2022), further indicating that neural organoid induction is closely related to NPT. The abnormal morphology of ParKO cells during NPT suggests that this transition to the epiblast-like state is impaired. In the revised manuscript, we have provided a clear statement on this point. In addition, we also have contextualized these findings by explicitly discussing how the differentiation phenotypes especially neural differentiation phenotypes relate to the earlier morphogenetic events associated with pluripotency progression in Discussion, rather than presenting Figure 6 as a standalone observation.

      (3) The manuscript contains a substantial amount of experimental work; however, several results would benefit from deeper discussion. For example, in Figure 1, what is the rationale behind ZO1 downregulation being observed specifically in primed PAR knockout cells but not under naïve culture conditions? In addition, in Figure 3, the authors perform co-culture and conditioned medium experiments between wild-type and knockout cells. While the authors focus on the secreted protein fraction that rescues the phenotype, they also mention that other fractions display rescuing activity. Could the authors briefly discuss what additional components may contribute to this rescue effect? For example, could other molecules within these fractions also converge on AKT signaling regulation?

      We thank the reviewer for recognizing the substantial experimental work in our manuscript and for providing these thoughtful suggestions to improve the depth of our discussion. We agree that deeper discussion of several key results will strengthen the manuscript. In the revised version, we have addressed these points as follows:

      (1) Regarding ZO1 expression in Figure 1:

      Our primary focus is actually on ZO1 localization rather than its total expression level. In our experiments, RNA-seq and immunofluorescence analysis revealed that the total expression level of ZO1 does not change significantly in PAR knockout cells. However, ZO1 localization is markedly altered in PAR knockout primed cells. Specifically, in wild-type primed cells, ZO1 is predominantly localized at the cell membrane, whereas this specific membrane accumulation is not observed in PAR knockout primed cells. Furthermore, this phenomenon is observed specifically under primed state and does not occur under naïve culture conditions. This is likely due to the differential requirement for PAR complex components in maintaining tight junction integrity at distinct pluripotency stages.

      (2) Regarding the rescue activity of other fractions in Figure 3:

      In our experiments, we found that beyond the >100 kDa fraction, the 50-100kD fraction and exosome fraction exhibited limited rescue efficacy. The soluble fractions were separated with ultrafiltration tubes, we cannot exclude the possibility that the 50–100 kDa and >100 kDa fractions were not completely separated, and that some overlap may exist. This could contribute to the weaker and delayed rescue activity of 50–100 kDa fraction. The components of exosomes are complex vesicles containing proteins, lipids, and nucleic acids, they may function through membrane fusion, interacting with membrane proteins, and endocytosis. For example, it is possible that exosome may function by regulating ECM-cell interaction directly though interacting with membrane proteins. However, since WT CM did not influence the level of p-AKT (Figure S4A), so it is unlikely that exosomes function through AKT phosphorylation regulation.

      (4) Importantly, transitions in cell potency are frequently associated with coordinated morphogenetic changes. For example, during mouse embryogenesis, naïve pluripotent inner cell mass cells progressively polarize into a rosette-like structure with apical domain specification before lumen formation and epithelialization during progression toward the primed epiblast state. This developmental context could help strengthen the biological interpretation of the study.

      We sincerely thank the reviewer for providing this valuable developmental context. We agree that transitions in cell potency are frequently associated with coordinated morphogenetic changes. As the reviewer notes, naïve pluripotent inner cell mass cells progressively polarizing into rosette-like structures with apical domain specification before lumen formation and epithelialization during progression toward the primed epiblast state is highly insightful and directly relevant to our study. This is consistent with our findings that ParKO cells failed to establish proper apical-basal polarity during NPT, resulting in aberrant morphology with mislocalization of ZO1 and CDH1, and markedly impaired differentiation ability.

      In the revised manuscript, in the Introduction section, we have incorporated literature on the role of cell polarity in coordinating both pluripotency transitions and morphogenetic changes during early embryogenesis; in the Discussion section, we have incorporated this developmental perspective to strengthen the biological interpretation of our finding. We believe this contextualization will significantly improve the framing of our study and better connect our in vitro observations to in vivo developmental processes.

      (5) There are also several claims throughout the manuscript that appear to be overinterpreted or insufficiently quantified. For example, in Figure 1, the authors state that CDH1 expression is uniform; however, this is difficult to appreciate from the images shown, and quantitative analysis would be necessary to support this conclusion.

      We thank the reviewer for this important comment. We agree that the claim that "CDH1 expression is uniform" in Figure 1 is overinterpreted based on the images shown, and we apologize for the lack of quantitative support.

      Upon re-examination, we realized that our focus should be on CDH1 localization rather than its expression level or uniformity. In the updated manuscript, we rephrased the statement about uniformity. In addition, we confirmed, through quantitative analysis (e.g., RNA-seq and fluorescence quantification across multiple cells), that neither the mRNA nor the total protein expression level of CDH1 was significantly changed. Because we have clarified in the manuscript that our primary focus is the localization of CDH1, we no longer present these quantitative data in the manuscript to avoid misleading readers.

      (6) Another example appears in Figure 2, where the authors claim that "heatmap analysis revealed that transcriptomic profiles of PAR knockout cells progressively diverged from wild type from day 3 onwards". This conclusion is not fully supported by the presented data for two reasons: (1) transcriptomic divergence is more appropriately assessed through principal component analysis, clustering, or distance-based methods rather than by visual inspection of a heatmap alone; and (2) although some genes displayed in panel E begin to show genotype-associated differences from day 3, the overall transcriptomic structure shown in the PCA and heatmap remains primarily dominated by temporal progression rather than genotype.

      We thank the reviewer for this careful and constructive critique. We apologize for the imprecise claim regarding the heatmap analysis in Figure 2. We agree that 1) transcriptomic divergence should be assessed by PCA, clustering, or distance-based methods rather than by visual inspection of a heatmap alone, and 2) the overall transcriptomic structure shown in PCA and heatmap remains primarily dominated by temporal progression rather than genotype.

      In fact, our main point in this figure was to show that differentially expressed genes (DEGs) between PAR KO and WT become more numerous and more pronounced from day 3 onwards, and the supporting data for this claim are presented in Figure S2A–B. The number of DEGs between PAR knockout and wild-type cells is 480 at day 1, 523 at day 3, 1088 at day 4, and 1893 at day 6. Furthermore, we focused on specific genes within particular signaling pathways, and their expression levels began to show significant differences between PAR knockout and wild-type cells from day 3 onwards.

      We realized that our original wording was misleading. In the revised manuscript, we have rephrased our conclusion more accurately to reflect what the data actually show, focusing on the timing and extent of differential gene expression rather than suggesting a global divergence of transcriptomic profiles.

      (7) In this context, it remains unclear whether PAR knockout cells truly retain a more naïve pluripotent transcriptomic identity. To support this claim, the authors should compare the knockout transcriptome directly against a naïve pluripotent population. The phenotype observed in the knockout cells may instead represent an incomplete or aberrant primed transition rather than maintenance of naïve pluripotency itself. Intermediate morphogenetic states, such as rosette-like epithelial stages, could also explain the observed phenotype.

      We apologize for the confusion caused by our imprecise wording. We realized that our original manuscript may have inadvertently suggested that Par-knockout cells retain a naïve pluripotent transcriptomic identity, which was not our intended claim.

      To clarify, Par knockout naïve cells lose their naïve identity and differentiate toward a primed state during the NPT process described in this manuscript. Unlike wild-type primed cells, PAR-knockout primed cells exhibit altered morphology: they cannot establish or maintain the typical flat morphology, and possess distinct expression profile. In terms of naïve identity, key naïve markers (e.g., Esrrb or Oct4) are downregulated to comparable levels in both wild-type and PAR-knockout primed cells. Although these two cell types differ in their overall expression profiles, several core primed markers (e.g., Fgf5 or Foxa2) show normal expression in both groups. Collectively, these results indicate that Par knockout naïve cells do lose their naïve identity and undergo differentiation toward a primed state during NPT, even though the final primed states of the two cell populations are distinct.

      In the revised manuscript, we have:

      (1) Revisited and revised our wording to avoid any misinterpretation that Par knockout ESCs retain a naïve identity (e.g., see results section).

      (2) Directly compared the expression of naïve and primed makers of Par knockout cells against a true naïve pluripotent population (e.g., naïve ESCs) to further support our conclusion that the knockout cells are not maintaining naïve pluripotency (Figure S4F), but rather exhibiting an aberrant primed state with morphological abnormalities.

      (8) Strengthening this aspect of the study would substantially improve its developmental and in vivo relevance, which currently appears somewhat limited. In particular, it would be interesting to determine whether this mechanism operates during embryogenesis itself. The authors could consider relatively simple but informative experiments, such as perturbing PAR signaling or Furin activity during embryo culture.

      We thank the reviewer for this constructive and forward-looking suggestion. We agree that the current manuscript focuses primarily on in vitro cellular mechanisms, and we have not sufficiently explored the developmental and in vivo relevance of our findings, determining whether this mechanism operates during embryogenesis would strengthen the developmental relevance of our findings. Unfortunately, our laboratory does not have access to embryo culture platforms, which prevents us from performing these experiments.

      However, we have integrated relevant published evidence into the Discussion to contextualize our findings.

      (9) Along the same lines, some statements in the manuscript appear overly speculative. For example, the statement that "these findings may reveal a developmental compensation mechanism during embryogenesis, whereby normal cells rescue defective cells or increase their own proportion" extends well beyond the experimental evidence presented. Such claims invoke concepts related to cell competition, abnormal cell recognition, or developmental quality control mechanisms in vivo, none of which are directly demonstrated in this study. The authors are encouraged either to substantially tone down these statements or move them to the Discussion as speculative possibilities.

      We thank the reviewer for this important critique. We agree that our original statement—"these findings may reveal a developmental compensation mechanism during embryogenesis, whereby normal cells rescue defective cells or increase their own proportion"—is overly speculative and extends beyond the experimental evidence presented in our study. We also acknowledge that it was inappropriate to directly extrapolate from in vitro cellular mechanisms to in vivo developmental rules without proper justification.

      In the revised manuscript, we have removed the statement from the Results section and clarified that our study primarily focuses on the cellular level.

      (10) Another important conceptual point concerns the relationship between PAR complex regulation and Lefty signaling. If this mechanism indeed reflects a physiological or homeostatic process operating during embryogenesis, what would be the developmental rationale for the PAR complex regulation of Lefty? Lefty is well known for its role during gastrulation and anterior epiblast patterning. It would therefore be interesting if the authors could further discuss potential links between these developmental contexts.

      We thank the reviewer for raising this important conceptual point. In our manuscript, we have indeed demonstrated that the PAR complex regulates Lefty signaling under the conditions of this study, and we are aware from the literature that Lefty signaling plays a critical role during early embryogenesis, particularly in gastrulation and anterior epiblast patterning.

      However, we admit that we have not deeply considered the potential pathways and developmental rationale for PAR complex-mediated regulation of Lefty in the context of embryogenesis. This is an important gap in our current discussion.

      In the revised manuscript, we have:

      (1) Reviewed and incorporated relevant literature to better understand and discuss the potential links between PAR complex regulation and Lefty signaling during early embryonic development, including possible connections to gastrulation and anterior patterning.

      (2) Offer speculative but informed perspectives on the developmental rationale for such regulation, while clearly distinguishing between what our data directly show and what remains to be explored in future studies.

      Minor points:

      (1) The authors state that PAR knockout cells do not exhibit major differences in self-renewal capacity; however, they simultaneously claim that these cells remain in a more naïve-like state. This interpretation requires clarification, as naïve pluripotent cells are typically associated with increased clonogenicity, enhanced self-renewal, and expression of markers such as alkaline phosphatase and SSEA1 compared to primed cells. The relationship between the observed phenotype and the proposed "naïve-like" state should therefore be discussed more carefully.

      We thank the reviewer for this comment, which addresses a similar concern as Point 7 mentioned above. Consistently, we do not claim that PAR knockout cells remain in a more "naïve-like" state. Our actual conclusion is that PAR knockout naïve cells undergo differentiation toward the primed state during NPT. However, due to loss of cell polarity, PAR knockout primed cells fail to establish and maintain the typical flat morphology and instead form dome-shaped colonies. Importantly, these dome-shaped colonies do not retain the characteristics of the naïve state, such as increased clonogenicity, enhanced self-renewal, or expression of alkaline phosphatase and SSEA1.

      In the revised manuscript, we have:

      (1) Revised our wording to avoid any misinterpretation that PAR knockout primed cells maintain a naïve-like identity (e.g., see results section).

      (2) Explicitly clarified that the observed dome-shaped morphology represents an aberrant primed state rather than a naïve or naïve-like state in Figure 2B and 2C.

      (3) Examined naïve and primed markers in Par KO naïve and primed cells, demonstrating that Par KO primed cells exhibit only abnormal morphology but have lost naïve identity and acquired primed identity in Figure S4F.

      (2) The authors generated several independent knockout clones, but appear to use only one clone for downstream analyses after observing similar morphogenetic phenotypes. Is this sufficient to account for potential clonal heterogeneity? Would the use of pooled clones provide a more robust experimental system?

      We thank the reviewer for raising this important concern regarding clonal heterogeneity. We agree with the reviewer that our current approach—using only one representative knockout clone for downstream mechanistic analyses after confirming similar morphogenetic phenotypes across multiple independent clones—is not sufficient to fully exclude potential clonal heterogeneity.

      To address this issue, we performed additional experiments in the revised study. Specifically, we used another independent knockout clone (ParKO6) to repeat the key mechanistic analyses. The following experiments were carried out:

      (1) ParKO6 and wild-type ESCs were be subjected to NPT. During the NPT process, cells were be treated with an AKT inhibitor (MK2206), a FAK inhibitor (PF562271), or WT CM. We observed whether the morphological defects of ParKO6 cells are rescued, and RT-qPCR was performed to characterize the molecular features of ParKO6 cells under these conditions (Figure S4C, S4D and S4F).

      (2) After treatment with the AKT inhibitor (MK2206), FAK inhibitor (PF562271), or WT CM, immunofluorescence (IF) was conducted to detect p-FAK levels in ParKO6 cells (Figure S4E).

      (3) Following the same treatments, Western blotting (WB) was performed to detect FURIN and LEFTY protein levels in ParKO6 cells (Figure S4J).

      These additional experiments confirmed that the observed results are not due to clone-specific artifacts from the originally used clone.

      (3) The rescue experiments using pathway inhibitors are interesting; however, the interpretation again relies primarily on colony morphology. Readers may question whether these experiments truly represent rescue of the naïve-to-primed transition itself without additional transcriptomic or molecular characterization.

      We thank the reviewer for this important comment. We apologize for the lack of clarity in our original manuscript, which may have led to the misunderstanding that our interpretation of the rescue experiments relied solely on colony morphology.

      In fact, we did perform molecular characterization on a subset of cells rescued by pathway inhibitors, and these data are presented in Supplemental Figure S2D–E. We realized that our description of these results was insufficiently clear, and we failed to properly highlight this molecular evidence in the main text.

      In the revised manuscript, we have revised our wording to clearly state that the rescue effects are supported not only by morphological observations but also by molecular characterization (Page 17, Line 360-362).

      (4) In Figure 4, the manuscript could be strengthened by integrating transcriptomic analyses from pharmacological treatments with the secreted-factor and co-culture datasets.

      We thank the reviewer for this constructive suggestion.

      In our current manuscript (Figure 4), we have indeed performed an integrated transcriptomic analysis comparing pharmacological treatment and secreted-factor treatment, and we demonstrated that both treatments converge on the FAK signaling.

      Regarding the co-culture dataset, we did not include it in the integrated analysis presented in Figure 4. This is because, based on our data in Figure 3, we concluded that the rescue effect observed in co-culture is primarily mediated through secreted factors. Therefore, the secreted-factor transcriptomic data already capture the key signaling pathways responsible for the co-culture rescue effect.

      (5) The authors could better clarify the context of Furin downregulation in the knockout cells. Is this a direct consequence of altered transcriptional regulation by the PAR complex, or could it instead represent a secondary consequence of impaired progression through the primed pluripotent transition?

      We thank the reviewer for this important mechanistic question.

      Based on our experimental data, we conclude that Furin downregulation in PAR knockout cells is a direct consequence of altered transcriptional regulation by the PAR complex, rather than a secondary consequence of impaired progression through the primed pluripotent transition. Our evidences are as follows:

      (1) Transcriptomic analysis revealed that PAR knockout leads to a significant reduction in Furin RNA levels.

      (2) Western blot analysis confirmed that PAR knockout also results in a significant reduction of FURIN protein levels.

      (3) Importantly, treatment with an AKT inhibitor (upstream of the proposed pathway) significantly upregulated both Furin RNA and protein levels in PAR knockout cells. In contrast, treatment with a FAK inhibitor or WT CM (downstream) did not significantly alter Furin expression.

      These data collectively indicate that Furin downregulation is directly linked to PAR complex-mediated transcriptional regulation, rather than being an indirect consequence of defective primed state transition.

      Reviewer #2 (Public review):

      Summary:

      The study demonstrated that Par, but not other polarity genes, Crumbs or Scrib, regulates cell polarity during PSC transition to primed state as well as neural tube formation.

      Strengths:

      The use of KO convinces the role of Par in NPT. Scrib and Crumbs KO data are informative to the field. The conditioned medium experiment is informative. They suggested the potential secreted factors over 50kDa are responsible for maintaining the polarity of NPT in Par KO.

      Weaknesses:

      (1) Most importantly, how Par is important for PSC maintenance and differentiation is not clear. The data provided are dome shape formation, endoderm lineage tendency, and neural tube formation reduction. The manuscript lacks a core message of the physiological importance of Par. Is Par critical of PSC maintenance? Is Par critical for neural system development?

      We thank the reviewer for this critical comment, which helps us better articulate the core message of our study.

      In our manuscript, we have provided clear evidence regarding the role of the PAR complex in pluripotent stem cell (PSC) maintenance and differentiation:

      (1) Regarding PSC maintenance:

      The PAR complex is not critical for PSC maintenance under self-renewing conditions. Specifically, PAR knockout does not significantly affect the expression levels of pluripotency genes (Figure 1B–C and Supplemental Figure 1C). Moreover, PAR knockout PSCs can be continuously cultured for at least 30 passages without notable changes in cell morphology or proliferation capacity (Figure 1D–F). These findings are consistent with previous literature, which demonstrated that the core function of the PAR complex is to establish and maintain cell polarity, rather than directly regulating the transcriptional network of pluripotency genes. In the revised manuscript, we have clearly stated that Par knockout does not affect pluripotency maintenance of ESCs (Page 7, Line 142).

      (2) Regarding PSC differentiation:

      The PAR complex is important for proper differentiation. PAR knockout leads to multiple differentiation defects, including: Failure to establish normal cell morphology during (NPT) (Figure 1G–K), impaired formation of proper three-germ-layer structures during teratoma and embryoid body (EB) differentiation (Figure 5A–F). In particular, the type and quantity of ectodermal tissues are significantly reduced. Consistent with our findings, previous literature has reported that PAR complex deficiency leads to neural developmental defects in mouse embryos, resulting in mid-gestation embryonic lethality.

      (3) Regarding neural system development:

      The PAR complex is critical for neural development. During neural stem cell (NSC) differentiation, PAR knockout cells exhibit a significantly reduced efficiency of NESTIN-positive cells and fail to form the classical rosette structures (Figure S5B–C). During neural tube organoid induction, PAR knockout cells show significantly impaired lumen formation and spontaneous elongation efficiency. Moreover, during subsequent maturation, PAR knockout cells fail to differentiate into neurons, leading to a marked reduction in neural tube organoid maturation efficiency (Figure 6B–E).

      These findings are consistent with previous literature showing that in zebrafish embryonic development, mislocalization of the PAR complex leads to neural tube abnormalities while PAR complex deficiency results in severe hydrocephalus; in mouse embryonic development, PAR complex deficiency causes neural developmental defects leading to embryonic lethality; and disruption of the PAR complex impairs the formation of apical tight junctions in the neuroepithelium and subsequent neuroepithelial tissue polarization, resulting in neural tube closure defects in humans.

      In the revised manuscript, we have incorporated classical literature to discuss the essential roles of the PAR complex in early embryonic development (Page 4, Line 81-84), thereby providing a broader developmental context for our findings.

      (2) Secondly, the AKT-FURIN-...... axis still lacks supportive data. Various inhibitors were used to rescue the Par KO. But the link between each component in the axis is missing and rather superficial.

      We thank the reviewer for this critical comment. We acknowledge that the proposed AKT–FURIN–LEFTY–ECM-integrin–FAK signaling axis has certain limitations, particularly that the connection between LEFTY and ECM-integrin lacks direct experimental support. Therefore, in the revised manuscript, we de-emphasized the role of ECM and integrin and revised the signaling axis to AKT–FURIN–LEFTY–FAK.

      We believe the current data and previous publications support this revised signaling axis well. Accordingly, we have summarized the relevant information as follows. In addition, we performed additional experiments to further support the new signaling axis, which are also included in the following text.

      (1)AKT-FAK

      We found that Par KO cells exhibit defects during NPT, and these defects can be rescued by AKT inhibitor (MK2206), FAK inhibitor (PF562271), and WT CM. Through transcriptomic analysis, we found that both AKT inhibitor and WT CM share similar expression profiles with WT and converge on FAK signaling. Notably, through Western blotting analysis, we found that Par KO led to upregulated p-AKT levels, which were effectively suppressed by MK2206 treatment, but WT CM did not decrease p-AKT levels. In contrast, through immunofluorescence analysis, we found that FAK signaling was hyperphosphorylated in Par-knockout-primed cells compared to WT primed cells, and MK2206, WT CM, and PF562271 all effectively reduced p-FAK levels. Given that both MK2206 and WT CM attenuated the elevated p-FAK, we propose that all three treatments restore the flat monolayer morphology by regulating FAK signaling homeostasis, with WT CM acting downstream of AKT signaling. The relevant data are presented in Figure 1G-I, Figure 2D-F, Figure S2C, Figure 3H-I, Figure 4A-D, Figure S4A, and Figure S4C-E.

      (2) AKT-LEFTY

      Through integrated proteomic and transcriptomic analysis, we identified a set of functional proteins. Proteomic analysis revealed that the protein levels of LEFTY were higher in WT CM compared to KO CM, suggesting that WT cells modulate FAK signaling via secretion of LEFTY proteins. Overexpression screening revealed that LEFTY exhibited the most significant rescue effect in Par KO cells during NPT. It is therefore reasonable to infer that MK2206 rescues the defects in Par KO primed cells through upregulation of LEFTY expression. Western blotting analysis confirmed this, showing that MK2206 significantly increased LEFTY protein levels in Par KO primed cells. The relevant data are presented in Figure 4E-F, Figure 4H, Figure S4G-H, and Figure S4J.

      (3) LEFTY-FAK

      Proteomic analysis indicated that WT CM supplied extracellular LEFTY to Par KO cells, thereby rescuing the phenotypic defects of Par KO-primed cells, and significantly reduced p-FAK levels in these cells. Concordantly, LEFTY overexpression also reduced p-FAK in Par KO primed cells. These results are consistent with the reported role of LEFTY in suppressing FAK signaling (Alowayed et al., 2016). The relevant data are presented in Figure 4D, Figure 4F, and Figure S4H-I.

      (4) AKT-FURIN

      LEFTY proprotein requires convertase like FURIN to cleave and mature for secretion and function (Dubois et al., 2001). Through transcriptomic analysis, we found that Par KO downregulated Furin mRNA expression, while MK2206 treatment restored its expression levels. Through Western blotting analysis, we found that MK2206 increased FURIN protein abundance and cleaved LEFTY levels. The relevant data are presented in Figure 4G-H. To further validate the regulation of AKT on FURIN, we treated ParKO6 cells with MK2206 during NPT, and observed an increase in FURIN protein (Figure S4J).

      (5) FURIN-LEFTY

      To validate the role of FURIN in LEFTY maturation, we treated WT cells with BOS318, a highly specific and potent inhibitor of FURIN that irreversibly binds to the protease by mimicking its natural substrate (Ivachtchenko et al., 2024). BOS318 induced WT primed cells to adopt a dome-shaped morphology resembling Par KO primed cells, confirming that inhibition of FURIN prevents LEFTY secretion and function, leading to defective primed cell morphology. The relevant data are presented in Figure 4I-J. To further strengthen the role of FURIN in regulating LEFTY during the revision, we treated wild-type cells with BOS318 and examined the expression changes of LEFTY, it was found that BOS318 treatment decreased LEFTY levels (Figure S4K).

      (6) ECM/integrin

      Integrated analysis of both transcriptomic and proteomic data revealed that Par KO leads to significant enrichment of pathways associated with ECM and integrin (Figures 2D, 3F, 3K, and S4B). Notably, both MK2206 and WT CM treatment co-upregulated the ECM-receptor interaction pathway (Figure 4C). The FAK signaling pathway serves as a central node that integrates upstream inputs from both PKC and AKT pathways while transducing extracellular cues derived from ECM-integrin interactions into intracellular signaling cascades (Sakthivel et al., 2025). We therefore propose that secreted LEFTY acts as an extracellular signal that modulates ECM receptors and integrin complexes, thereby regulating FAK phosphorylation and maintaining normal cell adhesion and morphology. To test this hypothesis, we subjected LEFTY-overexpressing Par KO ESCs to NPT, followed by qPCR analysis. During NPT, Par KO led to downregulation of the mRNA levels of ECM- and integrin-related components, whereas LEFTY overexpression significantly upregulated the mRNA levels of these components (Fig. S4L). Nevertheless, we are aware that our data in this part are limited; therefore, in the revised manuscript, we have de-emphasized the role of ECM and integrin in the AKT–FURIN–LEFTY–FAK axis and present it as a possible mechanism rather than a confirmed step.

      References

      Alowayed, N., Salker, M.S., Zeng, N., Singh, Y., and Lang, F. (2016). LEFTY2 Controls Migration of Human Endometrial Cancer Cells via Focal Adhesion Kinase Activity (FAK) and miRNA-200a. Cellular Physiology and Biochemistry 39, 815-826.

      Brons, I.G., Smithers, L.E., Trotter, M.W., Rugg-Gunn, P., Sun, B., Chuva de Sousa Lopes, S.M., Howlett, S.K., Clarkson, A., Ahrlund-Richter, L., Pedersen, R.A., et al. (2007). Derivation of pluripotent epiblast stem cells from mammalian embryos. Nature 448, 191-195.

      Dubois, C.M., Blanchette, F., Laprise, M.-H., Leduc, R., Grondin, F., and Seidah, N.G. (2001). Evidence that Furin Is an Authentic Transforming Growth Factor-β1-Converting Enzyme. The American Journal of Pathology 158, 305-316.

      Ivachtchenko, A.V., Khvat, A.V., and Shkil, D.O. (2024). Development and Prospects of Furin Inhibitors for Therapeutic Applications. International Journal of Molecular Sciences 25.

      Matsuda, M., Rozman, J., Ostvar, S., Kasza, K.E., and Sokol, S.Y. (2023). Mechanical control of neural plate folding by apical domain alteration. Nat Commun 14, 8475.

      Park, J., Hsiung, H.-A., Khven, I., La Manno, G., and Lutolf, M.P. (2022). Self-organizing in vitro mouse neural tube organoids mimic embryonic development. Development 149.

      Sakthivel, K., Kotowska, A., Fan, Z., Portner, E.J., Merry, C., Nordenfelt, P., Simonsen, A.C., Wright, A.J., and Swaminathan, V.S. (2025). Integrin‐Piezo1 Axis Drives ECM Remodeling and Invasion of 3D Breast Epithelium. Advanced Science.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Reviewer #1 (Public review):

      Summary:

      This study was motivated by the general claim that delayed development of cognitive control can be beneficial for learning, and investigated this claim in the specific domain of conceptual development. A comprehensive set of computational model simulations showed that delaying the onset of semantic control produces faster learning with only minimal effects on conceptual abstraction. The simulations also showed that control was most effective at intermediate levels between modality-specific "spokes" and the multimodal "hub". A meta-analysis of developmental data was consistent with the claim of delayed onset of semantic control: young children show substantially better semantic knowledge than the ability to constrain that knowledge to a specific task at hand.

      Strengths:

      The computational modelling is based on a very well-established model of semantic cognition, which means that the simulations allow exploring the specific issues under investigation here in the context of a model that accounts for a very large set of semantic cognition phenomena. The simulations are comprehensive - manipulating different parameters of the model provides important insights into how (and why) it works.

      In addition to simulations exploring delayed maturation, there is an exploration of where semantic control is most effective, yielding the interesting result that control is most effective when it targets intermediate levels of semantic processing. To my knowledge, this is a novel finding and a concrete prediction for future testing.

      The meta-analysis is designed in a very clever way that allows extracting evidence of semantic control from a large body of prior work. The results are quite clear and compelling in showing that semantic knowledge is acquired before children are able to use task demands to constrain the use of that knowledge.

      We thank the reviewer for highlighting the core contributions of the research, in particular, their view that our evidence is a compelling demonstration that there is a delay for semantic control in relation to semantic representation and that this may be beneficial. We address each of the reviewer’s concerns in turn below.

      Weaknesses:

      Computational models of cognition inherently require simplification in order to focus on the mechanisms under investigation. However, it is also important to keep these simplifications in mind because they limit the generality of the inferences that can be made from the simulation results. Two aspects are important in this context:

      (1) The multimodal structure was orthogonal to the surface similarity structure of the concepts to be learned. It is certainly true that multimodal structure does not perfectly mirror surface similarity, but closely related things tend to be perceptually similar. There are exceptions (whales, penguins, etc.), but they are *exceptional*, not typical. It may be that the somewhat extreme dissociation of multimodal and surface similarity structures creates demands that are not faced in natural conceptual development.

      We agree that the model environment is relatively small-scale and may not reflect all aspects of our real environment. However, one virtue of the small-scale modelling endeavour in the current work is that we can be very explicit about the nature of the structure apparent within and across spokes. The reviewer notes that, whereas our model environment employs orthogonal structures across spokes and for the cross-modal features, perceptual structure may be better-aligned with conceptual structure for real-world experience. While we appreciate the intuition, its validity depends to a key extent on how visual information about objects is encoded. Conceptual structure is certainly not apparent, for instance, in the distance between bitmap images of objects, nor the overlap of simple feature-extraction algorithms (such as edge detection or Fourier decomposition, etc). Even in this age of deep vision models, it remains unclear how the visual system extracts and discerns perceptual similarity from retinal input (see e.g. Mukherjee & Rogers, 2025). Most successful contemporary models train neural networks to assign visual images to semantic categories, suggesting that the visual features the model learns, and thus the perceptual similarities it represents, depend on learning to generate semantic information. Therefore, it is not clear whether the similarity that people perceive amongst instances of the same class is natively apparent in the bottom-up visual input, or whether it depends on semantic/cross-modal learning and representation.

      It should also be noted that within our training environment, there are features in each modality that are predictive of features in other modalities (those classed as part of the multimodal structure), as well as some that are only predictive of features within this modality (those within each unimodal structure). Thus, the full cross-modality conceptual structure is not orthogonal to the information available in each sensory domain, instead there is a relationship between surface and multimodal similarity in the dataset as in the real-world environment. Similarly, the results presented here are consistent whether the full cross-modal structure is assessed (using all features), or the individual multimodal and unimodal structures. While it will be interesting for future research to consider the scalability and ecological validity of these results, this is not a trivial endeavour.

      These points have been clarified in the Methods and Discussion text:

      “Thus, anatomy and maturational delay can conspire to promote fast learning with good conceptual abstraction, with the maturational delay allowing the full network to lay down base representations that approximate the cross-context structure of the environment before control begins to shape behaviour and control interfacing at an intermediate part of the semantic representation network leaving the multimodal hub relatively insulated from control. The current analyses demonstrate this in the context of a relatively simple model environment, allowing explicit assessment of representation quality. Again, future work should assess the scalability of such assessments to the complexity of a real-world environment.”

      “The model environment is the same as in Jackson et al., (2021), designed to assess how well each model layer can encode cross-modal similarity structure through conceptual abstraction across sensory modalities and contexts. It includes 16 concepts, each possessing a unique activation pattern across 12 feature units in each of the 3 modality-specific information channels (see Figure 1.B.). While this environment is relatively simple, it allows us to be explicit about the nature of the structure within and across modality-specific spoke regions.”

      “The inclusion of features that express the same structure across modalities ensures that the full multimodal structure differs from that apparent in any single channel, and captures the common intuition that conceptual structure emerges from patterns of covariation across stimulus modalities and task contexts. Note that while the unimodal and multimodal structures are orthogonal, the presence of both unimodal and multimodal structures within each modality means that the multimodal conceptual structure is not orthogonal to the information available in each sensory domain.”

      (2) Much of the benefit of delayed semantic control seems to be because the model is not penalised for activating task-irrelevant features. This blurs the distinction between being aware of a feature and making a response based on that feature. A full model that also includes a response layer could become a lot more complicated and more difficult to understand, so maybe there is an advantage to using a simpler architecture.

      As the reviewer notes, our model does not separately simulate response-generation and the selective activation of relevant feature representations. We agree that there are interesting questions about how feature-potentiation and response-generation relate to one another, and that incorporating response selection in the current model would significantly complicate the analysis. The general idea that control potentiates/suppresses task-relevant feature representations in addition to simply promoting the correct response derives from classic work by Martin and others (e.g., Martin et al., 1995) showing that, for instance, regions involved in colour perception activate more strongly in tasks requiring retrieval of colour than tasks involving retrieval of action and vice versa—results consistent with the model training/testing procedure in the current work. In general, it may be counterproductive to become aware of aspects of a concept that would be irrelevant, or even actively unhelpful in making a response, suggesting guided activation is a necessary precursor to response selection (Botnivick & Cohen, 2014). Here, we focus on this important feature potentiation step.

      We now highlight this important distinction in the Introduction text:

      “Thus, the model of controlled semantic cognition must learn concepts by integrating their constituent features across sensory modalities, episodes and contexts, reflecting semantic representation processes, but it must also produce context-sensitive responses based on current task goals: features presented as input in one of three informational modalities must generate output across some but not all modalities based on a task context representation originating in PFC. This semantic control demand reflects the selection of task-appropriate and/or inhibition of task-irrelevant conceptual features necessary for context-sensitive behaviours. As it may be counterproductive to become aware of aspects of a concept that would be irrelevant, or even actively unhelpful in making a response, such guided activation is considered a necessary precursor to response selection (Botnivick & Cohen, 2014).”

      In addition, there is a bit of a misalignment between the model simulations and the meta-analysis. In the model, there are distinct modality-specific "spokes" and control is required in order to focus on modality/spoke in a task-appropriate way. The meta-analysis does not compare a task-defined selection of a modality; it compares the selection of taxonomic vs thematic relations, both of which are multimodal. One way to resolve this is to say that taxonomic and thematic relations are also represented in distinct sub-systems of semantic knowledge and semantic control is needed to select between them in a task-appropriate way.

      This is particularly relevant to the inference at the bottom of p. 38: "taxonomic and thematic relationships ...[are]... both being encoded within the same system of representation", which seems in direct contradiction to the present results, or at least to the logic of combining these simulations with this meta-analysis. The simulations are based on semantic control being used to select/constrain the correct distinct sub-system (modality-specific spoke); the meta-analysis is based on semantic control being used to select/constrain the correct relationship type. If these two things are analogous in some way, then the relationship type has to be something like a distinct sub-system.

      We thank the reviewer for highlighting the lack of clarity in the relationship between the taxonomic and thematic relationships considered in the behavioural meta-analysis and the features in different spoke regions simulated with the models. Both the model and the meta-analysis focus on the same mechanism, the controlled selection of task-appropriate features. In the case of the meta-analysis, this was the features and associations needed to identify the taxonomic or thematic relationships. As the reviewer notes, one possibility is that these kinds of structures are represented in distinct cortical regions. For instance, Schwartz, Mirman, and colleagues have suggested that temporoparietal regions may preferentially support thematic knowledge while temporal regions may preferentially support taxonomic knowledge. Alternatively, they may be supported by different features instantiated within the same regions, for instance, both have been shown to rely upon the anterior temporal lobe hub (Jackson et al., 2015). This could be in concert with relative differences in involvement of different spoke regions. However, whether taxonomic and thematic relationships require access to features in different regions or not, is not crucial to the conclusions of this paper.

      The simulations used here happen to select features based on their inclusion in a particular sensory modality, yet they could learn to select any combination of features within and across regions. Thus, thematic and taxonomic relationships would simply need to rely on different features, not different regions to enable their task-relevant selection. This reliance on different features is well accepted. Future work should consider whether the selection of features across versus within brain regions has any implications for the onset of semantic control.

      We have extended the rationale for the comparison of taxonomic and thematic relationships in text to clarify these issues:

      “In high control studies all trials have both a thematic and taxonomic match, but the instructional context indicates which kind of information should drive the selection. These trials thus require both the relevant semantic knowledge and the ability to select the correct kind of information for the task.”

      Note that taxonomic and thematic relationships are encoded by different varieties of environmental structure—for instance, dogs, wolves and foxes are similar by virtue of shared parts, behaviours, and appearances, but dogs, bones, and leads are similar by virtue of common co-occurrences with one another and with other contextual cues (e.g., Binder et al., 2016). Consequently, selecting the taxonomic versus thematic relationships relies upon selecting some set of relevant features and inhibiting a different set of irrelevant features, whether these are represented in the same or different brain areas. This is the same operation performed by the computational models in Part 1.

      We have also highlighted the potential for further investigation as to the impact of different versus overlapping spoke regions in the Discussion:

      “The current analyses demonstrate this in the context of a relatively simple model environment, allowing explicit assessment of representation quality. Again, future work should assess the scalability of such assessments to the complexity of a real-world environment and the impact of selecting different features within the same versus different modalities.”

      Reviewer #1 (Recommendations for the authors):

      My critiques are listed under the "Weaknesses" section of the Public Review. The modelling weaknesses perhaps deserve a bit of discussion but are not necessarily critical. The issue of how modality control is meant to align with taxonomic/thematic control is somewhat more pressing because I think there is an incorrect inference (as explained in the Weaknesses section).

      We thank the reviewer for their positive comments. We have discussed each of these points above and hope that the clarification that it is not critical whether the model selects features within or between sensory regions resolves the apparent contradiction between the modelling and behavioural work.

      Reviewer #2 (Public review):

      Summary:

      This paper investigates the idea that the protracted maturation of the prefrontal cortex - often viewed as a developmental limitation - may actually confer advantages for conceptual learning in children. The authors focus on semantic control processes, which govern the context-sensitive application of conceptual knowledge, and are closely associated with late-developing regions of the prefrontal cortex.

      Drawing on a computational model, the paper formally tests whether delayed maturation of semantic control promotes the acquisition of conceptual knowledge. The simulations demonstrate that when semantic control and anatomical connectivity mature later, conceptual learning is accelerated without compromising the integrity of the learned representations. Notably, the benefit is most apparent when control connections target intermediate layers in the computational model, suggesting a nuanced interplay between control processes and the underlying conceptual network.

      To validate these computational insights in a human developmental context, the authors conduct a meta-analysis of the classic triadic matching task - a paradigm where participants decide which of two choices best matches a reference concept based on either taxonomic or thematic relations. Critically, when these relations conflict, semantic control is required to select the context-appropriate match. Results indicate that context-sensitive semantic control develops more slowly than basic conceptual knowledge, showing marked improvements between 3 and 6 years of age.

      Overall, the paper argues that the delayed development of prefrontal cortex-based control processes allows for a period of less constrained learning, ultimately enhancing conceptual acquisition. The findings challenge the traditional view of late PFC maturation as solely disadvantageous and instead position it as an adaptive feature for building robust conceptual frameworks in early childhood.

      Strengths:

      (1) Novel Theoretical Contribution

      The paper offers a compelling, counterintuitive argument that a developmental lag in the maturation of control processes might be beneficial for semantic learning. This stands in contrast to the conventional framing of late prefrontal cortex (PFC) development as purely disadvantageous (e.g., a "necessary but unfortunate" constraint).

      (2) Well-Grounded Computational Approach

      The authors propose a neural network model that is both theoretically driven (hub-and-spoke framework) and systematically tested under various conditions (different timelines for control onset, and different connectivity patterns). Their simulations replicate and extend previous findings about how insulating the multimodal hub from direct control inputs helps preserve abstract conceptual representations.

      (3) Neuro-anatomical basis

      The paper connects its computational claims to empirical neuroanatomy, particularly the lack of direct structural connectivity between ventral ATL (the "hub") and the PFC in humans. This lends biological plausibility to the argument that control signals likely reach the ATL via intermediate regions (e.g., posterior temporal cortex).

      (4) Meta-Analysis of Triadic Match-to-Sample

      The authors leverage decades of developmental data on conceptual matching tasks, reframing them in terms of semantic control vs. semantic representation. Their analysis nicely illustrates that children can identify semantic relationships (taxonomic or thematic) at age 2 if the task does not require them to select between conflicting semantic relations. In contrast, the ability to choose a task-relevant relation only emerges more robustly in 3-6 years. This developmental pattern aligns with the computational model's predictions.

      We thank the reviewer for their positive comments on the theoretical importance of the research presented here, including its novelty and grounding in theory and neuroanatomy. We have addressed each of the reviewer’s concerns in turn below.

      Weaknesses:

      The contribution of the paper might be considered rather specialist, and might not appeal to a broad public, which should be typical of a generalist journal. Moreover, the scope of the model is fairly narrow - its relatively small, controlled training environment raises questions about scalability to more naturalistic, high-dimensional data.

      Given the theoretical and behavioural implications of the research, we believe it to be of wide interest to researchers in executive control, semantic cognition, and neural development more generally. We address the specific comments on model scalability in the weaknesses section below.

      Finally, the meta-analysis does not test directly the model predictions in terms of specific outcomes of the task, error patterns, or model fit, but only the developmental pattern which was an already observed phenomenon that in part motivated the hypothesis and the model itself.

      We thank the reviewer for highlighting the need for a clearer distinction between the known delay in domain-general executive control and the previously unknown delay in semantic control, hypothesised by the model. The reviewer suggests the results of the meta-analysis were already known and provided motivation for the simulation. However, an important contribution of the current work is the observation that, in fact, there is very little prior work on the development of semantic control. The widely known developmental delay in domain-general executive control, which did indeed motivate the study, is exclusively based on tasks requiring very different forms of executive control to semantic control assessments. Many of these involve no meaningful stimuli or require the child to completely inhibit a practiced response and generate an opposite or completely arbitrary responses, instead of requiring the child to use context to select among two or more meaningful behaviours that are equally valid in different contexts (see the introduction to Part 2). Such tasks are considered to rely upon domain-general executive control brain regions. Unlike domain-general control, semantic control relies on specialised neural systems which differ to the executive function of other domains, with inferior frontal and posterior temporal regions crucial for semantic, but not, non-semantic control (e.g., Hodgson et al., 2024). Consequently, its developmental trajectory could differ substantially. Alternatively, it could be similar if the ventrolateral and dorsolateral PFC develop at a similar rate. Delineating the developmental trajectory of semantic control requires a task in which control is applied to the context-appropriate retrieval and manipulation of semantic knowledge, such as the triadic matching task. Moreover, the results show that semantic control, while arising later than semantic representation, nevertheless begins to mature earlier (around 2.5 years) than typical estimations of domain-general executive control (around 4). Thus, the meta-analysis contributes to our understanding of cognitive development while also testing a key prediction of the model.

      We have edited the manuscript text to more clearly differentiate semantic and executive control, and clearly establish what is and is not known about the developmental trajectory of each of these processes. Throughout we have improved our consistency of the terms ‘semantic control’ and ‘domain-general executive control’. In addition, we have extended the explanation for the distinction between these processes and their neural differences -

      “Unlike domain-general executive control, the developmental trajectory of semantic control is unknown, allowing us to first consider whether it would be beneficial for semantic control to develop later than semantic representation and then subsequently, to consider whether it does develop late in human development.”

      While many domains require control processes to shape behaviour, semantic control relies on at least partially distinct systems from executive control more generally. Functional brain imaging and patient studies suggest that the ventrolateral prefrontal and posterior temporal substrates crucial for semantic control are specialised for the control of meaningful content, and not domain-general executive control (Chiou, Jefferies, Duncan, Humphreys, & Lambon Ralph, 2023; Gao et al., 2021; Hodgson, Lambon Ralph, & Jackson, 2021; Hodgson, Lambon Ralph, & Jackson, 2024; Humphreys & Lambon Ralph, 2017; Jackson, 2021; Jefferies & Lambon Ralph, 2006). Thus, the regions supporting semantic control are at least partially dissociable from those supporting the executive control of other domains, with differential reliance on ventrolateral versus dorsolateral prefrontal areas, as well as posterior temporal versus parietal cortices. Such dissociations may partially reflect the differences in how control operates in semantic retrieval versus other executive tasks. Semantic control makes use of contextual information to generate accurate and task-appropriate semantic inferences—for instance, inferring the weight of a piano rather than its function in the context of moving house, but function rather than weight in the context of a recital. In both cases, the information retrieved is true of the piano, and the control system shapes which inference is to guide subsequent behaviours in a context-appropriate manner. Neither fact about pianos is arbitrary, unfamiliar, or difficult to retrieve; they are simply relevant in different situations.

      In contrast, executive control tasks often employ measures requiring the inhibition of some strong behavioural impulse, or a tendency to behave in accordance with a novel, arbitrary rule (e.g., Kochanska, Murray, & Harlan, 2000)—a kind of behaviour known to develop late (e.g., Zelazo et al., 2008). For instance, several tasks require the child to forego an immediate reward for a period of time (e.g., Delay of Gratification, Forbidden Toy, Gift Delay, Pinball, Snack Delay), to abandon impulsive behaviours in favour of those that accord with social conventions (e.g., Disappointing Gift; Whisper task; turn-taking in the Tower task), to inhibit previously successful behaviours (e.g. multilocation search tasks, dimensional-change card sort) or responses to perceptually salient stimuli (e.g., shape Stroop), or to generate temporal sequences of behaviours conforming to an arbitrary rule (e.g., backward digit span, count-and-label, motor sequencing). While some executive tasks do include selection and inhibition processes that seem to parallel those of semantic control (such as the Cattell Culture Fair Task; Cattell, 1971; Woolgar, Bor, & Duncan, 2013), nevertheless such tasks recruit different brain networks for meaningful words versus meaningless shape stimuli even when task processes and demands are matched, with greater ventrolateral PFC and posterior temporal cortex involvement for meaningful stimuli (Hodgson et al., 2024).

      Thus, delineating the developmental trajectory of semantic control specifically requires tasks in which control is applied to the context-appropriate retrieval and manipulation of semantic knowledge. Unlike domain-general executive control, the development of semantic control has not been extensively studied. Because semantic control also relies on the PFC, it seems plausible that it should follow a similar developmental trajectory to general executive function. Yet the PFC itself is neither anatomically nor functionally homogeneous, with different subregions maturing along different timelines (Gogtay et al., 2004; Sowell et al., 2002). Because semantic control relies upon a distinct ventrolateral PFC region, it is equally possible that its developmental trajectory differs from that of domain-general executive control.

      “The simulations suggest that a delay in the maturation of the semantic control system can lead to overall faster mastery of controlled semantic behaviours and to better structured semantic representations. Does the literature contain evidence of such a delay? As noted in the Introduction, research on the development of semantic control is lacking, with much of the prior control research tapping into distinct domain-general executive control processes and/or utilising tasks lacking the retrieval of any semantic knowledge. Thus, it is unknown whether semantic control develops later than semantic representation. Next, we assess existing research at the border of executive control and semantic cognition to determine whether it can provide any clues as to the development of semantic control.”

      Reviewer #2 (Recommendations for the authors):

      (1) Training Environment: The model's environment (16 concepts, each with certain cross-modal features) is relatively small and highly controlled. While that is appropriate for proof-of-concept work, readers might wonder about scalability and whether the same effects would hold in larger, noisier, or more naturalistic training sets.

      We agree that the model and its environment are relatively small, simplifications of reality, and readers may wonder about implications for ecological validity of the simulations and scalability to larger, noisier, and potentially more systematically structured training environments. This is an important direction for future research, but one that faces nontrivial challenges. For example, the nature of the mechanisms that allow for context-sensitive responding in large-scale language/vision models such as GPT 4 are complex and may not be ‘brain-like’. Such models are trained on web-scale language and vision and provide a means of simulating controlled behaviour with realistic stimuli, so might seem to provide a means of assessing scalability of current neuro-cognitive models. Large language/vision models rely, however, on transformer architectures whose relationship to hypothesized mechanisms of control in the mind and brain is unclear. In transformers, context-sensitive responding depends upon “attention” mechanisms that are fully distributed and integrated throughout the entire system—there is no distinction between control, representation, and short-term memory in the architecture. As a consequence, it is very difficult to understand why a model behaves the way it does, or to relate patterns of behaviour to hypothesised mechanisms in the human mind/brain. Yet transformers are currently the only models capable of exhibiting context-sensitive patterns of responding based on both language and vision. Scaling up neuro-cognitive models will require developing alternative architectures that preserve the critical hypothesised distinctions between representation and control while retaining the ability of transformers to learn from large-scale ecologically realistic corpora of language and images. In the meantime, small-scale simulations like those reported here provide some critical insights into aspects of architecture and maturation that may aid in this endeavour. We have added the following text to note the importance of future work to assess the scalability of the findings:

      “Thus, anatomy and maturational delay can conspire to promote fast learning with good conceptual abstraction, with the maturational delay allowing the full network to lay down base representations that approximate the cross-context structure of the environment before control begins to shape behaviour and control interfacing at an intermediate part of the semantic representation network leaving the multimodal hub relatively insulated from control. The current analyses demonstrate this in the context of a relatively simple model environment, allowing explicit assessment of representation quality. Again, future work should assess the scalability of such assessments to the complexity of a real-world environment and the impact of selecting different features within the same versus different modalities.”

      “The model environment is the same as in Jackson et al., (2021), designed to assess how well each model layer can encode cross-modal similarity structure through conceptual abstraction across sensory modalities and contexts. It includes 16 concepts, each possessing a unique activation pattern across 12 feature units in each of the 3 modality-specific information channels (see Figure 1. B). While this environment is relatively simple, it allows us to be explicit about the nature of the structure within and across modality-specific spoke regions.”

      (2) The simulations indicate that extremely long delays in introducing control (e.g., half or more of training epochs) degrade conceptual abstraction. The authors briefly note that real children presumably do develop partial top-down influences earlier. It may be interesting to connect more explicitly: Is there a "critical window" or sweet spot for introducing control signals in actual human development? The authors hint at a 2-3 year timeframe, but more commentary on how to map the model's "epochs" to chronological age might help interpretation.

      We agree that it would be of great interest to be able to provide more information on the timing of semantic control development in children based on the model, and we have added further text considering this question. The current assessment shows that a period without control approaching half of total learning time appears optimal for the model. Direct translation is difficult, in part because there is no equivalent point at which humans are finished learning semantic representations. However, this would likely constitute years of a child’s life. This is high compatible with the behavioural evidence for semantic control developing between 3 and 6 years old. However, more precise mapping between an epoch and a year is nontrivial. Moreover, we do not simply demonstrate a plateau in the training time improvements. Instead, we suggest that the optimal developmental delay in gaining semantic control processes will require a balance as extremely long delays may impact the quality of the representations, yet learning will be faster. The optimal point in this balance may well constitute a ‘sweet spot’, however its timing will depend on the costs and benefits of faster vs. better learning. The relative importance of these factors will likely depend on the nature of the representations learnt and the environment the child is in (e.g., the likelihood of errors leading to serious danger). Of course, these factors are not estimable based on the model. Moreover, this would depend on the information learnt, necessitating a more realistic training set. Thus, the exact timings should be based on behavioural assessment of children and not modelling predictions. However, we agree this is an important consideration for the Discussion and that the overall evidence of a substantial period of time without control demands is highly compatible with the meta-analysis results.

      We have added further consideration of this relationship to the Discussion text:

      “While it may seem tempting to consider what the simulations suggest about the optimal length of delayed semantic control in cognitive development, several factors make the extrapolation non-trivial. One important limiting factor is the nature of the model training environment, which sacrifices ecological validity in favour of the strict control that allows us to measure conceptual coherence and speed of learning. The results make it clear that later development of semantic control is beneficial overall, but connecting this observation to real developmental trajectories will require models with richer and more realistic training corpora such as those recently studied by Giallanza et al. (2025) in related work. It will also require better assessment tools for tracking the true developmental profile of semantic control from ages 2-10, and for differentiating this profile from executive function more broadly.”

      (3) In Part 1, the hub-and-spoke model seems naturally suited to capturing taxonomic relationships, because its feature-based architecture highlights shared attributes among items. However, in the subsequent meta-analysis, the authors pool studies of both taxonomic and thematic associations without always distinguishing them. Thematic relationships (e.g., horse-saddle) typically rely on more contextual or event-based links, which may not be as easily represented by the same feature sets that drive taxonomic structure. I'd like to hear the authors discuss whether their model and analysis can adequately distinguish these two relationship types-particularly since one relies on overlapping features (taxonomic) and the other on spatiotemporal co-occurrence (thematic).

      We thank the reviewer for highlighting the lack of clarity provided on the relationship between the taxonomic and thematic relationships considered in the behavioural meta-analysis and the models. Both the model and the meta-analysis focus on the same mechanism, the controlled selection of task-appropriate features and associations. In the case of the meta-analysis, this was the features and associations needed to identify the taxonomic or the thematic relationships. While thematic relationships may be initially learnt based on a differing mechanism (spatiotemporal co-occurrence), they may be instantiated in a similar way to taxonomic relationships, i.e., being detectable through feature overlap. This is because features may include aspects such as being found in a particular context, e.g., the kitchen or Halloween, which would consequently overlap between two concepts (dish and spatula, bat and pumpkin). Indeed, models of language-based co-occurrence still rely on ‘feature’ overlap between concepts in a multidimensional space, it is simply that these features are the likelihood of the word occurring with different words or in different contexts (e.g., Binder et al., 2016). Similarly, a recent paper demonstrated a shared feature-based representational space for event and object concepts (Tong et al., 2025). This is also highly compatible with a) how thematic relationships and word co-occurrence have been treated in prior models of semantic control (e.g., Hoffman et al., 2020), and b) the evidence that both thematic and taxonomic relationship rely on the anterior temporal lobe hub (although it is not contingent on their reliance on the exact same neural correlates). While only a hypothesis, this is an efficient explanation for how these two relationship types can work together within a single system and why it is the ability to follow the task instructions and not the presence of thematic vs. taxonomic relationships that dictates whether a child can correctly perform these judgements. Our analyses did allow us to test thematic and taxonomic representations at each stage and we found both were significantly above chance from 3 years on, and neither were at 2 years old. If we had found that there were ages at which children have thematic but not taxonomic relationships (or vice versa), we would have considered the task-sensitivity within this context. This was not however the case.

      We have added a clarification of the relationship between the representation of taxonomic and thematic structures to the text:

      “In high control studies all trials have both a thematic and taxonomic match, but the instructional context indicates which kind of information should drive the selection. These trials thus require both the relevant semantic knowledge and the ability to select the correct kind of information for the task.”

      Note that taxonomic and thematic relationships are encoded by different varieties of environmental structure—for instance, dogs, wolves and foxes are similar by virtue of shared parts, behaviours, and appearances, but dogs, bones, and leads are similar by virtue of common co-occurrences with one another and with other contextual cues (e.g., Binder et al., 2016). Consequently, selecting the taxonomic versus thematic relationships relies upon selecting some set of relevant features and inhibiting a different set of irrelevant features, whether these are represented in the same or different brain areas. This is the same operation performed by the computational models in Part 1.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      This study investigates the role of site-specific DNA methylation changes during spermatogenesis and their contribution to paternal epigenetic inheritance. Using MethylCap-seq, the authors identify a transient, site-specific loss of DNA methylation at transcription start sites (TSSs) of late spermatogenesis genes during the transition from differentiating spermatogonia (KIT+) to pachytene spermatocytes (PS). This demethylation event correlates with the gain of H3K4me3, which presets nucleosome retention sites in mouse sperm. The study proposes that selective loss of DNA methylation at a subset of promoters is required for nucleosome retention and the establishment of epigenetic states that may influence embryonic gene regulation. These findings provide complementary insights to earlier work by the Peters lab, "DNA methylation modulates nucleosome retention in sperm and H3K4 methylation deposition in early mouse embryos."

      Overall, the study presents a valuable dataset; however, additional analyses could strengthen the conclusions and provide further mechanistic insights.

      Major Comments:

      (1) Prior work should be acknowledged and used for comparative analysis. A key proposal in this study is that regions undergoing DNA methylation loss retain histones, influencing the zygote's epigenetic landscape. However, previous studies (e.g., Peters et al.) have shown that regions losing methylation in DNMT3a/b knockout (KO) mice do not necessarily retain histones, suggesting additional factors are involved. Moreover, Peters et al. demonstrated that regions of low DNA methylation in sperm render paternal alleles permissive for H3K4me3 establishment in early embryos, independent of the paternal inheritance of sperm-borne H3K4me3. Comparing these findings would refine the model presented in this study.

      We agree that the study by Fanourgakis et al. provides important evidence that DNA methylation modulates nucleosome retention in sperm and the establishment of H3K4me3 on paternal alleles in early embryos. Importantly, their study showed that embryonic H3K4me3 establishment can occur independently of the direct inheritance of sperm-borne H3K4me3.

      Our study addresses a complementary question: when the hypomethylated regions associated with sperm nucleosome retention are established during normal spermatogenesis. We have expanded the Discussion to compare the two studies and clarify that site-specific demethylation during the mitosis-to-meiosis transition may contribute to the establishment of these sperm epigenetic states. We also now emphasize that not all demethylated regions exhibit strong nucleosome retention, indicating that DNA demethylation alone is insufficient and that additional chromatin features contribute to nucleosome retention.

      (2) Figure 2A: The data suggest an increase in methylation peaks in PS cells. How does this align with the hypomethylation observed in Figure 1D? Reconciling these observations would improve clarity.

      We agree that the relationship between the global reduction in 5mC observed in Figure 1 and the regional methylation changes detected by MethylCap-seq required clarification.

      Additional immunostaining confirmed strong 5mC signals in KIT-positive spermatogonia, STRA8-positive preleptotene spermatocytes, and DMC1-positive leptotene spermatocytes, but markedly reduced signals in pachytene spermatocytes (new Figure S1).

      We also clarified that ELISA and immunostaining measure global 5mC abundance, whereas our MethylCap-seq analysis detects regional methylation enrichment primarily within uniquely mappable genomic regions. Thus, methylation changes in repetitive sequences, which constitute a substantial portion of the genome, are not fully captured by this analysis, and the number of stage-specific peaks does not directly reflect total genomic 5mC. The Results and Discussion have been revised accordingly.

      (3) Figure 4A: The effect size of demethylation on nucleosome retention is unclear - do all demethylated promoters retain histones or only a subset? Quantifying this would clarify whether DNA methylation loss consistently predicts nucleosome retention.

      To quantify this relationship, we divided 1,225 promoter-associated demethylated peaks into four groups according to the magnitude of demethylation and compared sperm mononucleosome enrichment among the groups. Mononucleosome enrichment increased significantly across groups with greater demethylation (Jonckheere–Terpstra test, P = 1.1 × 10<sup>-10</sub>). Analysis of the continuous values also revealed a modest positive correlation between demethylation and mononucleosome enrichment (Spearman’s ρ = 0.192, P = 1.31 × 10<sup>-11</sup>).

      However, substantial variability was observed among individual regions, indicating that not all demethylated promoters exhibit strong nucleosome retention. We therefore conclude that promoter demethylation is quantitatively associated with nucleosome enrichment but is not sufficient to determine nucleosome retention. These analyses have been added as new Figure S4, and the Results and Discussion have been revised accordingly.

      (4) Prior studies have generated bisulfite sequencing data from Tet KO sperm. Do the regions that undergo demethylation during the KIT+ to PS transition overlap with those misregulated in TET KO sperm? Integrating this comparison could provide further insight into the regulation of site-specific demethylation.

      To address this point, we compared our Class I regions, which undergo demethylation during the KIT-positive spermatogonia-to-pachytene spermatocyte transition, with the TET1-dependent sperm hypomethylated regions identified from whole-genome bisulfite sequencing of TET1-knockout sperm by Prasasya et al. (Prasasya et al., 2024). Only limited overlap was observed between the two datasets (new Figure S5).

      We have added this analysis to the Results and revised the Discussion to clarify that most regions identified in our study do not correspond to the previously defined TET1-dependent sperm hypomethylated regions. Although differences in developmental stage and analytical approach should be considered, these findings suggest that additional mechanisms, potentially involving other TET family members or incomplete maintenance methylation during premeiotic DNA replication, may contribute to the demethylation observed in our study.

      (5) The role of SCML2 enrichment in germline stem cells and its connection to H3K27me3 deposition in later germ cells is unclear. Earlier figures show that regions undergoing DNA demethylation from KIT+ to PS include genes expressed in later-stage germ cells. 

      Why is SCML2 enrichment occurring in germline stem cells (GSCs)? Why is H3K27me3 only acquired at later stages if SCML2 is already present? Is SCML2 preventing premature expression independent of K27ME? 

      Showing the dynamics of H3K27me3 and SCML2 across these stages would clarify the proposed conclusions.

      Previous studies from our group demonstrated that SCML2 is highly expressed in undifferentiated spermatogonia and associates with hypomethylated promoters at this stage (Hasegawa et al., 2015). Thus, SCML2 enrichment in germline stem and progenitor cells reflects its preferential association with hypomethylated promoter regions.

      H3K27me3 is acquired later because SCML2 occupancy and PRC2-mediated H3K27me3 deposition are temporally separated. SCML2 is already present at these regions in spermatogonia, whereas PRC2-dependent H3K27me3 accumulates predominantly after meiotic entry (Hasegawa et al., 2015; Maezawa et al., 2018). SCML2 may therefore mark regions that subsequently acquire H3K27me3 during meiotic progression.

      The late spermatogenesis genes identified in the earlier analyses are not necessarily direct SCML2 target genes, and our data do not support the conclusion that SCML2 prevents their premature expression independently of H3K27me3. We have therefore not extended our interpretation in this direction.

      We have revised the Discussion and added citations to previous studies that established the stage-specific dynamics of SCML2 occupancy and H3K27me3 deposition. Because these dynamics have already been characterized, we clarified their temporal relationship using the published data rather than repeating the analyses in the present study.

      Reviewer #2 (Public review):

      Summary:

      This study profiles the genome-wide distribution of DNA methylation using methylation capture sequencing in four stages of male germ cells: Thy1+ (undifferentiated spermatogonia), Kit+ (differentiated spermatogonia), pachytene spermatocytes, and round spermatids. These analyses revealed site-specific loss of DNA methylation in pachytene cells compared with differentiating spermatogonia. Integrated analysis using published datasets indicates that hypomethylated sites correlate with nucleosome retention sites and bivalent histone methylation sites in sperm.

      Strengths:

      The methyl-seq approach provides a comprehensive profile of DNA methylation in male germ cells. The concept that DNA hypomethylation in meiotic cells precedes histone modification and histone retention in sperm is interesting.

      Weaknesses:

      (1) In the title, the word "presets" should be changed to "precedes" or "correlates with". Preset means a causal relationship, which is not the case. This needs to be changed throughout the manuscript. For example, in the abstract, "predetermine" needs to be changed to "precede".

      We agree that our data demonstrate a temporal association rather than a direct causal relationship between site-specific DNA demethylation and nucleosome retention. We therefore revised the title to “Site-specific DNA demethylation during spermatogenesis precedes nucleosome retention in mouse sperm” and replaced terms such as “preset” and “predetermine” throughout the manuscript with “precede” or other appropriately descriptive expressions. We also revised the Discussion to clarify that DNA demethylation may contribute to, but does not independently determine, nucleosome retention in sperm.

      (2) The statement that "Based on these results, we propose that meiosis is a process of epigenetic reprogramming that sets up embryonic gene regulation" (lines 94-95) is a speculation that in the opinion of this reviewer should be removed from the text. It is too broad and not supported by the data presented.

      We agree that the original statement was broader than what is directly supported by our data. We have therefore revised the text to avoid implying that meiosis globally establishes embryonic gene regulation. The revised text now states: “Our findings suggest that meiotic DNA demethylation contributes to the establishment of sperm epigenetic states associated with embryonic gene expression.”

      (3) Figure 1B: details are missing. How many cells were analyzed/used? How many times was this experiment done [(The number of experiments, (n)]? Were the changes statistically significant (Lines 109-111)

      We have revised the Materials and Methods and Figure 1 legend to specify the number of cells used for DNA extraction, the amount of genomic DNA analyzed, the number of biological replicates, and the statistical analysis. The overall difference among the four populations was significant by one-way ANOVA, and the results of Tukey’s multiple-comparison test are now indicated in Figure 1B.

      (4) Figure 1A and Figure 1D: These seem to be contradictory. According to Figure 1D, leptotene/zygotene spermatocytes show bright 5mC staining. However, the diagram in 1A shows delayed recovery of DNA methylation. The authors should clarify this. It appears that 5mC was high in Kit+ spermatogonia and leptotene/zygotene spermatocytes, and then decreased in pachytene spermatocytes.

      We agree that the schematic in Figure 1A required clarification. Figure 1A summarizes the previously reported delay in maintenance methylation following premeiotic DNA replication, which results in transient hemimethylation (Gaysinskaya et al., 2018). In contrast, Figure 1D shows overall 5mC signals measured by immunostaining.

      We revised Figure 1A, its legend, and the Results to clarify this distinction. Additional immunostaining showed strong 5mC signals in KIT-positive spermatogonia, STRA8-positive preleptotene spermatocytes, and DMC1-positive leptotene spermatocytes, followed by reduced signals in pachytene spermatocytes (new Supplementary Figure S1). Thus, the two panels reflect different aspects of DNA methylation dynamics and are not contradictory.

      (5) L121-122: Statement: These results suggest that 5mC levels change dynamically during spermatogenesis before and after the transient reduction of DNA methylation in the premeiotic S phase. In order to make this claim about the premeiotic S phase, I suggest performing 5mC staining in premeiotic S phase cells, which can be pulse-labelled with BrdU or cite a reference if available.

      We agree that additional evidence defining the timing of 5mC dynamics around meiotic entry would strengthen our conclusion. To address this point, we performed additional immunofluorescence analyses using stage-specific markers. Strong 5mC signals were observed in KIT-positive differentiating spermatogonia, STRA8-positive preleptotene spermatocytes, and DMC1-positive leptotene spermatocytes, whereas γH2AX-positive pachytene spermatocytes exhibited markedly reduced 5mC staining (new Figure S1). These results indicate that the reduction in overall 5mC signals becomes evident between the leptotene and pachytene stages. We revised the Results accordingly and now state that 5mC levels change dynamically during spermatogonial differentiation and meiotic progression, without assigning the reduction to a precise point within premeiotic S phase.

      Recommendations for the authors:

      Reviewing Editor comments:

      One major issue brought up during the review was that the present study provides complementary insights to a recently published work by the Peters lab, "DNA methylation modulates nucleosome retention in sperm and H3K4 methylation deposition in early mouse embryos.", thus it is advisable that their findings are incorporated into the discussion. The Peters lab's publication does not undermine the present work, and the authors do not necessarily have to perform all the experiments suggested by reviewers. Still, it is important to place the findings in the context of current knowledge of the field.

      We have revised the Discussion to incorporate the findings of Fanourgakis et al. and to clarify how our study complements their work. Specifically, we now discuss their evidence that DNA hypomethylation promotes nucleosome retention in sperm and permits H3K4me3 establishment on paternal alleles in early embryos. We also clarify that our study addresses when these hypomethylated regions emerge during normal spermatogenesis and emphasize that DNA demethylation is associated with, but is not sufficient to determine, nucleosome retention.

      Reviewer #1 (Recommendations for the authors):

      Minor Comments:

      (1) Figure 1: The authors use PLZF and ZBTB16 interchangeably. Consistently using one term throughout the manuscript would improve clarity.

      To improve consistency, we have standardized the nomenclature and now refer to this marker as ZBTB16 throughout the manuscript

      (2) Figure 1C: The logic in describing differentiating spermatogonia as "PLZF-negative" is somewhat indirect. Instead, it may be clearer to use a positive marker (e.g., c-KIT) to define differentiating spermatogonia and show that these cells exhibit increased 5mC levels.

      We agree that c-KIT is a clearer positive marker for differentiating spermatogonia. We therefore performed additional immunofluorescence analysis using c-KIT and 5mC. KIT-positive differentiating spermatogonia exhibited strong nuclear 5mC staining (new Figure S1A), consistent with our original observations and with the previous report that DNA methylation increases in c-KIT-positive differentiating spermatogonia (Shirakawa et al., 2013). We have incorporated these data into the revised Results and cited Shirakawa et al.

      (3) Figure 1D: Ideally, this figure would include co-staining with three antibodies: one marking leptotene/zygotene (L/Z) spermatocytes, one marking pachytene spermatocytes, and one for 5mC. Currently, the study relies on DAPI to distinguish L/Z spermatocytes, which may be insufficient. Additionally, the reduction in 5mC should be monitored specifically from the L/Z to the pachytene stage of spermatocytes.

      We agree that stage-specific markers provide a more reliable assessment of DNA methylation dynamics during meiotic progression than identification based solely on DAPI staining. We therefore performed additional immunofluorescence analyses using STRA8 and DMC1 as markers of preleptotene and leptotene spermatocytes, respectively, and γH2AX to identify pachytene spermatocytes (new Figure S1). STRA8-positive and DMC1-positive spermatocytes exhibited strong nuclear 5mC staining, whereas γH2AX-positive pachytene spermatocytes showed markedly reduced 5mC signals. These experiments directly demonstrate a reduction in overall 5mC signals between the early meiotic and pachytene stages. The Results section has been revised accordingly.

      (4) In Figure 2A: The distinction between common and unique peaks is informative, but in addition to stacked bar plots, providing a supplemental table and a heatmap summarizing these loci would improve visualization of stage-specific changes.

      To facilitate interpretation and reuse of the dataset, we have added Supplementary Table 1 containing the complete lists of common and stage-specific (unique) MethylCap-seq peaks identified in each comparison, together with their genomic annotations. We did not add a separate heatmap because the stage-specific methylation changes are already summarized in Figure 2A, illustrated by representative genome browser views in Figure 2B, and further characterized in the subsequent analyses. The complete peak lists provide a complementary resource without duplicating the existing visualizations.

      Reviewer #2 (Recommendations for the authors):

      (1) L163: The section title "DNA demethylation at TSSs correlates with the activation of late spermatogenesis genes" is the same as the last sentence from the preceding section "These results suggest that DNA demethylation at TSSs is associated with activation of late spermatogenesis genes at the KIT+ to PS transition." Figure 2C logically belongs to Figure 3. Suggestion: Move Figure 2C to Figure 3.

      We agree that Figure 2C is closely related to the promoter-focused analyses in Figure 3. However, we have retained it in Figure 2 because it summarizes the initial genome-wide observation that DNA demethylation is preferentially associated with late spermatogenesis genes and provides the rationale for the more detailed promoter analyses that follow. To avoid redundancy, we revised the final sentence of the preceding section and changed the next section title to “Promoter demethylation accompanies activation of late spermatogenesis genes.”

      (2)-1 Figures 5A, 5B: mononucleosome enrichment and H3.3 enrichment in class I do not appear obvious to me. Is it possible to quantify or do a statistical analysis of the level of enrichment?

      Class I and Class II regions were defined according to the magnitude of DNA demethylation (Class I, log₂ fold change < −5; Class II, log₂ fold change ≥ −5), rather than according to mononucleosome or H3.3 enrichment. The corresponding regions are provided in Supplementary Table 4. 

      Figures 5A and 5B show aggregate enrichment profiles across all regions in each class. We agree that the difference is not readily apparent from the heatmaps alone. We therefore revised the text to avoid implying that enrichment was used to define the two classes and to clarify that the profiles indicate a greater overall tendency toward mononucleosome and H3.3 enrichment in Class I regions. Figure 5C separately examines the relationship between mononucleosome and H3.3 enrichment within Class I regions.

      (2)-2 Figures 2C, 3C, 3D, S2A, S2B: Please provide the list of genes in each category in spreadsheets preferably with their MethylCap-seq data or expression data.

      The gene set used in Figure 2C was previously reported in Maezawa et al. (2018). We have added Supplementary Table 2 containing the gene lists used for the GO analysis in Figure 3C and the corresponding RNA-seq expression values used for the heatmap in Figure 3D, and Supplementary Table 3 containing the gene lists and expression data used in Figures S3A and S3B. Together with the additional data provided in response to Reviewer 1, we have added four supplementary tables: common and unique MethylCap-seq peaks (Table S1), differentially methylated TSSs and associated expression data (Table S2), single-exon genes and expression data (Table S3), and Class I and Class II loci (Table S4).

      Table S1. Common and transition-specific MethylCap-seq peaks identified across all spermatogenic transitions (Fig. 2A)

      Table S2. Differentially methylated transcription start sites and associated gene expression data (Fig. 3B–D)

      Table S3. Single-exon genes and associated gene expression data (Fig. S3A, B)

      Table S4. Class I and Class II loci defined by the extent of DNA demethylation (Fig. 5)

      (2) Line 77: Change "After the postnatal stage" to "At the postnatal stage".

      Done

      (3) Line 135: Change "THY+" to "THY1+".

      Done

      (4) Line 213: Change "overserved" to "observed".

      Done

      (5) Line 219: Change H4K4me3 to H3K4me3.

      Done

    1. Author response:

      The following is the authors’ response to the original reviews.

      eLife Assessment:

      The study presents a useful computational analysis of how the ratio between excitatory and inhibitory neural numbers affects coding capacity. The authors show that increasing the proportion of inhibitory neurons (as observed in upper cortical layers compared to the input recipient layer 4) increases the dimensionality of neural activity and improves the encoding of time-varying stimuli. However, the evidence about the role of the inhibitory population in coding is incomplete because numerical results are neither supported by analytical mathematical results nor include controls for changes in firing thresholds or subtypes of inhibitory neurons.

      We thank the editor for this assessment. We addressed both points raised here in the manuscript explicitly. With regard to the analytical results, we explain below that in this case, it would not add much to the existing thorough results by Ostojic et al. (2014) [1], as we observe no state transitions. We have explained this explicitly in the Methods section. With regard to the subtypes of inhibitory neurons, we recognize that while the effects of E/I ratio changes offer new insights, our comparison has inherent limitations. W e recognize that incorporating more detailed features, such as inhibitory cell subclasses (SOM, VIP, PV), synapse-specific differences, realistic population sizes, and inter-layer connectivity are essential for a more comprehensive understanding, and we addressed this in the discussion. We consider this work a foundation for subsequent investigations that will build upon these findings, and trust that we have clarified this with our revisions.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      The authors seek to understand the role of different ratios of excitatory to inhibitory (EI) neurons, which in experimental studies of the cerebral cortex have been shown to range from 4 to 9. They do this through a simulation study of sparsely connected networks of excitatory and inhibitory neurons.

      Their main finding is that the participation ratio and decoding accuracy increase as the E/I ratio decreases. This suggests higher computational complexity.

      This is the start of an interesting computational study. However, there is no analysis to explain the numerical results, although there is a long literature of reduced models for randomly connected neural networks which could potentially be applied here. (For example, it seems that the authors could derive a mean field expression for the expected firing rate and variance - hence CV - which could be used to target points in parameter space (vs. repeated simulation in Figures 1,2).) The paper would be stronger and more impactful if this was attempted.

      Strengths:

      Some issues I appreciated are:

      (1) The use of a publicly available simulator (Brian), which helps reproducibility. I would also request that the authors supply submission or configuration scripts (if applicable, I don't know Brian).

      Good point, we have now included the Python simulation scripts detailing their use in the data directory to enhance reproducibility.

      (2) A thorough exploration of the parameter space of interest (shown in Figure 2).

      (3) A good motivation for the underlying question: other things being equal, how does the E/I ratio impact computational capacity?

      Weaknesses:

      (1) Lack of mathematical analysis of the network model

      Thank you for highlighting this point. We would like to clarify that our network model is based on the framework established by Ostojic et al. (2014) [1]. In their seminal work, they utilized mean-field theory to rigorously analyze the network dynamics. Specifically, their network parameters included N<sub>ext</sub> = 10,000, N<sub>inh</sub> = 2,500, j<sub>ei</sub> = 0.1 mV, g = 5, and an inhibitory threshold of 20 mV, maintaining a balanced state.

      Our initial model state closely aligns with the configuration of Ostojic et al. (2014) [1]. We do not observe state transitions in our work, and hence an analytical analysis into such state transitions would not add much here. The observed increases or decreases in computational capacity and dimensionality are within the inhibition-dominated balanced state. Therefore, we decided not to repeat the mathematical analysis already thoroughly addressed in the Ostojic et al. [1] study and instead focused our efforts on evaluating how the excitatory-inhibitory (EI) ratio influences the network's coding capacity. Furthermore, we would like to emphasize that a purely mathematical analysis might not sufficiently capture the functional role of different inhibitory populations in neural coding, a point you also raised in your assessment summary. We have added a paragraph to the methods to clarify this.

      Major issues I recommend that the authors address (not sure whether these are "weaknesses"):

      (1) In "Coding capacity in different layers of visual cortex" the authors measure PR values from layers 2/3 and 4 in VISp and find that layer 2/3 has a higher PR than layer 4.

      But in Dahmen et al. 2020 (https://doi.org/10.1101/2020.11.02.365072), the opposite was found (see Figure 2d of Dahmen et al.): layer 2 had a lower PR than layer 4. Can the authors explain how that difference might arise? i.e. were they analyzing the same data sets? If so why the different results? Could it have to do with the way the authors subsample for the E/I ratio?

      From the Methods of that paper: "Visual stimuli were generated using scripts based on PsychoPy and followed one of two stimulus sequences ("brain observatory 1.1" and "functional connectivity"). We focused on spontaneous neural activity registered while the animal was not performing any task. In each session, the spontaneous activity condition lasted 30 minutes while the animal was in front of a screen of mean grey luminance. We, therefore, analyzed 26 of the original 58 sessions corresponding to the "functional connectivity" subdataset as they included such a period of spontaneous activity. " This suggests to me they may have analyzed recordings with the other stimulus sequence; however, the hypothesis that E/I ratio should modulate dimensionality would not seem to "care" about which stimulus sequence was used.

      We appreciate the reviewer's comment regarding the differences in data analysis. As noted, our approach diverged from Dahmen et al. (2020) [2] in several key aspects. We focused exclusively on the 'brain observatory 1.1' stimulus sequence, specifically analyzing the primary visual cortex (VISp) response to 'natural images'. In contrast, Dahmen et al. (2020) [2] examined 'functional connectivity' sequences, calculating participation ratios across the spontaneous activity. Furthermore, to align our excitatory/inhibitory (EI) ratios with those of the barrel cortex used in our stimulation paradigm (7.4 for layer 4 , 5.32 for layer 2 /3), we subsampled excitatory and inhibitory neurons from VISp layers 2/3 and 4. This contrasts with Dahmen et al. (2020) [2] , who included all neurons from these layers. These methodological differences likely contribute to the observed discrepancies in participation ratios between layers 2/3 and 4.

      Based on the findings of Adesnik (2018) [3] , it is reasonable to conclude that neurons in Layer 2/3 (L2/3) of the mouse‘s primary visual cortex are likely to exhibit more diverse or higher-dimensional activity than those in Layer 4 (L4), and this is at least partly due to stronger recurrent inhibition within L2/3. The study showed that during optogenetically induced gamma oscillations, the balance of excitation and inhibition (E/I ratio) in L2/3 was significantly more tilted toward inhibition (E/I ≈ 0.18) compared to L4 (E/I ≈ 0.27), indicating that L2/3 circuits are under tighter inhibitory control. This strong local inhibition suppresses redundant or correlated activity, enabling more selective and sparse firing patterns, which in turn can increase the dimensionality of population activity. Moreover, L2/3 plays a distinct integrative role in cortical processing: it receives inputs not only from L4 but also from other cortical areas and sends outputs mainly to L5, positioning it as a key hub for complex intracortical computation. This contrasts with L4, which acts more as a feedforward layer receiving thalamic sensory input and distributing it to other layers with more uniform excitatory output and less specialized activity. The study suggests that the strong inhibition observed in L2/3 contributes to an inhibition-stabilized regime that enables nonlinear gain control, contextual modulation, and flexible computation—features associated with high-dimensional, heterogeneous neural representations. Therefore, the combination of stronger inhibition, integrative connectivity, and computational function supports the idea that L2/3 neurons exhibit more diverse activity patterns than those in L4.

      We added these comparisons to the Discussion section.

      (2) In Discussion (pg. 20, line 383): "They showed that brain regions closer to sensory input, like the thalamus, have higher dimensionality than those further away, such as the visual cortex. " How is this consistent with the hypothesis that "higher dimensionality might be linked to more complex cognitive functions"?

      We appreciate the reviewer pointing out this error. The corrected statement now reads: 'They showed that brain regions closer to sensory input, such as the thalamus, have a lower dimensionality than those further away, like the visual cortex.

      (3) What is the probability of connection between different populations? e.g. the probability of there being a synaptic connection between any two E cells? I could not find a statement about this. It should be included in the Methods.

      Apologies for not making this sufficiently clear. So far, the ratio had been mentioned in the results, but we have also added it now in the Methods.

      (4) pg. 27, line 540: "Synchronicity within the network" For each cell pair, the authors use the maximum cross-correlation over time lag. I don't think I have seen this before. Can the authors explain why they use this measurement, vs (a) integrated cross-correlation or (b) cross-correlation at some time scale? Also, it seems like this fails to account for neuron pairs for which there is a strong inhibitory correlation.

      Thank you for bringing up this question. The choice of correlation method was motivated by the possibility of lags in the co-activation between neurons and therefore we did not want to focus on a 0-lag measure. In reality, the delay of the peak in the cross-correlation relative to 0-lag was only 3 ms +/- 3 ms. We therefore think that other measures would have delivered very comparable results. We did not use an integrated measure, because we were worried that this would 'wash out' the results, if there is an overall high level of correlation, which would overwhelm the peak correlation. Also, using an integrated measure immediately required defining a range over which to integrate, which seems arbitrary and could contribute to overwhelming the peak correlation. If one had used a sum over a small time-window in the cross-correlation, we think a very similar result would have been obtained, as the cross-correlograms were generally 'well behaved', i.e. symmetric around their peak.

      Regarding the inhibitory correlations: we are a bit confused about what the reviewer refers to. Two possible interpretations are: (i) correlations between inhibitory neurons, or (ii) negative correlations between neurons (be they excitatory or inhibitory).

      For the first option, these have been measured with our approach, by computing correlations between neurons including inhibitory neurons (Figure 3C). For the second option, these have not and should not contribute (positively) to the synchrony in the network. Therefore, unless we are missing an interpretation, we think that these cases are appropriately covered by our correlation measure.

      We would also like to note that negative correlations are typically rare in these networks, which we document in Author response image 1 with a graph of the distribution of correlations over all neurons in the network in different network realisation:

      Author response image 1.

      Cross-correlation between all neuron pairs in different network realizations for the following parameters: the number of inhibitory neurons N<sub>inh</sub> is between 2500 and 1000, and consequently the EI ratio is between 4 and 10, J<sub>ei</sub> between -0.75 mV and -0.5 mV, and θ<sub>inh</sub> = 18,18.5,19,19.5, and 20 mV.

      (5) "When stimulated, a time-varying input, μ<sub>ext</sub> (t), is applied to 2,000 randomly selected excitatory neurons. " I would guess that computing PR would depend on the overlap of the 500 neurons analyzed and this population. Do the authors check or control for that?

      (5b) Related: to clarify, are the 500 neurons chosen from the analysis equally likely to be E or I neurons?

      The reviewer's insightful comment regarding the potential impact of the overlap between stimulated and analyzed neuron populations on participation ratio (PR) is appreciated. We recognize that the direct external input can synchronize neurons and affect the PR. To eliminate this confounding factor, we implemented a strict selection process: after randomly selecting 2,000 neurons to receive input, we chose the 500 neurons for PR analysis, respecting the EI ratio exclusively from both inhibitory and remaining excitatory neurons. This guarantees no overlap between the stimulated and analyzed populations. We have now detailed this procedure in the methods section.

      Reviewer #2 (Public review):

      Summary:

      Alizadeh et al. investigate how varying cellular E/I (excitatory/inhibitory) composition impacts coding across cortical layers. They build on findings from a recent study (Huang et al., 2022) that demonstrated a decrease in the fraction of inhibitory neurons from L2/3 to L4. Using a network of excitatory and inhibitory leaky integrate-and-fire neurons, they systematically assess how these anatomical features influence the dimensionality of network activity and coding capacity. Their key finding is that increasing the proportion of inhibitory neurons enhances the dimensionality of activity and improves the encoding of time-varying stimuli.

      Strengths:

      The authors use a clear methodology and well-established model of network activity that allows them to relate network parameters to the coding properties. They systematically evaluate the impact of the key features of the inhibitory population. Thus, in addition to changing the fraction of inhibitory cells, they control for the inhibitory firing threshold of inhibitory neurons and connection strength between inhibitory and excitatory cells. Furthermore, they show their modeling results are aligned with the analysis of the spiking activity in L2/3 vs. L4 from the Allen Institute data.

      Weaknesses:

      One general shortcoming of this approach is that it focuses on a small preselected number of network features. For example, it is unclear to what extent the results would be affected by other aspects of the organization of cortical columns, such as subclasses of inhibitory cells (SOM, VIP, PV), specific differences in synapses, realistic population sizes, or even connectivity between layers. Similarly, the models of L2/3 and L4 are constrained based on a limited set of observations, and it has not been demonstrated whether the same findings hold true for V1 recordings analyzed by the authors.

      We appreciate the reviewer's valid point regarding the focus on a limited set of network features. We acknowledge that our model, while providing valuable insights into the influence of the EI ratio on layer-specific dynamics, simplifies the complex organization of cortical columns. As the reviewer notes, factors such as inhibitory cell subclasses (SOM, VIP, PV), synapse-specific differences, realistic population sizes, and inter-layer connectivity are important and could potentially influence the results.

      This study represents an initial exploration of the E/I ratio's role in layer-specific function, and we aimed to create a simplified, interpretable model as a starting point. By focusing on a randomly connected network with realistic E/I ratios derived from our previous experimental work [4] , we were able to demonstrate that our model captures key aspects of cortical dynamics, as evidenced by comparisons with VISp recordings in terms of participation ratio and decoding capacity.

      We recognize that future studies incorporating more detailed features, such as those mentioned by the reviewer, are essential for a more comprehensive understanding. We consider this work a foundation for subsequent investigations that will build upon these findings and address the limitations acknowledged. We are currently exploring methods to incorporate some of the suggested features into our models, and we believe that expanding the model's complexity will allow for more detailed comparisons with experimental data, including VISp recordings. We have added these considerations to the discussion section.

      The modelling relies on anatomical data from the barrel cortex, but the decoding comparison is based on V1 data. This raises questions about how anatomical differences between regions may influence the conclusions.

      The reviewer's concern about anatomical differences between barrel cortex and V1 (VISp) is valid. While both regions follow general cortical principles, their specific wiring and organization differ substantially, potentially affecting our comparison of a barrel cortex-inspired model with V1 data. We will now elaborate briefly on these key anatomical distinctions in the discussion section of this paper.

      Firstly, they process fundamentally different sensory information: the barrel cortex handles tactile input from whiskers via a direct pathway through the brainstem and VPM thalamus, creating a map of whiskers. In contrast, VISp processes visual information from the retina relayed by the LGN, forming a map of the visual field [5, 6].

      Second, layer 4 in V1 is strikingly different from that of S1 in terms of across-column spatial organization. Barrel cortex L4 features distinct "barrels," each dedicated to a single whisker and with specialized microcircuits. V1's layer 4 is more uniform and lacks these discrete, whisker-specific compartments [5, 7] .

      Third, the types and distributions of interneurons, crucial for local circuit processing, likely vary between these areas to suit their specific sensory processing needs. Similarly, horizontal connections, responsible for integrating information across the cortical surface, have different patterns and functional roles related to tactile versus visual integration [5, 7].

      Finally, the plasticity mechanisms that allow these regions to adapt to experience are also likely tailored to their respective sensory modalities [5, 7].

      Our use of V1 data, due to the absence of a suitable barrel cortex dataset, involved adapting the E/I ratio, a key factor influencing neural activity. The fact that our V1 analysis showed similar dynamics to our barrel cortex model, despite the aforementioned differences, suggests that the E/I balance might be a fundamental constraint on circuit behavior that can lead to similar outcomes despite these anatomical variations.

      However, it is crucial to acknowledge that the unique barrel structure and the processing of tactile information in the barrel cortex are fundamentally different from the more homogeneous structure and visual processing in V1. Therefore, while the E/I ratio comparison offers some insight, it also has inherent limitations. Future research must aim for a direct comparison between our model and barrel cortex data to provide a more definitive validation of our model. Moreover, we recognize that incorporating more detailed features, such as inhibitory cell subclasses (SOM, VIP, PV), synapse-specific differences, realistic population sizes, and inter-layer connectivity are essential for a more comprehensive understanding. We consider this work a foundation for subsequent investigations that will build upon these findings. These considerations have been added to the discussion section.

      The coding capacity appears inversely correlated with the firing rate, which in this study is largely influenced by the properties of the inhibitory population. It would be important to confirm that the observed changes in coding capacity and participation ratio are not solely driven by firing rate changes.

      We appreciate the reviewer’s concern regarding the possibility that the observed changes in coding capacity and participation ratio may be driven solely by variations in firing rate.

      We would like to clarify that in our network model, variations in firing rate are primarily governed by properties of the inhibitory drive—specifically, the inhibitory threshold (θ<sub>inh</sub>), the number of inhibitory neurons (N<sub>inh</sub>), and the synaptic strength from inhibitory to excitatory neurons (J<sub>ei</sub>). To rigorously address this concern, we refer to the simulations shown in Figure 4, where firing rates were held constant at 8 Hz, 4 Hz, and 2 Hz, while other network parameters were systematically varied.

      To isolate the effect of firing rate on coding capacity, we varied the excitatory-inhibitory EI ratio by decreasing the number of inhibitory neurons and simultaneously adjusting θ<sub>inh</sub> and J<sub>ei</sub> to maintain a constant inhibitory drive—thus preserving the overall firing rate across different network configurations.

      As demonstrated in Figure 4, when the number of inhibitory neurons is fixed (e.g., vertical line at N<sub>inh</sub> = 1900) and the firing rate is maintained at 4 Hz (brown lines), reducing θ<sub>inh</sub> (from dark to light lines) requires a corresponding decrease in J<sub>ei</sub> to sustain the same firing rate. Under these conditions, we observe an increase in network dimensionality and coding capacity. This finding indicates that, even when firing rate is held constant, changes in inhibitory parameters can significantly influence network structure and function.

      Together, these results demonstrate that the observed changes in coding capacity and participation ratio are not merely consequences of firing rate differences, but rather reflect the impact of inhibitory dynamics on the population structure of the network.

      We clarified this in section Network coding capacity for realistic cortical EI ratios and discussion.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      Minor issues:

      (1) Pg 23, lines 453-456: "Our spiking neural network incorporates heterogeneities in the coupling strengths between excitatory and inhibitory neurons (J<sub>ei</sub> was varied as an independent variable) and in the inhibitory firing thresholds (the threshold of the inhibitory neurons was varied as an independent variable), but not in other parameters." My customary understanding of "heterogeneity" is that it refers to variation within a system or simulation. But from my reading, Jei is fixed and constant within a simulation. True?

      We appreciate the reviewer's insightful comment regarding the term 'heterogeneity' and the specific parameters in our model. We understand how our previous phrasing caused confusion.

      Our intention was to highlight the difference in magnitude between the excitatory-inhibitory coupling strength (J<sub>ei</sub>) and the other coupling strengths (J<sub>ii</sub> and J<sub>ee</sub>), as well as the difference between the inhibitory and excitatory neuron firing thresholds. We did not intend to imply variability of J<sub>ei</sub> or the inhibitory firing threshold within a single simulation run.

      To clarify, within each simulation, J<sub>ei</sub> and the inhibitory firing threshold (θ<sub>inh</sub>) were held constant. However, we varied these values across different simulations to explore their impact on network dynamics. We now realize that using the term 'heterogeneity' in this way was misleading, as it typically implies variation within a single instance.

      We have revised the relevant section of the manuscript to replace 'heterogeneity' with more precise language, such as 'differences in magnitude' or 'varied parameters across simulations,' to accurately reflect our methodology and avoid further misinterpretations. We will also explicitly state that J<sub>ei</sub> and θ<sub>inh</sub> were constant within each simulation but varied across the set of simulations performed.

      (2) I noticed a few misspellings: pg. 9 line 163, "Wee" instead of "We" (3) Some equations need formatting. For example: in Eqn. (6), parentheses should be resized to fit their contents.

      We corrected these errors.

      Reviewer #2 (Recommendations for the authors):

      Major:

      (1) It may be relevant to control for firing rate while demonstrating that coding improves as a function of the number of inhibitory neurons.

      We appreciate the reviewer’s suggestion that it is important to control for firing rate when demonstrating that coding improves as a function of the number of inhibitory neurons.

      As mentioned in our response to Reviewer 1, we took care in our study to disentangle the effects of inhibitory drive from firing rate by explicitly controlling the firing rate across conditions.

      As detailed in Figure 4, we performed simulations at fixed firing rates (8 Hz, 4 Hz, and 2 Hz), during which we systematically varied the number of inhibitory neurons by adjusting the EI ratio. To maintain a stable firing rate while manipulating inhibitory population size, we jointly adjusted the inhibitory threshold (θ<sub>inh</sub>) and the synaptic strength from inhibitory to excitatory neurons (J<sub>ei</sub>), thereby ensuring a constant inhibitory drive across different EI ratios.

      We observed that, even with a fixed firing rate, changing the inhibitory parameters by θ<sub>inh</sub>, J<sub>ei</sub>, and N<sub>inh</sub> led to a change in network dimensionality and coding capacity. This inverse relationship, observed independently of firing rate changes, demonstrates that inhibitory influence plays a direct role in shaping the population-level dynamics and coding properties of the network.

      We clarified this in sections Network coding capacity for realistic cortical EI ratios and discussion.

      (2) The discussion could benefit from additional justification for the chosen approach and the selection of features. Specifically, it is not entirely clear why these three parameters were deemed the most interesting.

      Thank you for this suggestion. Our selection of parameters is grounded in experimental measurements quantifying cell bodies across six cortical layers of the barrel column [4] . This dataset revealed distinct differences in the EI ratio across layers and areas. For instance, an EI ratio of 5.25 in layer 2/3 and 7.34 in layer 4 (see Figure 1 in the manuscript). Motivated by these findings, we aimed to investigate how layer-specific EI ratios influence the dynamics and computational properties of the corresponding cortical layers.

      To do this, we manipulated the EI ratio in a balanced network model by varying the number of inhibitory neurons. To maintain physiological firing rates across network configurations, we additionally adjusted two parameters:

      First, we changed the firing threshold of inhibitory neurons N<sub>inh</sub> —motivated by evidence showing differences in intrinsic properties between excitatory and inhibitory cortical neurons (see Figure S1 and reference [8]).

      Second, we varied the synaptic strength from inhibitory to excitatory neurons J<sub>ei</sub> —this follows both theoretical work [1, 9] and experimental studies that emphasize the importance of asymmetry in synaptic strengths for maintaining stability and balance in cortical circuits. For example, Xue, et. al (2014) [10] demonstrate how synaptic strength is differentially regulated across cell types to maintain balance, and Isaacson and Scanziani (2011) [11] highlight differences in the timing and strength of excitation-to-inhibition vs. inhibition-to-excitation pathways.

      We added this clarification to the discussion section to better justify our modeling choices and the focus on these specific parameters.

      (3) Are CV or synchrony different in example L2/3 and L4 networks? How does this compare to cortical recordings?

      Thank you for raising this important point regarding differences in CV and synchrony between layer 2/3 and layer 4 networks. Your question prompted us to correct Figure 3, which previously showed CV and synchrony with a wrong colorbar. We measured CV<sub>ISI</sub> and synchrony in both layers under these conditions, as shown in Figure 4 (black and red dots):

      Black dots:

      - Layer 4 (EI ratio = 7.35, firing rate = 8 Hz): CV<sub>ISI</sub> = 0.69, synchrony = 0.09

      - Layer 2/3 (E/I ratio = 5.25, firing rate = 4 Hz): CV<sub>ISI</sub> = 0.71, synchrony = 0.036

      Red dots:

      - Layer 4 (E/I ratio = 7.35, firing rate = 4 Hz): CV<sub>ISI</sub> = 0.78, synchrony = 0.05

      - Layer 2/3 (E/I ratio = 5.25, firing rate = 2 Hz): CV<sub>ISI</sub> = 0.76, synchrony = 0.024

      We included this analysis in the section "Network coding capacity for realistic cortical E/I ratios" where we discuss E/I ratios characteristic of the barrel cortex.

      Additionally, we analyzed CV<sub>ISI</sub> and synchrony in experimental cortical recordings from the Allen Institute for both layer 4 and layer 2/3, using data from networks with E/I ratios similar to those of the barrel cortex.

      In this data, we found the following values:

      - Layer 2/3 shows CV<sub>ISI</sub> = 0.090, synchrony = 0.05

      - Layer 4 shows CV<sub>ISI</sub> = 0.088, synchrony = 0.08

      We included these experimental results in the section "Coding capacity in different layers of the visual cortex.

      (4) The provided code link appears to be broken.

      Thank you for pointing this out. We have fixed the link and ensured that the code is now properly imported there.

      Minor Comments:

      (1) The discussion could expand on differences in cortical networks across the brain to justify or highlight the limitations of using anatomy from the barrel cortex and comparing it with V1 coding in the data analysis section (e.g. see Scala et al., 2019).

      We thank the reviewer for this valuable suggestion and for referencing Scala et al. (2019) [7]. We agree that expanding the discussion to address broader differences in cortical network organization across brain regions helps clarify the limitations of comparing a model based on barrel cortex anatomy with V1 coding data.

      As noted in above, we have incorporated these points into the revised discussion. Specifically, we now highlight key differences in intrinsic connectivity, receptor expression, neuromodulation, and functional specialization between cortical areas. These additions, along with citations to Scala et al. (2019) [7] and other relevant literature, aim to provide a more comprehensive perspective on the challenges of cross-area comparisons and to contextualize the scope and limitations of our modeling approach.

      (2) Using the E/I ratio instead of absolute numbers on plot axes might improve readability.

      The excitatory neuron count was held constant at 10,000, while the inhibitory neuron count was varied from 2,500 to 1,000 in 150-decrements. This resulted in an E/I ratio that ranged from 4 to 10, with unequal intervals between values. Consequently, we opted to use the number of inhibitory neurons as the plot axis instead of the E/I ratio.

      (3) The 3D plots are somewhat difficult to interpret. Consider alternative visualizations.

      We appreciate the feedback regarding the interpretability of 3D plots. Our aim has always been to present the data as clearly as possible. To address this, we consistently employ complementary 2D plots to simplify the interpretation of our 3D visualizations.

      For instance, in Figure 2 B, while we show a 3 D representation of the average firing rate across EI ratios, J<sub>ei</sub>, and θ<sub>inh</sub>, we also provide a corresponding 2D plot specifically for θ<sub>inh</sub> = 20 mV. This allows for a more direct and understandable view of how firing rate changes across EI ratios and J<sub>ei</sub> at that specific θ<sub>inh</sub> value.

      Similarly, for all 3D plots in Figure 3, which depict the average coefficient of variation of inter-spike intervals, synchrony, and participation ratio, we consistently present simpler 2D plots in the top panels. These 2D plots focus on the relationships between EI ratios and J<sub>ei</sub> at θ<sub>inh</sub> = 20 mV, making the complex 3D data more accessible.

      To further enhance clarity in Figure 4, which illustrates the regularity of network spike patterns in relation to participation ratio(PR), firing rate, and network encoding capacity, we have introduced an additional 2D plot within Figure 3. This new visualization specifically details the regularity of network spike patterns as a function of firing rate and network encoding capacity, providing a more focused and interpretable view.

      Beyond just visual demonstrations, we have also made a concerted effort to explain these 3D plots in extensive detail within both the main text body and the corresponding figure captions. We hope that with this multi-pronged approach even complex relationships are thoroughly communicated and understood.

      (4) Including a separate figure for the Allen Institute data analysis might help better evaluate the results.

      Because the Allen Institute data analysis measures dimensionality and coding capacity of layer 2/3 and layer 4, which are primarily numerical, a dedicated figure would not substantially enhance the visual information. We believe a direct textual explanation, as discussed in the results, effectively conveys the relevant information.

      (5) The claim: "However, neither previous theoretical nor simulation studies have addressed how these differences in EI ratio will affect layer-specific dynamics and computational properties" could benefit from clarification and additional references.

      Thank you for requesting additional referencing. We now add more clarification to the paragraph as follows:

      Although previous studies have explored various biologically realistic aspects of classical balanced networks, such as the effects of more complex neuronal properties including spike frequency adaptation using adaptive exponential integrate-and-fire (AdEx) neuron models [12] , the temporal evolution of randomly connected balanced networks through second-order mean-field approximations [13], predictions of nonlinear dynamics across diverse neuron models ranging from integrate-and-fire to Hodgkin–Huxley formulations, thus bridging population dynamics to neuronal electrophysiology [14], the impact of spatial heterogeneity in balanced networks [15–17], and variations in synaptic timescales [18], the specific effects of differences in EI ratios on layer-specific dynamics and computational properties have, to the best of our knowledge, not yet been addressed.

      (6) It might be worthwhile to discuss other cortical layers and interlaminar connectivity. r – Add refs in discussion about other brain areas with other EI ratios (cerebellum?)

      Thank you for your suggestion. We agree that including layer-specific distributions and E/I ratios in other brain areas provides valuable context. Exact percentages vary across studies, and detailed counts for every interneuron subtype are rare, but general patterns are well established. Across species from Drosophila [19], rodents [8, 20], cats [21, 22], to non-human primates [23] and humans [24], roughly 70–80% of cortical neurons are excitatory and 20–30% inhibitory, with the hippocampus and cerebellum showing ~85–90% excitatory neurons [8, 25, 26]. This conserved E/I ratio supports memory, multi-task learning, and flexible information processing [27–29].

      In the barrel cortex (S1), the layer-specific distributions reflect this pattern while highlighting functional specialisation: Layer 1 is almost entirely inhibitory (~90–95%), with very few excitatory cells (~5–10%), functioning primarily as a modulatory layer [21, 30]. In layers 2/3, 4, 5, and 6, excitatory neurons dominate numerically (~75–85%), while inhibitory neurons make up ~15–25% and include PV+, SOM+, and VIP+ interneurons that regulate local circuits and pyramidal outputs [30–33]. These excitatory and inhibitory neurons form interlaminar circuits that balance activity, stabilize network dynamics, and allow flexible signal propagation across the cortical column.

      This explanation has now been added to the discussion to clarify layer-specific E/I ratios and interlaminar connectivity.

      (7) Consider adding a justification for the grid search approach compared to simulation-based inference methods in the discussion.

      We appreciate the reviewer's suggestion to discuss the rationale behind our grid search approach, particularly in comparison to simulation-based inference methods. We understand the value of exploring more sophisticated inference techniques.

      We acknowledge that there are various simulation-based inference methods, such as approximate Bayesian computation or likelihood-free inference, that could potentially be applied to our model. However, for this study, our primary goal was to perform a systematic sensitivity analysis of the classical balanced network with respect to the EI ratio, inhibitory firing threshold, and inhibitory-to-excitatory synaptic strength. We aimed to comprehensively map the parameter space and observe the resulting changes in network dynamics across a wide range of parameter combinations.

      A grid search was chosen because it offered a straightforward and transparent way to achieve this objective. It allowed us to systematically explore the influence of each parameter independently and in combination with others, providing a clear visualization of the network's behavior across the parameter space. This method was particularly suitable for our initial investigation, which focused on understanding the fundamental relationships between these parameters and network activity.

      However, we recognize the potential benefits of simulation-based inference methods for future studies. These methods could be particularly useful for tasks such as parameter estimation, model selection, or exploring more complex parameter dependencies.

      We would be very interested to learn more about the specific simulation-based inference methods the reviewer had in mind and how they might be applied to our model. If the reviewer could provide more specific recommendations or references, we would be grateful. We will consider incorporating a discussion of these methods and their potential advantages in the discussion section, acknowledging the limitations of our current grid search approach and outlining potential avenues for future research.

      (8) Line 340: Correction needed for the "AP waveform."

      Thank you for your comment. We have revised the text to consistently specify AP waveform instead of just waveform throughout the manuscript.

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      (3) Adesnik H. Layer-specific excitation/inhibition balances during neuronal synchronization in the visual cortex. J Physiol 2018; 596: 1639–1657.

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      (7) Scala F, Kobak D, Shan S, et al. Layer 4 of mouse neocortex differs in cell types and circuit organization between sensory areas. Nat Commun 2019; 10: 4174.

      (8) Pelkey KA, Chittajallu R, Craig MT, et al. Hippocampal GABAergic Inhibitory Interneurons. Physiol Rev 2017; 97: 1619–1747.

      (9) Brunel N. Dynamics of Sparsely Connected Networks of Excitatory and Inhibitory Spiking Neurons. J Comput Neurosci 2000; 8: 183–208.

      (10) Xue M, Atallah BV, Scanziani M. Equalizing excitation-inhibition ratios across visual cortical neurons. Nature 2014; 511: 596–600.

      (11) Isaacson JS, Scanziani M. How inhibition shapes cortical activity. Neuron 2011; 72: 231–243.

      (12) Kusch L, Depannemaecker D, Destexhe A, et al. Dynamics and Bifurcation Structure of a Mean-Field Model of Adaptive Exponential Integrate-and-Fire Networks. Neural Comput 2025; 37: 1102–1123.

      (13) El Boustani S, Destexhe A. A master equation formalism for macroscopic modeling of asynchronous irregular activity states. Neural Comput 2009; 21: 46–100.

      (14) Carlu M, Chehab O, Dalla Porta L, et al. A mean-field approach to the dynamics of networks of complex neurons, from nonlinear Integrate-and-Fire to Hodgkin-Huxley models. J Neurophysiol 2020; 123: 1042–1051.

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      (23) Hendry SH, Schwark HD, Jones EG, et al. Numbers and proportions of GABA-immunoreactive neurons in different areas of monkey cerebral cortex. J Neurosci Off J Soc Neurosci 1987; 7: 1503–1519.

      (24) Hornung J-P, De Tribolet N. Distribution of GABA-containing neurons in human frontal cortex: a quantitative immunocytochemical study. Anat Embryol (Berl) 1994; 189: 139–145.

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    1. Author response:

      The following is the authors’ response to the original reviews.

      eLife Assessment:

      This valuable study presents a comprehensive comparison of human and macaque monkey behavior across a range of visual perceptual phenomena. The use of a unified oddball visual search paradigm enables direct cross-species comparison while minimizing task-related confounds. It provides solid evidence that visual perception is largely similar between these two species, with some interesting exceptions. These insights into qualitative and quantitative differences between species are relevant for evaluating macaques as a model organism for understanding human vision.

      Thank you, we are glad to note the positive overall assessment. We hope that our revision will lead to an even stronger assessment.

      Reviewer #1 (Public review):

      Summary:

      The authors set out to conduct a behavioral comparison of macaque and human vision across a wide range of visual properties. Such a comparison is critical for evaluating the use of macaques as a model system for understanding human vision and the underlying neural mechanisms. This goal represents a unique endeavour since prior studies have typically focused on only highly specific tasks. While the authors found consistent coarse representational structure for objects, evidence for Weber's Law and amodal completion, there was divergence for mirror image confusion and the use of global or local image properties.

      Thank you for your accurate assessment.

      Strengths:

      There are three major strengths of the study. First, the authors employed a behavioral paradigm (oddball search) that allowed them to test multiple perceptual phenomena without having to train the macaques on the specific type of stimuli tested. Second, humans and macaques could be tested in an identical manner. Third, the authors tested a range of different visual properties and phenomena, allowing a broader comparison between species.

      Thank you, we are glad that you found our study to be interestsing.

      There are also some weaknesses to the study (described below), but that doesn't change the fact that the authors have demonstrated and validated a novel approach for systematic and comprehensive comparisons of vision across species.

      We have now done our best to respond below to these comments and acknowledge limitations explicitly in the revision.

      Weaknesses:

      The weaknesses of the study arise in part because of the breadth of the work. In cases where there are divergences between the two species, it would be helpful to know what might account for such divergence, to have more depth. Is it really a species difference, or could there be a different account? For example, does the difference in mirror image confusion arise because the stimuli were objects that would have been highly familiar to the humans but not the macaques? Further, the authors often used small sets of stimuli (e.g. 8 objects only in the test of object similarity; a small set of highly specific occlusion stimuli), and how well the findings will generalize beyond those stimuli is unclear.

      Thank you for raising these important points. We have now acknowledged these issues in the Discussion (p.37) and the relevant paragraphs are reproduced below.

      “Although we have done our best to perform a comprehensive comparison of several perceptual phenomena between monkeys and humans, our study has several limitations.

      First, we were only able to test these phenomena on three monkeys, because training monkeys on these tasks is extremely challenging, and requires months of focused training, because of which it was simply not feasible for us to test larger numbers of animals. However, we consider it unlikely that our results would not generalize, because many of the tested perceptual phenomena were robust across our monkeys, and are highly robust across humans. There was also striking similarity between the three monkeys, which would not have been observed had there been large inter-individual differences. Even if our results did not generalize, the fact remains that a subpopulation of monkeys do show similarities and differences as observed here. Testing these phenomena on larger populations of animals will require installing automated training stations in group enclosures where many animals can be tested simultaneously.

      Second, the perceptual phenomena tested in this study are based on small numbers of images and conditions that again might not generalize when repeated on a larger set of images/conditions. While this is possible in principle, it was simply not possible for us to test a wide range of phenomena with a wide range of images, in the interest of having compact experiments that could be completed within one testing session. Testing a larger set of conditions would require multiple sessions for each animal, which would require counterbalancing sessions and introduce potential practice effects. However, we consider it unlikely that our results would not generalize across a wider set of conditions/images, because these effects are highly robust when tested in humans with relatively little inter-individual variability.

      Third, some of the perceptual phenomena tested in this study are based on testing natural objects, that are likely to be familiar to humans but not necessarily to our monkeys. As a result, the results observed could potentially be explained by familiarity to these images in humans but not in monkeys. We consider this unlikely, for several reasons. Our monkeys were housed in natural arenas where they encountered many natural objects, although not necessarily the images used in our experiments. While our human participants might have indeed been familiar with some objects, their responses during visual search may not have been driven by familiarity, particularly since their task involved searching for oddball targets without specifying their features. Indeed, oddball search shows only subtle effects of familiarity, as evidenced by highly correlated performance between readers and non-readers on letter searches (Agrawal et al., 2019, 2022). Understanding how familiarity shapes object representations in humans and monkeys would require careful testing with increasingly familiar objects and potentially with arbitrary shapes that are unfamiliar to both species. These are important considerations for future studies of cross-species comparisons.”

      The authors discuss the implications of training macaques to perform specific tasks on specific stimuli in comparing across species. While I agree that extensive training in monkeys could change perception, it is important to also consider that humans have been extensively trained through the types of visual tasks we conduct throughout our lives, so I'm not sure it is universally true that the best comparison is between humans and untrained monkeys. But this just consideration just highlights the general problem of comparing across species.

      We agree this is an important point. We now acknowledge this in the Discussion (p. 37) – see the paragraphs above.

      Reviewer #2 (Public review):

      Summary:

      The macaque monkey is often considered as the animal model of choice to study the neural correlates of visual perception, due to the close similarities to humans in terms of anatomy, physiology and behaviour (Van Essen and Dierker, 2007; DiCarlo et al., 2012; Roelfsema and Treue, 2014; Picaud et al., 2019; Van Essen et al., 2019; Hesse and Tsao, 2020). Quite some studies have been performed to compare the behaviour of macaque monkeys and humans on visual perception tasks. However, it remains difficult to compare the results of these studies as the methods that are used differ significantly between these studies. Furthermore, behavioural studies of macaque monkeys often involve extensive training as the tasks were relatively hard, making it difficult to compare the results with humans, who generally require very little training. The authors present a set of experiments to compare visual perception between macaque monkeys and humans, using the exact same behavioral task that is easy to learn and therefore requires very little training. As expected, they overall find that the two species behave similarly. However, they find a number of interesting exceptions.

      Thank you, we are glad that you found our study interesting.

      Strengths:

      A major strength of the current study is the relatively large number of tasks that were tested in the same subjects. This is made possible by using the oddball visual search task, which macaque monkeys can learn very quickly. This means that few trials are sufficient to obtain a significant difference between conditions, minimizing learning effects. Although this type of task has been used in previous studies (Sablé-Meyer et al., 2021), the current manuscript makes better use of the advantages and explains them more explicitly.

      In addition, the study finds a number of interesting differences between macaque monkeys and humans. In particular, while humans can dissociate horizontally mirrored images better than vertically mirrored images, monkeys show no difference between these two conditions (Experiment 4). Also, while humans dissociate images better based on the global shape of a stimulus, monkeys dissociate images better based on local elements of a stimulus (Experiments 5 and 6). Although these findings are largely a replication of previous results, they have not yet been studied together with other tasks within the same individual subjects, and the low number of trials avoids any learning effects.

      We thank the reviewer for highlighting the strengths of this study.

      Weaknesses:

      A weakness of the study is that while the objects that were used can be considered to be familiar to humans, they are not familiar to macaque monkeys

      In Experiment 4, humans can be expected to have 3D representations of familiar objects such as a Roman helmet or an office chair. Humans can therefore be expected to have view-invariant representations of these objects, predominantly for rotations around the vertical axis of the object (as movements are most common in the horizontal plane). This can explain why only humans confuse objects more often when mirrored vertically than when mirrored horizontally.

      Similarly, in Experiment 5, humans can be expected to be familiar with abstract geometric shapes such as squares and circles, while monkeys likely are not. This could explain why monkeys find it hard to recognize these geometric shapes in the global shape of the stimuli, even when thin grey lines are drawn to connect the local elements that constitute the global shape (Experiment 6). Instead, the combination of local shapes can be expected to form a texture that might be more easily recognized by the monkeys

      More generally, as proposed by Fagot et al, it might well be that monkeys tend to conceive stimuli as a combination of low-level visual features, instead of as references to objects in the outside world, as humans have learned to do (Fagot et al., 2010). This line of critique would be relevant to take into account.

      Thank you for raising these important points, which are similar to the concerns raised by Reviewer 1. We now acknowledge these limitations in the Discussion (p. 37), please see our responses above.

      Another weakness could be that only three monkeys are tested, while 24 human subjects are tested. According to some theoretical work, a finding in 3 animals is not sufficient to make a claim about an animal species (Fries and Maris, 2022). However, it seems that the results are largely consistent between the different monkeys. Moreover, the results generally agree with the results from previous literature. The conclusions by the authors are therefore largely supported by the results. Some results could be strengthened by additional experiments, or at least a more extensive discussion of the potential weaknesses.

      Thank you for this suggestion. We have now included a detailed section in the Discussion on limitations (p. 37).

      The potential impact of the paper is significant, as a start of a comprehensive comparison of visual perception between humans and macaque monkeys, which can inspire other labs to contribute to. This comparison can also be extended to other animal species (e.g. crows and rodents), as well as to different types of artificial neural networks (Leibo et al., 2018).

      Thank you, we now acknowledge this point in the Discussion (p. 40).

      Reviewer #2 (Recommendations for the authors):

      If additional experiments with the same monkeys are feasible, it would be valuable to test objects with which the monkeys are already familiar. In particular, there is evidence that monkeys interpret images of faces as referring to real-world objects (Fagot et al., 2010), which may be relevant for Experiments 4-6. For Experiments 5 and 6, for example, it may be useful to use face-like or emoticon-like stimuli rather than abstract geometric objects.

      Unfortunately, our study is now concluded and performing additional experiments is not possible at least for this study.

      In additionn, monkeys appear to discriminate geometric objects relatively well when they are presented as solid shapes (Sablé-Meyer et al., 2021). Rather than presenting only outlines, it may therefore be helpful to use filled shapes composed of local elements, in order to direct attention to the global shape (for example, a disk rather than a circle).

      Thank you for this interesting suggestion. We acknowledge this in the Discussion (p. 36).

      In case additional experiments are not feasible, it may still be worthwhile to examine the current dataset in more detail. In particular, there may be variation across stimuli in the degree of familiarity monkeys have with the objects used in Experiment 4, or in how easily they can distinguish the global shapes used in Experiments 5 and 6. It could therefore be informative to analyse performance separately for different pairs of objects, as in Figures 2B, C. For example, the contrast between an "X" and a circle may be easier for monkeys to distinguish at the global level than some other shape pairings.

      While these are interesting possibilities, we did not observe major differences in the monkeys’ performance on these shapes, and therefore did not include them here.

      Minor comments:

      (1) The fact that the reciprocal of reaction times seems to make it easier to compare between species could be due to the fact that the distribution of latencies then becomes symmetric instead of skewed, see the work on the LATER model (Noorani and Carpenter, 2016).

      Yes, thank you for noting this. We now acknowledge this in the Introduction (p. 5).

      (2) The study by Hopkins & Washburn 2002 is taken as evidence that macaque monkeys have a global advantage, while the conclusion of the paper itself is the opposite, and reaction times are indeed shorter for local differences than global differences (their Figure 3), as in the current manuscript.

      Thank you for pointing this out, we have corrected this copyediting error.

      (3) The discussion section about behavioral tasks that can be used to quickly probe perception is relevant, relating it to the free-choice paradigm. In addition, it may be useful to discuss the reward-association paradigm developed in the lab of Barry Richmond to quickly probe perceptual categorization after cortical lesions in macaque monkeys (Minamimoto et al., 2010). Although behavior in this paradigm is somewhat noisier, several dozen trials are generally sufficient to pick up differences in reaction times, which might provide an even more sensitive measure of the animals' ability to distinguish stimulus categories.

      We thank the reviewer for sharing this observation. While this is an interesting paradigm, the interaction with various reward volumes can make it extremely hard to interpret the results. We are not sure how this could be used for the kind of cross-species comparison we are attempting here.

      Reviewer #3 (Public review):

      Summary:

      In this study, Cherian and colleagues compare visual perception between humans and monkeys using a common oddball visual search task across a battery of perceptual phenomena. By keeping the task constant and varying only the stimulus sets, the authors aim to isolate perceptual similarities and differences between species. Across six experiments, they report that monkeys and humans share similarities in coarse object representations, Weber's law, and amodal completion, but differ in mirror confusion and global/local processing.

      We thank the reviewer for their careful evaluation of our manuscript and constructive feedback. We hope that our responses satisfactorily address the reviewers concerns.

      Strengths:

      A major strength of the study is the unified experimental framework. The authors designed the experiments such that the task procedures are identical across conditions and species, differing only in the images shown. This is a significant methodological advantage, as it minimizes task-related confounds that often complicate cross-species and cross-experiment comparisons. As a result, observed similarities and differences can be more directly attributed to perceptual processes rather than differences in training or task demands. This allows for a more comprehensive evaluation of visual perception than is typical in the literature, where individual studies often focus on a single effect with specialized training. The data are carefully collected, and the analyses are systematic and appropriate for the questions posed.

      Thank you for your accurate summary of the strengths of our study.

      Weaknesses:

      Despite its strengths, the study is largely descriptive and provides limited mechanistic or theoretical explanation for the observed similarities and differences. While the authors document several convergences and divergences between humans and monkeys, there is relatively little discussion of why these patterns arise or how they relate to existing theories of visual processing. As a result, it is difficult to assess the broader implications or generalizability of the findings beyond the specific task and stimuli used.

      Thank you for raising this point. Our goal was to characterize similarities and differences in perception between monkeys and humans. As previous comparative studies have typically focused on individual perceptual effects using different behavioural paradigms, it has remained difficult to obtain an integrated view of similarities and differences across multiple aspects of perception. Therefore, we believe that the establishment of this comparative benchmark is an important first step. We have deliberately chosen to avoid a deeper causative analysis of any observed differences in perception as that would necessitate further, and specific experiments to test out any competing hypothesis. This is an important aspect that can be studied in future experiments.

      Relatedly, the rationale for selecting the particular set of perceptual phenomena is not fully developed. Some tasks appear motivated by prior work comparing humans and deep neural networks, but it is unclear whether this set constitutes a representative or theoretically grounded sampling of visual perception. Without a clearer justification, it is difficult to interpret the absence or presence of specific effects (e.g., mirror confusion or global advantage) as reflecting fundamental species similarities/differences.

      We appreciate this insightful comment. The perceptual phenomena included in this study collectively span multiple aspects of visual processing while remaining measurable within the same oddball visual search paradigm. Our intention was not to provide an exhaustive survey of visual perception, but rather to demonstrate that a diverse range of perceptual signatures can be evaluated under identical behavioural conditions. These signatures are well-established and can be measured using the oddball visual search task. The primary aim of our study was to establish a general comparative framework rather than proposing any set of phenomena as the only or definitive dimensions of visual perception.

      Reviewer #3 (Recommendations for the authors):

      A key strength of this study is the use of a general oddball search paradigm that avoids task-specific training for each perceptual phenomenon. However, the manuscript provides very limited detail about how monkeys were trained to perform the task, with only a brief statement that they learned it in less than two weeks. Given that one of the central claims of the study is that it avoids training-induced biases, a more detailed description of training procedures is essential. In particular, it would be important to clarify what images were used during training, and whether these images were distinct from those used in the six experiments. If the monkeys were trained on a separate set of images and then generalized to novel stimuli, this would represent a significant strength that could be emphasized more clearly in the manuscript. If not, and if training involved the same or similar stimuli, this raises potential concerns about experience-dependent effects that should be addressed explicitly. Additionally, it would be helpful to clarify whether monkeys required retraining or familiarization when transitioning between experiments with different stimulus sets.

      Thank you for this important suggestion. We have now included details of the training procedures in the Methods (p. 42).

      The manuscript would benefit from a clearer and more principled justification of the selected perceptual phenomena. In the current version (e.g., L97-102), the choice appears to be motivated in part by the authors' prior work comparing humans with deep neural networks. While this is a reasonable starting point, it does not fully justify the selection in the context of cross-species comparison. The authors could strengthen the paper by explaining whether these phenomena were chosen to span distinct levels of visual processing, to test specific theoretical predictions, or to provide a representative sampling of perceptual functions. Making this rationale explicit would help readers interpret both positive and negative findings. For example, in its current form, there might be cross-species differences only in mirror-confusion and global advantage, and whatever is driving the differences does not affect any other visual processing.

      As we have detailed above, we attempted to employ a broad range of perceptual phenomena and unfortunately these do not have any common theoretical justifications, other than that many of them cannot be explained by simple pixel or low-level differences. We now acknowledge this point in the Introduction (p. 6).

      The results for coarse object representations and for global/local processing may benefit from further clarification. In Experiment 1, animate objects appear to be predominantly lateral views and therefore asymmetric, whereas inanimate objects are more often symmetric. As a result, within-category similarity may partly reflect shared global shape properties. It would be useful for the authors to clarify how this observation relates to the finding of a local (rather than global) advantage in monkeys in Experiments 5 and 6.

      Thank you for this interesting observation. While it is true that some of our inanimate objects are asymmetric, some are symmetric as well. Since the objects in this experiment were different in both their global and local features, it is not clear which features were being used by humans and monkeys, particularly since their performance was correlated. We now acknowledge this point in the Discussion (p. 35).

    1. Author response:

      The following is the authors’ response to the original reviews.

      eLife Assessment

      This Review Article addresses a significant and timely topic that concerns the role of cryo-EM in transforming RNA structural biology from static, individual conformations toward the reconstruction of dynamic conformational ensembles and energy landscapes. The authors describe eight case studies spanning different RNA classes and argue that conformational heterogeneity is a source of mechanistic information, rather than a limitation.

      We would like to thank the editor and all the reviewers for their careful assessment of our manuscript and for their comments and criticism. In this detailed point-by-point response, we have addressed all concerns of the reviewers.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      The review addresses an important and timely topic that concerns the role of cryo-EM in transforming RNA structural biology from a "static" discipline to one increasingly concerned with conformational ensembles and molecular dynamics. The scope is well within the eLife standards, and the style and general architecture do fit eLife.

      Strengths:

      The review is extremely well written, well-conceived and clear. The main strengths are in the breadth of coverage, the clear theme, and the inclusion of practical examples that explain in detail the construct design, sample preparation, vitrification, and data analysis. The manuscript will certainly be impactful and valuable, especially for readers who are not specialists in cryo-EM, as it provides an accessible overview of recent advances across a wide range of RNA systems.

      We thank the reviewer for their appreciation of our work.

      Weaknesses:

      My only reservation is that, currently, the review reads too much like a list of examples. The authors should make an effort, and I am sure they are well up to it, to try to synthesise the message, provide more critical insights and amalgamate the text better, to really reach a wider audience. If revised along the lines detailed below, I am sure that the review will become an authoritative and influential resource for the RNA structural biology community.

      To synthesize the message of our manuscript, we have now schematized the information on each case study in 6 dedicated Boxes, thus removing from the main text the detailed information that they contained, which results in a better amalgamated text. We have also increased the conceptual synthesis of the sections on regulatory RNAs (page 7, lines 33-37; page 8, lines 1-8) and on viral RNAs (page 9, lines 11-15; page 10, lines 1-6). Finally, we have provided more critical insights in the discussion on methodological limitations (page 21, lines 19-32; page 24, lines 6-10) and computational approaches (page 21, lines 12-19; page 24, lines 10-15), as suggested by the same reviewer in the recommendations for the authors (Reviewer 1, recommendations 2-7).

      Reviewer #2 (Public review):

      Summary:

      In this review, the authors set out to synthesize how cryo-EM is reshaping RNA structural biology, moving the field from the determination of static, individual conformations toward the reconstruction of dynamic conformational ensembles and energy landscapes. Through eight case studies spanning ribozymes, riboswitches, viral RNAs, and synthetic RNA assemblies, they aim to show how cryo-EM has revealed mechanisms of RNA motion, including folding, ligand-dependent switching, and cooperative assembly, and to provide a practical account of the experimental and computational challenges (construct design, sample preparation, vitrification, data analysis) that are specific to dynamic RNA targets.

      Strengths:

      The manuscript succeeds in bringing together a wide and genuinely current range of case studies illustrating the field's shift toward dynamics-focused cryo-EM, several published within the last one to two years. The dedicated "Challenges" section, which walks through construct engineering, buffer and vitrification optimization, grid screening, and heterogeneity-resolving computational approaches, is a particularly useful and practical contribution; it goes beyond simply cataloguing structures and gives readers new to the area a genuine methodological roadmap. The figures are detailed and well matched to the quantitative claims made in the text (helix rotations, distances, RMSDs), which strengthens the paper's value as a reference resource.

      We thank the reviewer for the appreciation of our work.

      Weaknesses:

      The coverage of two areas in particular, the SL5 viral RNA element and RNA quaternary/multimeric assemblies, would benefit from incorporating additional recent primary literature that is directly relevant but currently omitted. This does not undermine the manuscript's core narrative, but it means the review is presently less complete than it could be as a field synthesis, particularly for readers using it to identify the full body of recent work on these specific RNA classes.

      We have incorporated the following literature on viral RNA elements (de Moura et al., 2024; Jones & Ferre-D'Amare, 2025) and on multimeric RNAs (Huang et al., 2026), as recommended by this reviewer in the comments to the authors (Reviewer 2, recommendations 2-4).

      More concerning is that one specific structural claim, describing conformer heterogeneity in the cobalamin riboswitch (Case study 3, holo dimer 4), appears to invert the finding reported in its own source paper (Ding, Deme et al., 2023). As written, the manuscript states that P2 and the distal half of P6 are structured in dimer 4, whereas the source paper reports that these are the regions that could not be modeled. This is worth flagging prominently because it is a factual claim about a specific structure, not an interpretive point, and readers relying on this review as a secondary source could come away with an inverted understanding of that structure's flexibility.

      We apologize for the typo in our original version (structured instead of unstructured), which created confusion. The presentation of the cobalamin riboswitch case study is now schematized in a way that should resolve any ambiguity in Box 2 – Case study 3, to follow recommendations of Reviewer 1.

      The manuscript also contains several minor internal inconsistencies. None of these individually threatens the paper's core arguments, but together they suggest the manuscript would benefit from a careful proofreading and reference-list audit pass.

      We have proofread the manuscript and revised the reference list.

      Overall, the authors largely achieve their stated aim. The case studies convincingly illustrate that cryo-EM can now resolve discrete and continuous conformational states of RNA at near-atomic resolution, and the Challenges section substantiates the claim that construct design, sample preparation, and computational innovations have been jointly responsible for this progress. The gaps in coverage of SL5 and multimeric RNA literature, and the inverted claim in Case study 3, are the main respects in which the manuscript falls short of being a fully comprehensive and accurate synthesis at this stage, but these are correctable issues rather than flaws in the overall argument or framework.

      We have added relevant literature, as described in our responses to Reviewer 2, Public review and Recommendations 2-4.

      We have now also schematized case study 3 in Box 2, as explained in our responses to Reviewer 2, Public review, to follow recommendations of Reviewer 1.

      This review is likely to be a useful entry point and practical reference for researchers moving into RNA cryo-EM, particularly given the level of methodological detail in the Challenges section. Its impact would be strengthened by two additions. First, a short discussion of recent cryo-EM advances in tRNA would round out the manuscript's coverage of classical RNA structural targets alongside the ribozyme, riboswitch, and viral RNA case studies already included.

      We have introduced a new discussion of cryo-EM studies on tRNAs in the section on ribozymes (page 7, lines 5-10), along with the discussion of other relevant studies on ribosomal RNAs, as explained in our responses to Reviewer 2, Recommendations 5.

      Second, the raiA non-coding RNA, currently mentioned only briefly, has in the last two years become a genuine model system for cryo-EM-based ncRNA structure determination, progressing from a single novel-fold discovery to a comparative structural framework spanning multiple raiA subtypes and candidate protein partners. Expanding this into a full case study would let the manuscript showcase, in a single worked example, exactly the kind of field-level progression (from novel fold to scaffold-based strategy and further to comparative structural framework) that the review's own framing describes as the trajectory of the field as a whole.

      We have introduced a new discussion of cryo-EM studies on raiA in the section on regulatory RNAs (page 8, lines 22-28; page 9, lines 1-4). We have decided not to dedicate a specific case study to raiA, because our case studies specifically focus on examples where cryo-EM has revealed conformational dynamics of the targets. The raiA studies, instead, do not reveal notable dynamics – despite capturing interesting structural features of this RNA, as also indicated by Reviewer 2 in their comment to the authors (Recommendations 6). We have nonetheless highlighted some strategies used to obtain raiA cryo-EM structures in the “Challenges” sections (page 15, lines 23-24; page 18, lines 14-17; and page 20, line 12).

      Reviewer #3 (Public review):

      This review describes how cryo-EM is moving RNA structural biology from the determination of static structures toward the characterization of conformational ensembles. Eight case studies spanning self-splicing introns, riboswitches, viral RNA elements and synthetic assemblies show how cryo-EM has captured folding intermediates, hinge-mediated domain motions and ligand-dependent switching, and the authors pair these examples with practical guidance on construct design, sample preparation, vitrification and heterogeneity analysis. The argument that conformational heterogeneity is a source of mechanistic information, rather than a limitation, is well supported, and Table 1 will be a useful reference for laboratories entering the field. The manuscript is timely and of broad interest, and I recommend publication after minor revision.

      We thank the reviewer for their appreciation of our work.

      (1) Scaffold-based structure determination (page 14, lines 5-9). The section on chimeric RNAs presents the scaffold strategies as a single group and cites Haack et al. (2025) and Langeberg & Kieft (2023) in one parenthetical, so individual results are not attributed to their sources. The distinction between these studies is substantive. Earlier scaffolds based on the Tetrahymena group I intron (Langeberg & Kieft, 2023) or on RNA origami (Sampedro Vallina et al., Nucleic Acids Res. 51:4613-4624, 2023) resolved the appended RNAs at approximately 4.4-5 Å. Haack et al. (2025) reported the first RNA scaffold to yield a high-resolution structure of the target itself, resolving the ligand-binding pocket of the thiamine pyrophosphate (TPP) riboswitch at 2.5 Å and extending nucleotide-level cryo-EM analysis to small RNAs that had previously been intractable. I ask the authors to attribute each result to its source and to state explicitly that Haack et al. (2025) achieved the first high-resolution structure of a scaffolded target RNA. Because the same study captured the ligand-free TPP riboswitch in an open, Y-shaped conformation, a direct example of the ligand-dependent switching that is central to this review, the TPP riboswitch should also appear in the riboswitch section (page 8, lines 15-36), together with the fluoride riboswitch of Langeberg & Kieft (2023).

      We have split the reference in the section on chimeric RNAs (page 12, lines 11-16) to attribute individual results to their sources. We have also added a mention of the TPP riboswitch together with the fluoride riboswitch in our revised section on regulatory RNAs (page 8, lines 7-8), which we have now however conceptually synthesized in response to a comment from Reviewer 1.

      (2) Page 6, lines 8-14. Self-splicing introns are described collectively as evolutionary ancestors of the spliceosome that reside in pre-mRNA transcripts. The proposed ancestral relationship to spliceosomal introns and snRNAs applies to group II introns. Group I introns, including the Tetrahymena intron, which interrupts a pre-rRNA, initiate splicing with an exogenous guanosine and are not considered spliceosomal precursors.

      We apologize for the ambiguity that our original text created. We have now rephrased the corresponding paragraph (page 7, line 22) to indicate clearly that only group II introns, but not group I introns, are spliceosomal ancestors.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      This is a splendid and timely review which can become very influential in the field. My only reservation to accept it straightaway is that, currently, the review reads too much as a list of examples and is more descriptive than synthetic. Most of the manuscript is organized providing individual case studies. This is interesting and helpful, but the text often emphasises detailed structural observations, such as specific rotations, distances, RMSD, and conformational changes, without always drawing broader and more general conclusions from these numbers. As a result, the text sometimes reads more like a survey of recent literature than a critical review.

      We have schematized the descriptive examples in 6 dedicated Boxes, thus extracting from the main text the more detailed structural observations. See also our answer to Reviewer 1-Public review.

      The discussion would benefit from a stronger focus on common themes emerging across the examples discussed, such as recurring modes of RNA motion, general relationships between dynamics and function, and what cryo-EM uniquely contributes compared to other techniques.

      We have strengthened our discussion of recurring modes of RNA motion, general relationships between RNA structural dynamics and function, and the impact of cryo-EM in this field throughout the manuscript (i.e. page 13, lines 1-12; page 22, lines 11-18; and Table 1).

      In addition, the treatment of methodological limitations could be expanded. A more balanced discussion of the challenges associated with interpreting conformational heterogeneity and reconstructing energy landscapes would strengthen the central argument. Expanding the coverage of emerging computational approaches for analysing continuous heterogeneity would also enhance the review.

      We have introduced new considerations on the challenges associated with interpreting conformational heterogeneity and reconstructing RNA energy landscapes in the “Conclusions” section (page 23, lines 33-37; page 24, lines 1-3). We have also introduced new considerations on emerging computational approaches for analyzing continuous heterogeneity in RNA cryo-EM datasets, both in the “Challenges” section (page 21, lines 1232) and in the “Conclusions” section (page 24, lines 6-15).

      Taken together, the manuscript is strong and potentially impactful, but would benefit from greater synthesis, critical analysis, and conceptual discussion. It would be great if the authors could:

      (1) Increase conceptual synthesis.

      We have increased conceptual synthesis by shortening several sections, including those on regulatory and viral RNAs (page 7, lines 33-37 and page 8, lines 1-8; and page 9, lines 11-16 and page 10, lines 1-6, respectively), as also discussed in our response to Reviewer 1-Public review.

      (2) Reduce paper-by-paper description.

      We have introduced 6 schematic Boxes to summarize the 8 case studies in a synthetic manner, and reduce the paper-by-paper description, as also described in our response to Reviewer 1-Public review and Recommendations 1.

      (3) Expand discussion of computational approaches.

      We have expanded the discussion on emerging computational approaches for analyzing continuous heterogeneity in RNA cryo-EM datasets (page 21, lines 12-19; page 24, lines 1015), as also discussed in our responses to Reviewer 1-Public review and Recommendations 3.

      (4) Provide a more critical assessment of the limitations of cryo-EM.

      We provide a revised, extended description of the methodological limitations of cryo-EM (page 21, lines 19-32; page 24, lines 6-10), as also explained in our responses to Reviewer 1-Public review and Recommendations 3.

      (5) More carefully define what constitutes an "energy landscape."

      We have revised the text in the Introduction (page 4, lines 1-2 and lines 8-13), Challenges (page 21, lines 12-32), and Conclusion sections (page 23, lines 33-37; page 24, lines 1-3) to provide a more careful definition of what constitutes an “energy landscape”.

      Reviewer #2 (Recommendations for the authors):

      The description of holo dimer 4 states that "the majority of P2 and the distal half of the P6 are structured." This appears to invert the finding reported in Ding, Deme et al. (2023); the source paper states that these regions were the ones that could not be modeled in dimer 4. Please verify against the primary source and correct.

      We apologize for the typo in our original version (structured instead of unstructured), which created confusion. The presentation of the cobalamin riboswitch case study is now schematized in a way that should resolve any ambiguity in Box 2 – Case study 3, to follow recommendations of Reviewer 1.

      The discussion of SL5 structural dynamics would benefit from incorporating two additional primary studies:

      de Moura et al. (2024, Nucleic Acids Research, https://doi.org/10.1093/nar/gkae144) independently determined cryo-EM structures of the SL5 four-way junction across four Betacoronavirus subgenera (OC43-CoV, SARS-CoV-2, MERS-CoV, RoBat-CoV), combined with AFM and thermal stability data linking SL5 dynamics to start-codon accessibility, complementary to, and partly overlapping with, the Kretsch et al. (2024) structures already discussed.

      We have incorporated the recommended literature (de Moura et al., 2024) in Box 3 – Case study 5, and we have discussed AFM, thermal stability assays and temperature-dependent SHAPE results on page 17, lines 19-24.

      Jones & Ferré-D'Amaré (2025, RNA, https://doi.org/10.1261/rna.080413.125) solved a 3.3 Å crystal structure of SARS-CoV-2 SL5 confirming the T-shaped four-way-junction fold, and additionally collected a ~5 Å cryo-EM map with 3D variability analysis revealing conformational flexibility at the junction, an independent line of dynamics evidence for SARS-CoV-2 SL5 itself, distinct from the multi-conformation heterogeneity Kretsch et al. report for MERS and BtCoV-HKU5. Their in vitro translation data showing SL5 inhibits protein synthesis also directly substantiates the paragraph's framing of SL5 as a translation-modulating element. I'd encourage the authors to incorporate both.

      We have incorporated the recommended literature (Jones & Ferre-D'Amare, 2025) in Box 3 – Case study 5, and we have also included RNA construct modification information on page 14, lines 13-16.

      In the Multimeric RNAs section, suggested complementary review.

      In discussing natural RNA-only oligomeric assemblies (OLE, ARRPOF, GOLLD, ROOL) and their intermolecular interaction modes (kissing loops, A-minor interactions), the authors may wish to add Huang et al. 2026 (DOI: 10.1080/15476286.2026.2644525), a recent review specifically surveying the structural principles of RNA quaternary assembly, including the intermolecular motifs (kissing-loops, pseudoknots, palindromic base-pairing, stacking, metal-ion coordination) that mediate RNA dimer and higher-order oligomer formation. This would be a useful complementary reference for readers seeking a broader synthesis of RNA quaternary structure beyond the specific case studies presented here.

      We have included the recommended reference (Huang et al., 2026) in the section on multimeric RNAs (page 11, lines 23-24 and page 12, lines 1-2).

      The manuscript could benefit from a short discussion of how cryo-EM has recently advanced the structural characterization of tRNAs and tRNA-binding complexes, complementing the classical X-ray and NMR studies already cited. Biela et al. (2023, J. Biol. Chem. 299:104966) provides a recent overview of this shift that may be a useful reference.

      We have included the suggested reference (Biela et al., 2023) and a discussion on cryo-EM studies on tRNAs in the section on ribozymes (page 7, lines 5-10), along with the discussion of other relevant studies on ribosomal RNAs, as explained in our responses to R2-PR6.

      The discussion of raiA RNA would benefit from expansion into a dedicated case study, as raiA has become a rapidly developing model system for cryo-EM-based ncRNA structure determination. An initial cryo-EM structure (Badepally, de Moura et al. 2024, J. Mol. Biol. 436:168833) revealed a novel RNA 3D fold; subsequent work used raiA to demonstrate a scaffold-based cryo-EM strategy for small RNAs (Haack et al. 2025, Nat. Commun. 16:880) and included it among newly characterized large ornate bacterial RNAs (Kretsch et al. 2025, Nature 643:1135-1142). Most recently, He, Zhong et al. (2026, Nucleic Acids Res. 54:gkag185) determined four cryo-EM structures spanning distinct raiA subtypes, defining a conserved structural core (P3a-P3b, P4, and two pseudoknots) and identifying candidate protein-binding partners (KhpA-KhpB). This body of work illustrates how cryo-EM can progress from a single novel-fold discovery to a comparative structural framework for an entire ncRNA family, and would make a strong addition to the manuscript's coverage of the field.

      We have introduced a new discussion of cryo-EM studies on raiA in the section on regulatory RNAs (page 8, lines 22-28; page 9, lines 1-4). We have decided not to dedicate a specific case study to raiA, because our case studies specifically focus on examples where cryo-EM has revealed conformational dynamics of the targets. The raiA studies, instead, do not reveal notable dynamics – despite capturing interesting structural features of this RNA, as also indicated by Reviewer 2 in their comments above. We have nonetheless highlighted some strategies used to obtain raiA cryo-EM structures in the “Challenges” sections (page 15, lines 23-24; page 18, lines 14-17; and page 20, line 12).

      Minor comments:

      The reference list contains two pairs of entries (Wang, Xie et al., 2025a/b; Jadhav & Marcia, 2025a/b) that share identical DOIs and titles, differing only in volume/page formatting. These appear to be the same article, each cited twice as separate "a"/"b" references rather than genuinely distinct papers. Please consolidate each pair into a single reference and update the corresponding in-text citations accordingly. Given these duplicates, I would recommend the authors carefully check the entire reference list for accuracy before resubmission.

      We have corrected the reference list.

      Beyond the reference issues above, there are a few small inconsistencies worth addressing. In the "Multimeric RNAs" case study section, the main text consistently refers to "Brome mosaic virus" (BMV), while Table 1 lists it as "Bromo mosaic virus", please correct for consistency.

      We have corrected the typo in Table 1.

      Similarly, in the "Cryo-EM data collection" subsection discussing electron dose, the D43 aptazyme is referred to as the "PD1 aptazyme"; since PD-1 is the gene/protein that D43 regulates rather than the name of the RNA itself, this should be corrected to "D43 aptazyme" throughout.

      We have corrected the name of the D43 aptazyme throughout the text, and particularly in Box 6 – Case study 8.

      There is also a numerical discrepancy between the text and Table 1: the "Sample preparation of dynamic RNAs" section states that recent studies on dynamic RNAs have used magnesium concentrations in the range of 1-30 mM, yet Table 1 lists the RNA polymerase ribozyme's folding buffer as containing 100 mM MgCl₂, which falls outside this stated range; the authors should reconcile this.

      We have corrected the range of magnesium concentrations in the main text (page 15, line 5).

      Finally, in the Introduction, the statement that Miescher "described DNA" in 1871 slightly overstates the manuscript's own cited source (Thess et al., 2021), which argues that Miescher's original "nuclein" preparation contained both DNA and RNA; softening this phrasing (e.g., to "described nuclein, later shown to contain both DNA and RNA") would better align the claim with the citation supporting it.

      We have rephrased our description of the Miescher study in the Introduction to reflect that the “nuclein” preparation contained both RNA and DNA (page 4, line 33-34).

      References

      Biela, A., Hammermeister, A., Kaczmarczyk, I., Walczak, M., Koziej, L., Lin, T. Y., & Glatt, S. (2023). The diverse structural modes of tRNA binding and recognition. J Biol Chem, 299(8), 104966. https://doi.org/10.1016/j.jbc.2023.104966

      de Moura, T. R., Purta, E., Bernat, A., Martin-Cuevas, E. M., Kurkowska, M., Baulin, E. F., Mukherjee, S., Nowak, J., Biela, A. P., Rawski, M., Glatt, S., Moreno-Herrero, F., & Bujnicki, J. M. (2024). Conserved structures and dynamics in 5'-proximal regions of Betacoronavirus RNA genomes. Nucleic Acids Res, 52(6), 3419-3432. https://doi.org/10.1093/nar/gkae144

      Huang, Z., Lin, W., Wang, L., & Su, Z. (2026). Molecular insights into dynamic RNA quaternary assemblies. RNA Biol, 23(1), 1-13. https://doi.org/10.1080/15476286.2026.2644525

      Jones, C. P., & Ferre-D'Amare, A. R. (2025). Crystallographic and cryoEM analyses reveal SARS-CoV-2 SL5 is a mobile T-shaped four-way junction with deep pockets. Rna, 31(7), 949-960. https://doi.org/10.1261/rna.080413.125

    1. Author response:

      Thank you very much for carefully reading and providing thoughtful criticism of our manuscript, “A targeted bispecific TGFBR2 antagonist antibody demonstrates cell selectivity and enhanced potency on human fibroblasts.” It was very heartening to see that the reviewers recognized the insights from this work, and we agree with the highlighted limitations. As a group that has developed four biologics from concept to the clinic, we know that this work represents only the beginning; nonetheless, it demonstrates important progress, showing that in vitro it is possible to use targeting to enhance the capability of a TGFBR2 antagonist. The road forward for development of any TGFBR antagonist will likely be rocky. Even our in vitro journey highlighted a potential challenge related to differential sensitivity between cells to be reckoned with.

      After discussing it internally, we have decided to leave the manuscript in its current form as the version of record. There were several factors that we considered in our deliberations. For one, we know the data are solid and reproduceable. Second, in studies that we are not at liberty to share, we further validated this reported targeting strategy, achieving similar activity with other targeting receptors in multiple primary fibroblast types. Lastly and critically, because the reviews will be published with the manuscript, we think that collectively they show the strength of the work, its limitations, and delineate some of the next steps that others could pursue.

      We would like to reiterate our appreciation for the seriousness of the reviewers. Thank you.

    1. Author response:

      The following is the authors’ response to the original reviews.

      We would like to thank the editors and reviewers for taking the time to provide thoughtful comments on our manuscript. We were delighted to receive positive feedback, and we believe that the revisions made in response to these comments helped strengthen our manuscript even more. The key changes to the manuscript include:

      (1) Predictive utility analysis is now a more central focus of the paper, providing more guidance and discussion for how to apply it beyond the presented examples.

      (2) The details, assumptions, and limitations of the statistical settings explored by E2P Simulator are now discussed much more extensively.

      (3) The worked examples have been refined and updated. Each example now states its inputs, target population, and decision threshold with more detailed reasoning, in line with the guidance in Section 4.1. Several reported values in the treatment response, suicide risk, and Alzheimer's biomarker examples have also been updated as a result, although it did not change the overall conclusions and insights.

      (4) In the meantime, E2P Simulator has also been updated to v1.3.0, which now includes:

      a) Analytical solutions for the continuous outcome scenarios, which were sampling-based before. This provides more precise results for the treatment response prediction example.

      b) Threshold probability, pt, can now be set by entering a numerical value (previously, it was only possible to do it by sliding the threshold itself), which improves the ease of use.

      c) An interactive tutorial that explains the interface of E2P Simulator, making the interface more intuitive.

      Below we provide answers to each comment and quote the revised parts of the manuscript.

      Public Reviews:

      Reviewer 1 (Public review):

      Summary:

      The manuscript provides a well-argued discussion of the misalignment between common predictive performance evaluations reported in the literature and actually measuring clinical utility in the context of predictive psychiatry. Specifically, the authors discuss measurement reliability and prevalence as two neglected factors which can substantially inflate the assessment of model performance for clinical practice. To mitigate this, the authors offer a concrete framework and an accompanying web tool, with which to adjust performance metrics and additional predictive-value and decision-analytic measures.

      Strengths:

      The manuscript speaks convincingly about the risk of face validity and the practical irrelevance of seemingly promising predictive models in psychiatry. The authors outline how predictive performance estimations often fail to generalize to clinical contexts and thereby potentially mislead scientific efforts. In the face of ubiquitous biomarker models and incremental improvements in the literature, the reader is reminded that, irrespective of the glory of the proposed model, low reliability of clinical measurements fundamentally affects (and limits) both effect sizes and predictive performance ("garbage in, garbage out"), and that neglecting this can ultimately lead to misinformed decisions in the treatment of individual patients. The provision of an online tool with a user-friendly interface and clearly worked examples is a major practical asset that will facilitate the adoption of the proposed framework beyond quantitative methodologists.

      Weaknesses:

      While the outlined issues highlight important aspects in the translational gap, the suggested solutions remain somewhat theoretical. For example, the use of prevalence might not reflect what a model would see in practice, assuming that population prevalence and the composition of actual clinical cohorts are aligned. Accounting for who presents to care, and under which referral or triage patterns, is a crucial determinant of effective base rates. While the authors do acknowledge the importance of using base rates from the target population, these nuances could be emphasized more prominently at the points where practical recommendations are made. Relatedly, the analytical context and the methodological assumptions are not clearly specified. Many arguments and demonstrations are derived in univariate, group-comparison settings and then discussed in a way that can be read as broadly applicable.

      We thank the reviewer for the positive assessment and for highlighting these weaknesses. We now provide a lot more guidance on selecting the right base rate, and we also discuss the assumptions and limitations of the statistical settings under consideration in more detail.

      Regarding the base rate, we now expand on it in a newly added Section 4.1 Selecting appropriate inputs for predictive utility analysis:

      “Disease prevalence estimates can also vary substantially with study design, geographic region, cohort composition, and estimation method (e.g., Simeone et al., 2015; Flor et al., 2020). When base rates are very low, obtaining precise estimates becomes especially difficult (McGrath and Burke, 2024). For predictive utility analysis to be informative, two considerations are essential. First, the selected base rate must correspond to the population represented by the effect size or model performance estimate, because these quantities are not independent (Leeflang et al., 2013, 2009; Moons et al., 1997). Second, both the base rate and the effect size or model performance estimate should pertain to a clinically relevant population in which diagnostic, treatment, or risk decisions would actually be made. For example, comparing individuals with a history of suicide attempts with healthy controls (a common study design) could be meaningfully applied in predicting suicide risk in the general population, where the 12month prevalence of suicide attempts is extremely low (0.3%) (Borges et al., 2010), but this does not represent a clinically realistic use case. A more realistic scenario would involve predicting suicide risk in a psychiatric population presenting for clinical care, where the base rate would be higher, but could also vary with local triage and referral patterns. Evaluating prediction in this context would require an effect size or model performance estimate derived using controls from that same psychiatric population rather than healthy controls from the general population.”

      We also highlight these base rate selection nuances in a newly introduced Box 1, which provides a high-level summary of the predictive utility analysis workflow:

      “Use the outcome base rate expected where the predictor or model will be applied, rather than the proportion of cases in the study sample. The target population and, for risk prediction, the time horizon should align with those used to estimate the observed effect.”

      We also make these considerations more explicit in the examples we provide, eg, in section 3.1.1 we say:

      “Finally, because the effect size in question summarizes the differences between patients and healthy controls, the relevant target population for this illustrative analysis is the general population. Recent national surveys estimate depression prevalence to be around 9.2% among Americans aged 12 years or older (Goodwin et al., 2022) and 7.7% among Canadians aged 15 years or older (Halladay et al., 2026). We therefore use 8% as a rounded illustrative base rate within this range. Note that a more clinically realistic scenario, such as those explored below, would consider the biomarker in a preselected, higher prevalence group (e.g., help-seeking individuals); however, evaluating the biomarker in this setting would require an effect size estimated using controls drawn from that same target population rather than healthy controls from the general population.”

      As for the statistical setting and its limitations, we address this directly in the expanded Limitations section. Section 5.1 now states the distributional assumptions behind the binary classification examples:

      “The classification examples presented in this paper rely on Gaussian approximations: binary outcome mode assumes that the predictor or model score is normally distributed within each outcome group, whereas continuous outcome mode assumes a bivariate normal distribution of the predictor and outcome. These assumptions are necessary because commonly reported metrics such as Cohen’s d, Pearson’s r, and ROC-AUC summarize effect magnitude or discrimination but do not determine the shapes of the underlying distributions. Thus, when using these as inputs, E2P Simulator reconstructs distributions consistent with those values under Gaussian assumptions, even though clinical and behavioral data may often be skewed or heavy-tailed (Loth et al., 2021). Binormal models can approximate overall discrimination reasonably well across a range of distributional forms (Hanley, 1988; Hajian-Tilaki et al., 1997), but departures from normality may have greater effects on the ROC curve and thresholdspecific metrics (Walsh, 1997). The numerical results obtained with E2P Simulator should therefore be treated as approximations when the empirical distributions are unknown or nonGaussian. Although E2P Simulator v1.3.0 does not support non-Gaussian distributions, predictive utility analysis itself does not rely on parametric assumptions and could be performed by simply resampling the observed score distributions under different measurement noise and base rate assumptions, providing more exact estimates. Future releases of E2P Simulator will support this functionality.”

      In Section 5.3 we now address the assumptions behind the multivariable demonstrations:

      “The multivariable model simulations that we presented in this paper do not account for nonlinear relationships or interaction effects that machine learning models are designed to capitalize on. However, empirical evidence suggests this limitation may be less critical than may be expected. A systematic review by Christodoulou et al. (2019) showed that complex machine learning models rarely outperform simpler logistic regression in clinical prediction. Similarly, Schulz et al. (2020) found that deep learning models did not outperform simple linear models as sample size increased in UK Biobank brain-imaging data (with more recent work suggesting that this may be due to the disproportionate effect of measurement unreliability on interaction effects (Schulz and Ritter, 2026)). Finally, some research fields, like genetics, are primarily relying on linear models to begin with (Hill, 2010). Thus, while we may expect all kinds of interaction effects among our predictors to exist, they appear to contribute modestly to overall predictive performance in most clinical contexts.”

      In Section 5.4 we now specify the prediction settings that the current implementation does not cover:

      “While E2P Simulator currently focuses on binary classification and dichotomized continuous outcomes, it does not yet cover several important prediction contexts, including multiclass classification (e.g., subtyping, differential diagnosis, differential treatment response), risk stratification, time-to-event prediction, and longitudinal or trajectory modeling. Nevertheless, the same fundamental challenges stemming from measurement reliability and outcome base rate limitations remain equally critical in these scenarios.”

      We have also expanded the discussion around base rates in a newly added Section 4.2, which provides some considerations and observations around the high-risk subpopulations as a way to address low base rate challenges:

      “4.2. High-risk populations: predictive value and population coverage

      Given how strongly low base rates can constrain predictive value and clinical utility, a natural response is to focus the development of prediction models on high-risk subgroups. However, identifying such subgroups is itself a multistep classification problem involving referral, screening, and clinical assessment, each with its own sensitivity and specificity limitations. Cases missed at any earlier stage become false negatives of the overall identification process and are absent from performance estimates calculated only within the final high-risk group. This is well illustrated by our example on psychosis risk prediction: while predicting who will transition to psychosis within the CHR cohort benefits from a relatively high 19% 24-month transition rate (Salazar de Pablo et al., 2021), CHR criteria itself have low sensitivity, identifying only 6.7% of people who will later develop psychosis (Talukder et al., 2025). Strong performance within a high-risk subpopulation may therefore give an overly optimistic impression of the likely clinical impact if most eventual cases are missed before the prediction model is even applied. Accordingly, given that our goal is to maximize clinical impact rather than merely predictive performance, the development of prediction models should be guided by an assessment of where the main bottlenecks lie across the full clinical pathway, not just the final prediction stage within the high-risk group.”

      Reviewer 2 (Public review):

      Summary and strengths:

      The authors present a description of their online tool to estimate real-world performance of predictive models. The authors bring together different calculations to make better-informed implementation choices. It is a very nice tool to go from effect sizes to base rates to decision curve analysis. The paper describes the background and use of the tool with examples and seems like an extended version of their online howto. The methods themselves are not new, but I think the tool will be valuable for researchers from different fields. Tools already exist for the conversion of effect sizes (my current favorite is https://www.escal.site/), but I haven't seen measurement noise being incorporated previously. The main benefit is the evaluation of performance under different real-world scenarios. Code is available on GitHub, and the manuscript is wellwritten.

      Weaknesses:

      While comprehensive explanation and examples are important for correct use of the tool, I don't really see the added value above their online how-to guide, as the software itself has already been published (Karvelis, P. and Diaconescu, A. O. (2025b). E2p simulator: An interactive tool for estimating real world predictive utility of research findings. Journal of Open Source Software, 10(114):8334.)

      Thank you for raising this concern, which goes to the heart of the paper’s contribution. The JOSS article (Karvelis and Diaconescu, 2025b) is a two-page software paper: it announces the existence of the tool, states its dependencies and licence, and points to the repository. It contains no derivations, no worked examples, no guidance on the selection of inputs, and no discussion of the assumptions or limitations of the underlying statistical model. The online how-to guide provides more details and context but is a distilled version of the core motivations, assumptions and guidance. This manuscript (especially the current revised version) provides a much more detailed and literature-supported argument for the need of predictive utility analysis, guidance on how to perform it correctly, as well as a detailed discussion of caveats and broader considerations. Most importantly, the current manuscript goes beyond E2P Simulator and is focused more generally on predictive utility analysis as a principled workflow for evaluating findings and planning studies (with E2P Simulator being an accessible interactive tool for performing such analysis).

      Reviewer 3 (Public review):

      Summary:

      This important work provides a web-based tool to contextualize effect sizes in psychiatry with respect to reliability and base rates (collectively referred to as predictive utility analysis). The methods for the tool incorporate established psychometric principles that I think are of use for multiple fields in this seemingly easy-to-use tool. I agree with the critical importance of this tool and the methodological points made in this manuscript. Enthusiasm for the manuscript is weakened by a lack of clarity on the formulation of the paper and stated goals of the examples used, with the inferences and impact on clinical decision making from various parameterizations via this tool left open-ended.

      Strengths:

      This paper presents a well-considered and, what I think will be highly useful, web-based tool to contextualize effect sizes with respect to reliability and base rates. As the authors rightly point out, such a tool could be used in conjunction with widespread analytic power analysis tools in study planning. The paper also well contexualizes the need for such a tool in the relatively recent history of concerns of power, reliability, and inference in psychiatry specifically, and more general meta-scientific debates in psychology and neuroscience.

      Weaknesses:

      My primary feedback on this manuscript is the lack of clarity in what the paper itself, specifically, separate from the tool, is hoping to achieve. There is a central, but unresolved, tension in whether the reader is supposed to:

      (1) focus on the specifics of the examples used and whether to reevaluate the substantive claims from the studies,

      (2) buy in to how various reliability and base rate parameters impact modeling outcomes,

      (3) receive an introduction to the tool itself.

      In my estimation, the largest contribution to the field here is in (2) and (3), but currently much of the real estate of the paper is dedicated to several examples of (1). While these specific examples may be illustrative to some degree, I think given the number and brevity of such, they are unlikely to incidentally achieve points (2) and (3) above. Specific examples include the assertion of kappas for DSM diagnoses, without much nuance (e.g., see https://psycnet.apa.org/buy/2015-27500-001). Given the relatively limited space given to this example, however, it's hard to be entirely certain what the reviewer should take away.

      A second point of concern is where this tool would be situated in the research pipeline. I agree with the authors that this tool could be used in ways that parallel power analysis. With that in mind, it seems the most common use of this tool for an individual investigator is likely to be in a priori study planning. In contrast, and with my point above in mind, the use of the tool for existing results is likely best done with multiple estimates of effect sizes, reliability, and base rates, as is common in meta-analysis or consensus reviews. Nevertheless, there is no real example or guidance around how this influences new study planning.

      We are grateful for the reviewer’s careful and constructive assessment. This comment guided a substantial reframing of the paper: now in addition to the examples we put a lot more emphasis on the predictive utility analysis itself and provide more guidance on how to perform it, including what caveats need to be considered when selecting appropriate inputs.

      The updated abstract now reads:

      “… Here we argue that one important contributor to this translational gap is a pervasive misalignment between routine statistical analytic practices and the requirements for real-world decision making. To help address this, we introduce predictive utility analysis: a statistical workflow for estimating the practical significance of biomarkers and prediction models by accounting for outcome base rates and measurement reliability. Starting from effect size or model performance estimates, the workflow simulates expected real-world performance in a target population and summarizes it across complementary metrics including positive and negative predictive value, Precision-Recall AUC, and Net Benefit. Analogous to how power analysis is used for determining the conditions needed to achieve statistical significance, predictive utility analysis can help determine the conditions needed to achieve practical significance. We implement and illustrate this workflow using E2P Simulator, a recently developed open-source web tool that makes predictive utility analysis accessible through interactive simulations and publicationready visualizations…”

      We have also updated the title to reflect this emphasis:

      “Evaluating biomarkers and prediction models: predictive utility analysis with E2P Simulator”

      We now also include Box 1, which summarizes the predictive utility analysis workflow without having to go through the detailed examples.

      We have also introduced Section 4.1 for a detailed discussion on the nuances and caveats for selecting appropriate inputs for predictive utility analysis (see the revised manuscript for the full section). Among other things, this section also addresses your specific comment about DSM reliability estimates:

      “For example, interrater reliability of DSM diagnoses computed from clinicians rating the same recorded interviews can be higher than estimates based on repeated independent interviews (Chmielewski et al., 2015); however, the latter is more relevant because it better reflects the reliability of repeated assessments in real-world contexts (Regier et al., 2013), and that is what we used in our examples.”

      A third point is that more nuance would be useful in the introduction about the current state of psychiatry research. For example, I share many of the authors' concerns about reliability, power, reproducibility, and barriers to translation. That said, it is the case that while effect sizes should be considered considerably more, they are widely considered in psychiatry research via the common place of meta-analysis and other data pooling approaches. Another such example that the authors state in the context of reliability:

      "However, this [reliability] attenuation is rarely accounted for in routine analyses in psychiatry". This is true in practice, but somewhat misleading insofar as the method by which to do this remains unclear. For example, should we all report disattenuated associations, assuming there is no error and everything is perfectly reliable? This, of course, would be unrealistic to expect zero error. That we can achieve this with the new tool is clear, but the nuance of how and under what circumstances it should be done is not clear, and such nuance should be better reflected in the framing of the problem. That is, there is also a lack of clarity on what ought to be best practices and field-wide goals, rather than simply the lack of an ability to model these factors.

      Thank you for highlighting the need to further clarify these claims. Our argument is not that effect sizes are absent from psychiatric research or meta-analyses; it is that effect sizes, even when they are reported, are often difficult to interpret in an intuitive way. When it comes to poor reliability, the purpose of the predictive utility analysis is not to provide disattenuated values, but to show how much signal is lost (by comparing them to the observed and the disattenuated values). Another more general aim that we hope predictive utility analysis and this paper can help achieve is to increase the awareness of the importance of measurement reliability, prompting researchers to pay more attention to it, report it more consistently, and as a result of it, hopefully, find ways to improve it.

      The Introduction now states:

      “Even when effect sizes are reported and discussed (e.g., in meta-analyses), their meaningful interpretation often poses a problem (Funder and Ozer, 2019). The situation is further exacerbated by how effect sizes and thus their translational value are attenuated by measurement reliability, which often goes unassessed and unaddressed (Karvelis and Diaconescu, 2025a; Karvelis et al., 2023; Hedge et al., 2018).”

      We now also state these points clearly in Section 2.5 when introducing Predictive utility analysis and E2P Simulator:

      “To bring these statistical considerations together, we introduce predictive utility analysis: a statistical workflow for evaluating the practical significance of biomarkers and prediction models by explicitly accounting for real-world outcome base rates, measurement reliability, and, where relevant, the decision threshold. The workflow can be thought of as consisting of two key components: (1) translating conventional effect size and model performance metrics into measures that more directly reflect expected predictive value and utility, including PPV, NPV, PR-AUC, and NB by accounting for real-world base rates and relevant clinical decision thresholds, and (2) determining how much performance is lost due to measurement reliability.”

      Minor point

      For conceptual clarity, it would benefit the manuscript to at least briefly mention the role of validity in translational importance. Of course, the current psychometric issues of reliability, base rate, power, etc are critical, but it should at least be mentioned, given the potential wide audience of this manuscript, validity is important as well. For example, highly reliable measures may not be valid indicators of underlying disease etiology (e.g., fMRI head motion is a highly reliable trait-level feature, but typically not considered an important predictor or consequence of mental health worth investing translational resources in). Relatedly, confounding as a general topic would be useful to mention just briefly, to help with the spirit of considering underlying issues in translation.

      We thank the reviewer for raising this distinction. Construct or etiological validity and predictive utility address different questions. The present framework asks what predictive value and clinical utility follow from observed group differences under specified assumptions about measurement reliability, outcome base rate, and decision threshold. Whether the predictor indexes disease etiology is not required for these calculations: predictors used for diagnosis, prognosis, or risk stratification may be useful without supporting an etiological interpretation, while etiological relevance does not itself establish predictive usefulness.

      We have therefore kept a broader discussion of construct and etiological validity outside the scope of the manuscript. We have, however, added confounding to the new Section 4.1 because it can directly compromise the effect size or model performance estimates used as inputs to predictive utility analysis:

      “Predictive utility analysis is informative only to the extent that its inputs are carefully and appropriately chosen. Effect sizes from individual studies are subject to sampling error and may be inflated by publication bias, selective reporting, or analytical flexibility (Button et al., 2013; Ioannidis, 2008; Ioannidis and Panagiotou, 2011). Similarly, estimates of multivariable model performance may be overly optimistic because of overfitting (e.g., Karvelis et al., 2022; Schnack and Kahn, 2016; Hunt et al., 2024; Chen et al., 2025) or confounding features (Chyzhyk et al., 2022; Komeyer et al., 2025). This creates a tricky paradox: while our analysis shows that larger effect sizes are needed for clinical translation, many effects reported in the literature may already be inflated. To guard against these issues, researchers should use the most robust estimates available: effect sizes should ideally be supported by large samples, replication, or meta-analysis, while model performance should be estimated using properly held out or external validation data.”

      Recommendations for the Authors:

      Reviewer 1 (Recommendations for the Authors):

      I would like to thank the authors for their work. I truly appreciate their clear and structured definition of interpretative flaws in the current predictive psychiatry literature. The manuscript nevertheless has some issues in its current form, which, in my opinion, would need to be addressed.

      Major

      (1) The manuscript would substantially benefit from a paragraph introducing the common predictive modeling approach(es) to which the authors are referring. It seems there are a lot of implicit assumptions about the methodological details and nature of the predictive models which are not explicitly stated. Therefore, defining the methodological context would be helpful, specifically describing the common predictive model workflow, distributive assumptions, the statistical models which are used, etc. This might also be helpful in clearly distinguishing the statistical setting from related approaches, e.g., from crossvalidated machine-learning metrics, for which several of the metric mappings and conversions might not be valid or need to be calculated differently.

      (2) In general, I would encourage the authors to nuance some of the stronger claims about what and in which cases predictive utility analysis and E2P can deliver. While the authors' use case is really important, it is nevertheless limited. For example, all conversions are derived under the assumption of (bi)variate normality and linear separability, which neglects that psychiatric and neuroimaging variables can be skewed, heavy-tailed, or multimodal and decision boundaries can be non-linear or even multi-variate. Similarly, section 3.3.2 is informative but currently reads as quite strong in its implications, given the simplifying assumptions behind the multivariable calculator (equal effect sizes, constant pairwise correlations, linear additivity).

      We appreciate the reviewer’s request for a clearer account of the statistical setting. We have now clarified the assumptions and limitations in multiple places. First, we now include a new Supplementary note 1, which provides all equations, statistical models and assumptions used by E2P Simulator for the univariate binary and continuous modes. Supplementary note 2 has also been updated to more clearly explain assumptions when performing multivariable simulations.

      We now also elaborate on the considerations you highlighted; in Section 5.1 we discuss normality assumptions:

      “The classification examples presented in this paper rely on Gaussian approximations: binary outcome mode assumes that the predictor or model score is normally distributed within each outcome group, whereas continuous outcome mode assumes a bivariate normal distribution of the predictor and outcome. These assumptions are necessary because commonly reported metrics such as Cohen’s d, Pearson’s r, and ROC-AUC summarize effect magnitude or discrimination but do not determine the shapes of the underlying distributions. Thus, when using these as inputs, E2P Simulator reconstructs distributions consistent with those values under Gaussian assumptions, even though clinical and behavioral data may often be skewed or heavy-tailed (Loth et al., 2021). Binormal models can approximate overall discrimination reasonably well across a range of distributional forms (Hanley, 1988; Hajian-Tilaki et al., 1997), but departures from normality may have greater effects on the ROC curve and thresholdspecific metrics (Walsh, 1997). The numerical results obtained with E2P Simulator should therefore be treated as approximations when the empirical distributions are unknown or nonGaussian. Although E2P Simulator v1.3.0 does not support non-Gaussian distributions, predictive utility analysis itself does not rely on parametric assumptions and could be performed by simply resampling the observed score distributions under different measurement noise and base rate assumptions, providing more exact estimates. Future releases of E2P Simulator will support this functionality.”

      In Section 5.3 we discuss interaction effects in common predictive multivariable modeling approaches:

      “The multivariable model simulations that we presented in this paper do not account for nonlinear relationships or interaction effects that machine learning models are designed to capitalize on. However, empirical evidence suggests this limitation may be less critical than may be expected. A systematic review by Christodoulou et al. (2019) showed that complex machine learning models rarely outperform simpler logistic regression in clinical prediction. Similarly, Schulz et al. (2020) found that deep learning models did not outperform simple linear models as sample size increased in UK Biobank brain-imaging data (with more recent work suggesting that this may be due to the disproportionate effect of measurement reliability on interaction effects (Schulz and Ritter, 2026)). Finally, some research fields, like genetics, are primarily relying on linear models to begin with (Hill, 2010). Thus, while we may expect all kinds of interaction effects among our predictors to exist, they appear to contribute modestly to overall predictive performance in most clinical contexts.”

      And highlight these simplifying assumptions when presenting multivariable simulation results in Section 3.1.2:

      “E2P Simulator also includes multivariable calculators that estimate how many biomarkers of a given strength and collinearity would be required to achieve a specified performance target, assuming an additive linear model without interaction effects (see Supplementary note 2 for more details).”

      And we have softened the language around its implications; in Section 3.2.2

      “Because these predictors may capture overlapping information, collinearity can limit the incremental predictive gain obtained by combining them. For example, assuming an average collinearity of 0.15 among all predictors, we would need 20 predictors of r = 0.3 to achieve PRAUC = 0.8, which translates to R2 = 0.47 (Supplementary Fig. 2).”

      In Section 5.4 we also explicitly highlight which statistical settings we have not covered in this paper:

      “While E2P Simulator currently focuses on binary classification and dichotomized continuous outcomes, it does not yet cover several important prediction contexts, including multiclass classification (e.g., subtyping, differential diagnosis, differential treatment response), risk stratification, time-to-event prediction, and longitudinal or trajectory modeling. Nevertheless, the same fundamental challenges stemming from measurement reliability and outcome base rate limitations remain equally critical in these scenarios.”

      (1) The sentence "The literature seems to be filled with weak and false positive findings (Ioannidis and Panagiotou, 2011; Collaboration, 2015; Ioannidis, 2005)" strikes me as unnecessarily strong, especially given that the cited work is at least a decade old. The case is already compelling without this sentence, and I recommend removing it. Moreover, I suggest avoiding implying that overfitting is unique to or inherent in ML approaches. Classical statistical modeling is subject to many of the same problems (e.g. data dredging, post-hoc variable selection, inadequate validation).

      Thank you for this suggestion – we have removed the quoted sentence.

      We also made sure that our discussion around overfitting is general enough to include all multivariable models, not only ML. Eg, in the Introduction we say:

      “When multiple predictors of small effect sizes are then combined to build prediction models, they end up underperforming (which is often masked by inflated performance metrics due to overfitting).” And in Section 4.1 we now say:

      “Similarly, estimates of multivariable model performance may be overly optimistic because of overfitting (e.g., Karvelis et al., 2022; Schnack and Kahn, 2016; Hunt et al., 2024; Chen et al., 2025) or confounding features (Chyzhyk et al., 2022; Komeyer et al., 2025).”

      (2) The explanation of ROC-AUC could be reframed for clarity, e.g "ROC-AUC can be interpreted as the probability that, given a randomly chosen positive and a randomly chosen negative individual, the model assigns a higher predicted risk score to the positive than to the negative." The phrase "ranks higher" without explicitly referring to the risk score may be confusing to some readers.

      Thank you for suggesting a better phrasing. We have incorporated it; in Section 2.3.1:

      “Calculating the area under ROC (ROC-AUC) provides an informative summary metric which captures the average probability that, given a randomly chosen positive and a randomly chosen negative individual (e.g., a patient with a psychiatric condition and a control), a predictor assigns a higher predicted risk score to the positive than to the negative.”

      (3) In the depression biomarker example, the authors write: "Accounting for measurement reliability reveals that this observed effect would correspond to a much larger true effect, ..." The verb "accounting" here may be confusing, and does not reflect what is done: exploring via simulation how improved reliability would change effect sizes and predictive utility. I suggest reframing the sentence to make the intention clear.

      (4) Relatedly, the phrase "simply improving measurement reliability" in line 260 underplays how difficult and resource-intensive it is to substantially improve reliability for many psychiatric measures. The word "simply" might not be warranted here.

      Thank you for pointing these wording problems. We no longer use the word “accounting” and make it clear that we are simply exploring a hypothetical scenario where measurement reliability is higher. We also no longer say “simply improving” to not create a misleading interpretation that improving reliability is easy; in Section 3.1.1:

      “We can then explore the consequences of a hypothetical improvement in measurement reliability. If both the biomarker and diagnostic outcome were measured perfectly, the expected effect would increase to d = 1.58, with substantially better predictive performance: ROC-AUC = 0.87, PR-AUC = 0.46, PPV = 0.34, sensitivity = 0.63, and ∆NB = 0.033 at pt = 0.15. This illustrates how much diagnostic prediction could improve through better measurement alone.”

      (5) In the treatment-response section, the discussion of "neurocognitive predictors" and then "task-evoked BOLD signals" needs a better introduction, given that the reader has not read the paper the authors are referring to. Please specify what you mean by neurocognitive predictors (neuroimaging features, raw signals, task-fMRI derived response times or other metrics, cognitive test scores, clinical variables?). Moreover, from a clinical practice perspective, it would be important to at least acknowledge that taskbased fMRI is unlikely to become a routine clinical tool for antidepressant treatment selection in the foreseeable future.

      We now clarify what we mean by neurocognitive predictors in Section 3.2.1:

      “Research using multivariable / machine learning models suggests that neurocognitive predictors (brain activity and behavioral measures derived from cognitive tasks) can explain 20% of the variance (R² = 0.2) in symptom improvement in response to antidepressants and other treatments (Karvelis et al., 2022).”

      Near-term routine use of task-based fMRI for treatment selection is indeed unlikely. The example is retained for a narrower methodological purpose: it asks what the reported performance of this published predictor class would imply under plausible measurement conditions. Because the manuscript does not evaluate the cost or implementation feasibility of particular imaging modalities, we have not added a categorical forecast about routine adoption. Instead, the revised text makes the illustrative status and demanding performance requirements clear by describing the estimated performance as modest and the prospective target as ambitious, in Section 3.2.1:

      “Entering these values into E2P Simulator yields ROC-AUC = 0.71 and PR-AUC = 0.66, indicating rather modest predictive performance, as shown by the low PR-AUC (Fig. 5).”

      and:

      “Using E2P Simulator we find that to achieve PR-AUC = 0.8, it would require explaining approximately 47% of variance (R<sup>2</sup> = 0.47), which is rather ambitious.”

      (6) In the same vein, in section 3.3.2, you write that "predictors are associated with clinical variables". It would help readers if you were more concrete about what types of predictors you are referring to and what differentiates them from clinical variables.

      The earlier wording collapsed three distinct roles: candidate biomarkers, the clinical variables with which they are initially associated, and the outcomes predicted by the combined model. The revised sentence now distinguishes them; in Section 3.2.2:

      “When building prediction models in neuroscience, a common approach is to first show that candidate biomarkers are associated with clinical variables (e.g., symptom severity), after which both are jointly used to train a classifier for predicting clinical outcomes (e.g., Hauke et al., 2022; Tozzi et al., 2020; de la Salle et al., 2022; Karvelis et al., 2022).”

      Reviewer 2 (Recommendations for the authors):

      (1) My main concern with E2P is mainly related to the sample size calculation for multivariable models based on Riley et al. 2020, which goes wrong for machine learning. Riley refers to van der Ploeg et al. 2014, in which they don't consider standard machine learning procedures such as feature selection, tuning, etc. Empirical learning curves show that sample size calculations are way off. But as sample size calculations are not covered in this manuscript, please ignore for now, but I hope the authors can incorporate something more appropriate (synthetic learning curves?).

      Thank you for pointing out these issues. We will look into it and will update this module accordingly. Given that it is beyond the scope of the paper, no changes were made to the manuscript in response to this comment.

      (2) How do the True vs Observed effects above the figure relate to the True vs Observed effects for the effect size slider in the box on the left? One can only enter values under True, while one only obtains Observed effect sizes. Does this left ES box alternate with the Effects button above? It may be good to provide some additional explanation on when to enter values where.

      The apparent inconsistency arises because the two interface elements operate at different levels. The True/Observed switch above the plot controls which distributions and predictive metrics are displayed; it does not alter the paired True and Observed effect size values shown in the left panel. Those values remain linked through the reliability settings. Because the numeric field edits the latent True value, a user reproducing a reported observed effect should first enter the reliability parameters and then move the slider until the Observed value matches the reported result. Box 1 now presents the inputs in that sequence:

      “Specify measurement reliability. Enter reliability estimates for the predictor and outcome, preferably from the same dataset or closely matched studies.”

      and:

      “Enter the observed result. Use an effect size (e.g., Cohen’s d, OR, Pearson’s r) or predictiveperformance metric (e.g., ROC-AUC, PR-AUC).”

      We have now also added an interactive tutorial which explains the E2P Simulator’s interface, which will hopefully make the interface more intuitive.

      (3) A minor comment for the example under 3.1.1: I don't see how the population prevalence is relevant here, as one would only assess depression in a preselected clinical setting. Similarly, for 3.3.1: how is the response to antidepressants beyond placebo relevant, as one is only observing the response, regardless of whether it is related to the compound or placebo?

      Thank you for bringing this up. The two examples require different base rate logic. In the depression example, use of the general population prevalence is not a claim that the biomarker should be deployed for population-wide screening. It follows from the particular case-control effect, which contrasts patients with depression against healthy controls. The revised text makes this conditionality explicit and explains what would be required to analyze a preselected clinical population; in Section 3.1.1:

      “Finally, because the effect size in question summarizes the differences between patients and healthy controls, the relevant target population for this illustrative analysis is the general population. Recent national surveys estimate depression prevalence to be around 9.2% among Americans aged 12 years or older (Goodwin et al., 2022) and 7.7% among Canadians aged 15 years or older (Halladay et al., 2026). We therefore use 8% as a rounded illustrative base rate within this range. Note that a more clinically realistic scenario, such as those explored below, would consider the biomarker in a preselected, higher prevalence group (e.g., help-seeking individuals); however, evaluating the biomarker in this setting would require an effect size estimated using controls drawn from that same target population rather than healthy controls from the general population.”

      We thank the reviewer for highlighting the inconsistency in the treatment response prediction example: the relevant base rate is indeed the observed response rate among treated patients, not response beyond placebo. We have corrected the value to 46% and updated Figure 5 and all associated results; in Section 3.2.1:

      “A recent meta-analysis of SSRI trials reported a 46% response rate, defined as a ≥ 50% reduction in MADRS scores (Hieronymus et al., 2025); we therefore use 46% as the base rate…

      …ROC-AUC = 0.71 and PR-AUC = 0.66, indicating rather modest predictive performance, as shown by the low PR-AUC (Fig. 5). We use an illustrative threshold of pt = 0.20 to examine classification of likely responders among patients receiving antidepressant treatment. At pt = 0.2, we observe sensitivity = 0.98 and PPV = 0.48, meaning that 88% of nonresponders would still be classified as likely responders. This would correspond to ∆NB = 0.005 or 5 additional correctly identified responders per 1,000 patients evaluated. Under these proxy reliability assumptions, perfect measurement would improve performance quite substantially, up to ROCAUC = 0.85 and PR-AUC = 0.83, which at pt = 0.2 would result in sensitivity = 0.95, PPV = 0.59, and ∆NB = 0.035.”

      Reviewer 3 (Recommendations for the authors):

      My more directed recommendations are to reformulate the examples to consider the potential end users of this tool. As stated in the public review, I think this will significantly improve the clarity around the manuscript.

      We appreciate this recommendation; it became an organizing principle for the revision. The manuscript is now structured around two end user tasks: evaluating the practical significance of an existing finding and planning future research around a clinically meaningful performance target; in Section 2.5, we say:

      “Predictive utility analysis can be used both to evaluate existing findings and to plan new studies (Box 1). When evaluating an existing finding, researchers can work forward from a reported effect size or model performance estimate to examine its expected predictive value and utility in the target population. When planning research, they can work backward from a desired level of predictive performance (Lord et al., 2019) to determine which combinations of effect size or discriminative performance, measurement reliability, outcome base rate, and number of predictors would achieve that target. This is analogous to power analysis (Cohen, 1992): whereas power analysis evaluates whether a study is likely to detect an effect under specified assumptions, predictive utility analysis evaluates whether an effect or model is likely to provide meaningful practical utility under specified assumptions.

      The newly added Box 1 and Section 4.1 also provide more guidance on how to perform predictive utility analysis beyond the provided examples.

    1. Author response:

      We thank the reviewers for constructive and thorough reports. We are encouraged that they find the data of high quality, the method promising, and the interpretation well balanced. We will revise the manuscript thoroughly. Here we respond to the main common concern and outline the planned revisions.

      Independent validation.

      The assessment and all three reviewers ask whether our results could be artefacts of QPI. We would like to clarify that the results rest on two instruments that work in fundamentally different ways. 2D QPI (digital holography or interferometry, Holomonitor) measures the integrated optical path length. Refractive index tomography (3D QPI, Tomocube) reconstructs the 3D refractive index from multiple illumination angles. The two use different light paths, reconstruction algorithms and post-processing. In particular, the tomographic cell height comes from the geometric position of the RI contrast along the optical axis. It therefore does not depend on the absolute refractive index of the cell which 2D QPI height does. What the two methods share is the relation between optical phase and dry mass, which has been established for more than seventy years [1,2]. This relation has repeatedly been cross-validated with independent methods. Both QPI modalities have several times been cross-validated against other methods for single cells. For example, dry mass concentration from refractive index tomography agrees with stimulated Raman scattering measurements on the same cells [3]. Optical measurements (fluorescence exclusion volume combined with QPI dry mass) and mechanical measurements (suspended microchannel resonator) independently find the same mitotic swelling at constant dry mass [4,5]. The two modalities agree on the density dependence of monolayer height and on the magnitude of its spatial and temporal fluctuations. In the revision we will present the two modalities separately rather than pooled, so that this agreement can be seen directly.

      We nevertheless agree that comparison with a non-optical-phase method would strengthen the conclusions. We are exploring, with collaborators, volume measurements on MDCK monolayers using fluorescence exclusion adapted to monolayers. This may require some additional time.

      Comparison with previous height measurements.

      Our cell densities (1300–3200 cells/mm<sup>2</sup>) overlap those of the key earlier studies of MDCK monolayer dynamics: about 1400 cells/mm<sup>2</sup> in Zehnder et al. [6,7] and 1480–2630 cells/mm<sup>2</sup> in Angelini et al. [8]. Zehnder et al. [6,7] use the same parental MDCK line as we do, ATCC NBL-2 CCL-34 (T. E. Angelini, personal communication). We therefore do not think the difference from earlier reports is explained by a different cell line or by studying monolayers at a different stage of confluence. Remaining differences in substrate and medium will be discussed in the revision.

      We also note that the confocal literature on MDCK monolayer height is itself divided. Zehnder et al. found a flat layer (7.1 ± 0.7 µm, 4.7 % spatial variation) over a 160 × 160 µm area of about 64 cells [6]. In contrast, Thiagarajan et al. found thickness changes up to twofold during pulsations, also by confocal microscopy [9]. Our measurements cover a field of view of about 570 × 570 µm and agree with the latter. Zehnder et al. also reported single-cell area oscillations with an amplitude of 20 % and a period of 4 h [6], similar to the area fluctuations we observe. In their own confocal tracking of individual cells, some cells conserved volume and others did not (Supporting Material of [6]). What is new in our data is that the dry mass concentration stays nearly constant during these fluctuations. We will expand the discussion of why membrane-label confocal measurements and phase measurements may differ: axial resolution, the criterion used to define the apical surface, and averaging over the cell versus at the cell centre.

      Non-prismatic geometry and apparent mass non-conservation.

      We agree with Reviewers 1 and 3 that the most debatable part of the manuscript is the interpretation of apparent dry mass loss in segmented cells. We always presented mass shedding as one of two non-exclusive interpretations, and we explicitly favoured non-prismatic geometry as the main contribution. In the revision we will strengthen this emphasis. We will also add the alternative mechanisms suggested by Reviewer 3: material exchange between neighbouring cells through tunnelling nanotubes or unresolved cytokinetic bridges, and partial uptake of neighbours. We agree with Reviewer 3 that the recovery of mass conservation after coarse-graining favours redistribution over net loss.

      We note, however, that the existence of non-prismatic cell shapes in MDCK monolayers is not our central point. What matters is that such shapes quantitatively bias widely used measures: segmented cell volume, cell velocity from apical PIV or tracking, and continuum descriptions based on plug flow. The breakdown of the continuity equation below about two cell diameters and 0.6 h is a direct test of this. It implies that velocity fields measured at cellular scales do not in general represent the motion of the cell's centre of mass. We will make this point more explicit.

      We will attempt 3D segmentation of the refractive index tomograms, as Reviewer 1 suggests. We note, though, that lateral membranes have low RI contrast and that the axial resolution of holotomography is limited by the missing-cone problem (Appendix B). Reliable 3D segmentation of confluent monolayers therefore remains a challenge.

      Timescales.

      We thank Reviewer 3 for raising the question of timescales. The volume and height fluctuations we report have periods of hours (≈5 h). That is much slower than water flux (seconds) or ion pumping (minutes), and matches the timescale of dry mass changes. Together with the near-constant dry mass concentration, this supports our conclusion that fluid transport is not the dominant driver of the pulsations. We will restructure the discussion around this argument and reduce the repetition of results that Reviewer 3 noted.

      Further revisions. We will:

      - Add a sensitivity analysis of the results to the image-analysis parameters (Gaussian filtering, segmentation and height thresholds) (Reviewer 2);

      - Expand the description of the velocity-field determination (Reviewer 2);

      - Discuss growth as a source term in the continuity equation (Reviewer 2);

      - Add an error estimate for the dry mass concentration under plausible compositional changes in the refraction increment (Reviewer 1);

      - Clarify how the weak density dependence of the dry mass concentration in the ensemble (Fig. 8G) is consistent with the near-constant concentration in single-cell tracks (Reviewer 1).

      References

      (1) Barer R. Interference microscopy and mass determination. Nature 169, 366–367 (1952). doi:10.1038/169366b0

      (2) Davies HG, Wilkins MHF. Interference microscopy and mass determination. Nature 169, 541 (1952). doi:10.1038/169541a0

      (3) Oh S, Lee C, Yang W, Li A, Mukherjee A, Basan M, et al., Kirschner MW. Protein and lipid mass concentration measurement in tissues by stimulated Raman scattering microscopy. Proc Natl Acad Sci USA 119, e2117938119 (2022). doi:10.1073/pnas.2117938119

      (4) Zlotek-Zlotkiewicz E, Monnier S, Cappello G, Le Berre M, Piel M. Optical volume and mass measurements show that mammalian cells swell during mitosis. J Cell Biol 211, 765–774 (2015). doi:10.1083/jcb.201505056

      (5) Son S, Kang JH, Oh S, Kirschner MW, Mitchison TJ, Manalis S. Resonant microchannel volume and mass measurements show that suspended cells swell during mitosis. J Cell Biol 211, 757–763 (2015). doi:10.1083/jcb.201505058

      (6) Zehnder SM, Suaris M, Bellaire MM, Angelini TE. Cell volume fluctuations in MDCK monolayers. Biophys J 108, 247–250 (2015). doi:10.1016/j.bpj.2014.11.1856

      (7) Zehnder SM, Wiatt MK, Uruena JM, Dunn AC, Sawyer WG, Angelini TE. Multicellular density fluctuations in epithelial monolayers. Phys Rev E 92, 032729 (2015). doi:10.1103/PhysRevE.92.032729

      (8) T. E. Angelini, E. Hannezo, X. Trepat, M. Marquez, J. J. Fredberg, and D. A. Weitz, Glass-like dynamics of collective cell migration, PNAS 108, 4714 (2011).

      (9) Thiagarajan R, Inamdar MM, Riveline D. Interplay between cell height variations and planar pulsations in epithelial monolayers. Eur Phys J E 45, 49 (2022). doi:10.1140/epje/s10189-022-00201-6

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      The authors quantified and compared the 3D kinematics of bill and tongue movements between two seed-eating bird species: one that specializes on soft seeds, and one that is more adapted to feeding on hard seeds. Their goal was to determine specifically what the role of the tongue was for processing (e.g., dehusking) seeds, and to understand how differences in biting strength between species affect other aspects of seed processing. The authors provided intricate (visual) details of seed processing movements, and showed how coordination between the tongue and cranial kinesis (i.e., mobility of the upper bill relative to the cranium) is both critically important for properly positioning seeds to enhance feeding efficiency. Many studies have detailed how seed-eating birds process seeds, but this study has elevated those to a new level of quantification and visualization for readers to fully experience firsthand. Furthermore, the authors established that the force-velocity trade-off that has been observed between bill functions (e.g., feeding and singing) is largely driven by the contractile properties of the muscles. The conclusions are well supported by the results, and the authors placed the results more broadly into the context of manual grasping, making the argument that these birds achieve high levels of dexterity with far fewer degrees of freedom, which could have potential biomimetic applications.

      Strengths:

      This study builds upon - and advances - our understanding of the feeding mechanics of seed-eating birds using cutting-edge 3-dimensional modeling and kinematics. Their quantitative analyses of upper and lower bill, tongue, and seed displacements are complemented by elegant visualizations of seed processing in each species. Their comprehensive Bayesian modeling statistical framework tackles the issue of small sample sizes (i.e., few subjects) with volumes of data for each (i.e., lots of sequential kinematic variables) that plague comparative biomechanics studies, principally because (a) it is difficult to gather these high resolution XROMM and muscle contractile data on more than just a few subjects, and (b) these data streams are inherently very large, as they are gathered at high frame and sampling rates. Furthermore, I believe their approach to statistically testing for differences between species sets a new standard for our field that could (perhaps should?) be implemented in other similar types of studies. Another strength is in how the results were packaged: each subsection indicated how the objectives were addressed, and there were concluding statements trailing each subsection that helped deliver the key takeaways.

      Thank you very much for your positive evaluation, especially regarding our statistical method for testing for species differences.

      Weaknesses:

      A potential weakness is one that the authors themselves mentioned, regarding the body (and skull) size differences between species. Because gape size limits bite force, and given the force-velocity tradeoff in muscle function, there could be limitations on the rapid manipulation of relatively large seeds for similar reasons in the smaller finches. I see that the small finches appear to overcompensate in their beak rotations, but it's not clear how those compensatory movements might affect their seed processing kinematics with their preferred seed sizes. This does not nullify the authors' conclusions, but the results for the smaller finches might not be entirely representative of seed processing mechanics in smaller species.

      We extended the discussion of the effect of skull size differences, addressing potential implications for the generalizability of our findings.

      Reviewer #2 (Public review):

      Summary:

      This study investigates coordinated beak-tongue movements in seed manipulation, biting, and dehusking in songbirds. A comparative analysis of the seed-eating process in two songbird species with different biting forces, the domestic canary and Java sparrow, was conducted using high-speed XROMM with anatomical marker tracking and quantitative behavioral analysis. The authors have done a great job analyzing upper and lower beak rotation and translation, seed orientation and movement speed, and tongue kinematics.

      Strengths:

      The methodological approach of using high-speed (500 fps) X-ray reconstruction for 3D kinematic tracking in small animals is novel and powerful. It enables high temporal resolution tracking of orofacial movements and could potentially inspire future orofacial research in mammals, including mice and marmosets. Moreover, this study encompasses a wide range of anatomical components involved in seed manipulation behavior, including the upper and lower beak, the tongue, and jaw muscles. The behavioral quantification of these components is solid. The findings that both the upper and lower beaks contribute to seed processing, that the lower beak exhibits greater up-and-down and left-to-right flexibility than the upper beak during seed processing, and that the tongue plays an important role in transporting seeds into the mouth are all solid conclusions consistent with observations of bird feeding behavior. Nevertheless, it is valuable to confirm and quantitatively characterize these observations experimentally. The videos are excellent and very informative.

      Thank you very much for your positive evaluation!

      Weaknesses:

      (1) The paper often resorts to qualitative descriptions (e.g., "a high positive correlation of tongue velocity and seed velocity", "Compared to positioning, the measured velocities of both seed and tongue were much lower") instead of providing exact quantitative measurements or statistical results. The authors stated that temporal autocorrelation biases standard statistical analyses (lines 205-210), but this rationale does not justify the absence of statistical validation. Suggestion: use appropriate methods for time-series data, such as a permutation test, to test the significance of correlations between variables and avoid false positives.

      As suggested, we implemented a permutation test for the analysis of correlation between time series data. This was done for both the upper and lower beak pitch angles and for the seed and tongue translations. These analyses did not change the conclusions of the paper.

      (2) (Minor) The marker-tracking image shown in Figure 1B could benefit from the inclusion of a higher-contrast, zoomed-in frame of the head showing the metal markers without the red tracking points, alongside the same frame with the red tracking points overlaid, to provide readers with a clearer view of the X-ray image and the methodology and its precision.

      We adjusted Figure 1B as suggested.

      (3) (Minor: possibly soften the mechanistic claim). The proposed mechanism of lingual papillae on the tongue surface may aid food manipulation and food movement towards the posterior region of the mouth is interesting, yet the evidence describing their morphology is not strong enough to support the claim about their functional roles. Furthermore, the claim that papillae orientation affects food transport in lines 294-296 lacks supporting experimental evidence. In addition, the roles of extrinsic and intrinsic tongue muscles in controlling dexterous tongue shape changes and movements are not discussed.

      We adjusted the discussion paragraph on the morpho-functional role of the tongue, highlighting that experimental evidence is needed to confirm the suggested mechanistic role of lingual papillae.

      We decided not to include discussion on the role of extrinsic and intrinsic tongue muscles as we did not find any studies on lingual musculature in our species of interest (and also not in closely related species or in species of similar feeding type). Hence, any discussion on this topic would have been highly speculative, which we preferred to avoid.

      Recommendations for the authors:

      Reviewing Editor Comments:

      The reviewers are in agreement on both the strengths and the key areas for improvement. The authors should consider the following consolidated recommendations:

      Major

      (1) The Bayesian statistical modeling framework, while innovative and compelling, is inaccessible to less quantitative readers in animal behavior and ornithology. The authors should provide a more userfriendly version, either in the main text or as a supplement.

      We acknowledge that the rather technical descriptions and mathematical nomenclature may be difficult to grasp for readers without a strong background in that topic. Still, we believe that this way of description is necessary to accurately convey the method. To make the workflow easier to understand, we provide a visualization of the procedure in a flowchart figure as an additional Figure in the Appendix. We hope that this will help readers to better comprehend the method we applied.

      (2) Qualitative descriptions of key relationships (e.g., tongue-seed velocity correlations) should be backed by appropriate statistical validation. Given the temporal autocorrelation in these data, permutation tests or other time-series-appropriate methods are recommended.

      As suggested, we implemented a permutation test for the analysis of correlation between time series data. This was done for both the upper and lower beak pitch angles and for the seed and tongue translations.

      Minor

      (3) Sample sizes should be reported earlier in the paper (currently first appearing at line 780).

      The sample size for the XROMM and muscle experiments was actually reported in lines 426 and 681 of the original manuscript, respectively (in the first paragraphs of the according subsections in the Materials and Methods section). The number of sampled individuals is also given in each results figure caption. To make sure that sample size information is found easily, we added an extra sentence to the ‘Birds and housing’ paragraph of the Materials and Methods section.

      (4) The XROMM methods section should clarify that all movements are relative to a fixed cranium.

      We added such a clarification to the ‘XROMM animation and data export’ section.

      (5) Mechanistic claims about lingual papillae orientation and food transport (lines 294-296) should be softened, as the morphological evidence does not sufficiently support functional conclusions.

      We adjusted the discussion paragraph on the functional role of lingual papillae accordingly, highlighting that experimental evidence is needed to confirm the suggested morpho-functional relationships.

      (6) The discussion of body and skull size differences between species should be expanded to address how these affect the generalizability of findings for smaller finches.

      We extended the discussion of the effect of skull size differences, addressing potential implications for the generalizability of our findings.

      Reviewer #1 (Recommendations for the authors):

      (1) The probabilistic statistical modeling framework employed here is unique and compelling, but it's also very cumbersome and difficult to follow, which will make it difficult for other researchers to implement. This is not a fault of the authors; I'm sure their articulation of the procedures does proper justice to the methodologies, but those parts seemed to have been written for mathematicians, not for biologists. I wonder if a more "advanced" version could be made available in a supplement, and a more "user-friendly" version could be provided in the article (or vice-versa).

      We acknowledge that the rather technical descriptions and mathematical nomenclature may be difficult to grasp for readers without a strong background in that topic. Still, we believe that this way of description is necessary to accurately convey the method. To make the workflow easier to understand, we provide a visualization of the procedure in a flowchart figure as an additional Figure in the Appendix. We hope that this will help readers to better comprehend the method we applied.

      (2) Lines 304, 313, and 362 may or may not benefit from the recent findings of Sustaita & Laurin (2024; JEB 227, jeb246555).

      We included the Sustaita & Laurin (2024) reference in our discussion paragraph on cranial kinesis.

      (3) In the XROMM section, ca. line 535, consider indicating somewhere that all movements are relative to a fixed cranium.

      We added such a clarification to the ‘XROMM animation and data export’ section.

      (4) Perhaps I missed it, but it was not until line 780 that I encountered the actual sample sizes of subjects used; consider expressing this earlier in the paper.

      The sample size for the XROMM and muscle experiments was actually reported in lines 426 and 681 of the original manuscript, respectively (in the first paragraphs of the according subsections in the Materials and Methods section). The number of sampled individuals is also given in each results figure caption. To make sure that sample size information is found easily, we added an extra sentence to the ‘Birds and housing’ paragraph of the Materials and Methods section.

      Reviewer #2 (Recommendations for the authors):

      Minor point:

      Slightly awkward phrasing in lines 206-208: Since these data were derived "from" individual frames over time, independence of data points "could not be assumed/was violated due to potentially strong temporal autocorrelation".

      This paragraph was deleted in the revised manuscript.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      (1) Speed and mismatch between locomotion and visual stimulation.

      The authors do not clearly describe the definition of locomotion versus the resting state. The speed should, by itself, have an impact on neuronal responses, especially at the onset of locomotion. Several published studies show that the mismatch between a visual stimulus and the speed of the animal induces specific responses in V1, both in excitatory and subtypes of inhibitory neurons. The authors should address these points upfront in the manuscript, since it is likely a major variable explaining their results.

      This suggestion has revealed interesting new features in our data.

      We have now clarified in the methods that a trial was classified as “locomotion” when an animal ran at a minimum of 3 cm/s for at least 80% of the 10 s stimulus presentation, and was classified as “rest” when running under 3 cm/s during the same fraction of time. Trials with transitions from rest to locomotion and vice versa were rare and were excluded to ensure a stable behavioural state throughout the trial. We have included an example trace in Supplementary Fig. 1 to show how this categorization was done.

      We found a preferred speed at which locomotion most strongly modulates visual processing in layer 2/3, with the strongest effects in sensitizing PCs. To assess how visual responses varied with running speed, we classified neurons based on their average speed during the imaging session. We found that response amplitude does not simply increase monotonically with speed but rather exhibits a maximum at a preferred speed of 10-20 cm/s followed by a second weaker peak at 45-55 cm/s (Fig. 2A). These speed ranges overlap with those typically associated with walking (9 ± 5 cm/s) and trotting (51 ± 9 cm/s) in mice (Bellardita & Kiehn, 2015). Sensitizing PCs consistently underwent a larger increase in visual responses than depressors, with the largest difference occurring at speeds of ~10 cm/s (Fig. 2B,C).

      Locomotion has also been shown to modulate inhibitory interneurons (Dipoppa et al., 2018), but the impact on their visually-evoked responses is less well characterised. We found that visual responses of VIP and PV interneurons were strongly amplified at lower locomotion speeds (Fig. 2D-G), while SSTs were not significantly affected (Fig.2 H,I). Overall, these results reveal a preferred speed at which locomotion most strongly modulates visual processing in layer 2/3, with the strongest effects in sensitizing PCs.

      We did not find a correlation between stimulus onset and response increase. We quantified the onsets preceding each trial based on (Vinck et al., 2015). Although lower speed trials contained more locomotion onsets, as illustrated by the example traces, these events were relatively infrequent and occurred at different time points relative to stimulus presentation, making it difficult to assess their contribution to adaptation.

      The effects of visuomotor mismatch could not be directly assessed based on our experimental paradigm. While previous studies distinguished visual flow from running speed by introducing violations of their relationship in head-fixed mice navigating a virtual-reality corridor (Keller et al., 2012; Saleem et al., 2013), our mice were presented with a fixed stimulus irrespective of their locomotion speed. Consequently, different degrees of mismatch between visual input and locomotion were present continuously rather than being introduced as unexpected events during a trial.

      Action taken

      - At line ~173, we added the speed analysis as a new figure (Fig. 2).

      - At line ~889, we added a new Discussion section interpreting these results in the context of previous literature.

      - At Line ~1030 in the Methods section, we clarified the definition of locomotion and rest periods.

      (2) Use of deconvolution with MLSpike.

      Some results (Figure 2) exclusively depend on the deconvolution of calcium signals into spikes (since the initial peak is not seen in calcium transients). The authors should validate this result either with electrophysiological recordings or with the use of another deconvolution method (e.g. CASCADE), emphasising the limitations of this approach and the limitations of the time resolution of calcium imaging.

      We have now validated our results using an alternative spike inference method CASCADE (Rupprecht et al., 2021), and find that it generates a similar initial peak. This is now shown in Supplementary Fig. 3C, A similar initial increase in amplitude followed by fast depression is a consistent observation in electrophysiological recordings in V1 (Chance et al., 1998; Jin & Glickfeld, 2020; Varela et al., 1997). We have maintained MLSpike as our main spike inference method because CASCADE relies on a mapping learned from external ground truth datasets, whereas MLSpike estimates the calcium-spikes relationship from the dataset being analysed. If adaptation alters the spike-to-calcium transformation, there may exist discrepancies in inferred adaptation dynamics even when both methods recover the initial responses.

      We have also added a note in the Methods section (line ~1053) about the limitations of the method due to both the limited time-resolution of calcium imaging and the unvalidated assumptions we used to transform calcium signals into spikes.

      Action taken

      - Added Supplementary Fig. 3C.

      - At line ~216, “Despite the limited time-resolution of calcium imaging, the inferred spiking response revealed the initial phase of fast depressing adaptation that is a consistent feature of electrophysiological recordings (Chance et al., 1998; Fairhall et al., 2001; Varela et al., 1997) (red arrows In Fig. 3A-B). The initial peak was also recovered using the CASCADE (Rupprecht et al., 2021) spike inference method (Supplementary Fig. 3C).”

      - At line ~1053: “The initial component should be interpreted cautiously because of the limited time-resolution of calcium imaging and because spike inference relies on assumptions that were not directly validated in our experiments. Nevertheless, the initial peak was also recovered using a different spike inference method: CASCADE. Calcium traces were analysed using CASCADE (Ref. Rupprecht et al., 2021) with the pretrained Global_EXC_6Hz_smoothing200ms model. CASCADE automatically matched traces to the available noise levels and combined predictions across five network ensembles. The resulting inferred spike probabilities were compared with the MLSpike results.”

      (3) The manuscript is centred around a specific increase in visual responses in sensitizing neurons during locomotion, both in the fraction of responsive neurons and response magnitudes.

      It is hard to tell whether this difference is due to a greater scaling effect of locomotion, a difference in responses during the resting state, or both. The manuscript should further explore and discuss the differences in responses between sensitizing and depressing neurons, both during the resting state and locomotion. Adding metrics and direct comparisons of the magnitudes of fast responses, slow responses, and time integrals between sensitizing and depressing neurons in resting and locomotion states would help to clarify this. Same for fractions of responsive neurons of each type in each condition. E.g., the slow phase is harder to judge from the plots, but the DeltaF/F integral shown in Figure 1G seems to suggest the difference in response magnitude between sensitizing and depressing neurons is largest in locomotion state, rather than resting state. How do these integrals look for inferred firing rates shown in Figure 2?

      The difference between sensitizing and depressing PCs is due to a greater scaling effect of locomotion, not a change in the rest state. We have now clarified this point by adding the metrics suggested. Fig. 1G uses integrated responses and shows that in the resting state there is no significant difference in the visual responses of PCs categorized as sensitizing, intermediate and depressing. Fig. 1H then shows that the increase in the integrated response during locomotion is negatively correlated with the Adaptive Index.

      We have also divided the signal into initial amplitude and average amplitude to represent the fast and slow components respectively. While there are only small variations in initial amplitude that are not correlated with gain increase (Fig. 1I, Supplementary Fig. 2B), average amplitude is just a scaled version of the time integral giving exactly the same results (Supplementary Fig. 2D).

      The fraction of responsive cells of different adaptive types does not significantly vary from rest to locomotion beyond a difference in AI spread which is only the result of an additive change in gain (Fig. 1C, Methods line ~1025). For this reason, we defined the populations in tertiles, so that each population represents the same relative number of cells. We have now made this clearer in the text.

      We now also document metrics for inferred spikes. The new Fig. 3D-F compares the initial peak amplitudes, showing that locomotion causes a larger relative increase in peak response in sensitizing PCs compared to depressors. We have also added in Supplementary Fig. 3B time integrals which again show that sensitizers undergo a larger increase in gain.

      Action taken

      - Adding individual comparisons to Fig. 1G. and Supplementary Fig. 2D.

      - Adding individual comparisons of initial peak amplitude in inferred spikes to Fig. 3D, and time integral to Supplementary Fig. 3B.

      - Adding how the increase in response varies with AI in Fig. 1H and initial amplitude in Fig. 1I and Supplementary Fig. 2B.

      - At line ~142, “These differences were due to sensitizers displaying a larger response during the locomotion state, rather than differences in responses during the resting state (Fig. 1 D-I)”

      - At line ~130, “To investigate how these response changes affected PCs undergoing different forms of adaptation, we split the population into three equal-sized groups based on the distribution of the adaptive index (AI): sensitizing (more negative AI), intermediate, and depressing (more positive AI; Fig. 1C).”

      (4) There is something counterintuitive about how the changes in inhibition onto sensitizing and depressing neurons during locomotion explain the reported activity changes.

      Sensitizers receive reduced SST input and increased PV input during locomotion. If SSTs depress and PVs sensitize (and this is the main reason why sensitizers, which receive dominant input from SSTs sensitize, and vice-versa), how is it possible that this switch does not alter the sensitizing or depressing nature of these neurons' responses in locomotion? Are these changes insufficient to flip the dominant SST-PV drive? Figure 6D-E seems to show there is a flip, at least for sensitizers. How do authors explain this? Do authors think this is related to the narrowing of the adaptive index distribution shown in Figure 1C?

      The additional dimensionality reduction analyses has simplified the model and the PV: SST ratio remains approximately unchanged in sensitizing PCs (Rest = 1.1; Loco = 1.1) and decreases in depressing PCs, without reversing their relative inhibitory balance (Rest = 2.7; Loco = 1.8).

      The narrowing of the adaptive index distribution in Fig. 1C is the result of an additive gain increase from rest to locomotion. We calculated the adaptive index as AI = (R1 − R2)/(R1 + R2) where R1 is the average response over the period 0.5 - 2.5 s after stimulus onset and R2 is the average at 8-10 s. Adding the same constant to R1 and R2 will make all AIs closer to 0 narrowing the adaptive index distribution as observed in figure 1C. We have now clarified this in the Methods section.

      Action taken

      - At line ~1027, “As a result, adding the same constant to R1 and R2 will make all AIs closer to 0 which is what we observe from rest to locomotion.”

      (5) Presentation of the experimental data and the model.

      The manuscript introduces the results of interneuron recordings during the description of the model. Similarly, the results of optogenetic manipulations are presented inside the model's description. It would be clearer to present all experimental data first and introduce the model later, fitting it to all experimental evidence previously presented.

      We understand that a clear separation between experimental and modelling results is often preferred in papers that combine these approaches but in our case modelling and experimental data are highly interdependent and we believe that an overlapping presentation make it easier for the reader to appreciate the links. One example is Fig. 3G-L that shows experimental results validating a key feature of the model: the use of average response dynamics for each population of interneuron. Similarly, the results in Fig. 4 validate the use of the VIP response dynamics as the template for the slow modulatory input to layer 2/3. Then the results of optogenetic experiments in Fig. 5 are used to narrow down fits to the model. We have retained the integrated structure but revised the presentation throughout to clarify which findings are experimental, which motivate modelling assumptions and which are derived from the model.

      Reviewer #2 (Public review):

      (13) Lines 573-576 assert that given low numbers of PV and SST cells and low probabilities of their connection to PCs, simple random connectivity can give rise to the distribution of PV:SST input ratios on PCs inferred from the model - this is a hypothesis, and it would be simple to test it in simulations.

      This prompt has triggered a major addition to the paper. We find that variations in PV: SST input ratio predicted by the model are largely reproduced by simulations in which PV and SST connections are assigned randomly according to experimentally measured cell densities, connection probabilities and synaptic strengths. We now include this finding in the Abstract and Introduction and evidence it in a new section of the Results, “Random local connectivity as a driver of functional heterogeneity”, and the accompanying Fig. 8. This random connectivity rule provides a simple and parsimonious explanation for variations in PV and SST inputs, although in the Discussion we point out that we cannot rule out the possibility that more specific local connectivity rules also contribute to variations in the PV: SST input ratios that cause variations in adaptation across the PC population.

      In the model, they postulate that synapses within the 6-cell-type network - sensitizing, intermediate, and depressing E cells, and PV, SST, and VIP I cells - and from three sources of external input to each of the six types all change between rest and locomotion (except that connections between the E cells don't depend on their types). There are a lot of degrees of freedom, and this makes interpretation of the results difficult. I would have liked to have seen more efforts to constrain the degrees of freedom. For example, there seems to be very little difference between the three E cell types in any of the three types of external input received. Why not constrain them all to get the same external input and see if it significantly affects model fit? Or what if synapses from the three types of external input are left unchanged, and only change their strengths between rest and locomotion? How well could this do? During optimization, why not constrain the changes between rest and locomotion, for example, by putting an L1 penalty on the changes or the relative changes, trying to force them to be sparse, and see whether there are roughly equally good fits? And then, if the main changes are in a small set of synapses, can the authors isolate changes to that small set and do roughly equally well? What about looking at the principal components of the weight changes across models, to isolate patterns of change that are most important?

      We thank the reviewer for these suggestions; the additional dimensionality reduction analyses simplified the model and strengthened the conclusions drawn from it. We applied dimensionality reduction after the initial global sampling step by identifying weights that changed substantially from rest to locomotion. Because the model generated large ensembles of good solutions, conventional significance testing would be strongly influenced by the number of solutions and would not provide a meaningful measure of the magnitude of the differences. We therefore quantified each change using effect sizes, more specifically the normalized Mann–Whitney U statistic, U<sub>norm</sub> = U/(n<sub>1</sub>n<sub>2</sub>), equivalent to the Vargha–Delaney A effect size (Vargha and Delaney, 2000) (See Methods). Based on this criterion, we fixed nine weights showing no consistent change, and achieved similar model performance ( Values: Rest original = 2.9±0.0; Rest reduced = 2.9±0.0; Loco original = 9.2±0.01; Loco reduced = 8.1±0.03;) (Supplementary Table 3).

      We then examined whether any additional weights could be fixed. For this purpose, we performed principal component analysis on the original unrestricted solutions and examined the three weights with borderline effect size (w<sub>5</sub>, w<sub>6</sub> and w<sub>12</sub>). PC1 explained approximately 30% of the variance across solutions. Most weights fixed according to their effect sizes contributed little to PC1, whereas the weights that were kept variable generally made larger contributions (Supplementary Table 2). Among the borderline weights, w<sub>12</sub> made only a small contribution to PC1 and was therefore fixed, while w<sub>5</sub> and w<sub>6</sub> made substantial contributions and remained free to vary. The final reduced model therefore contained nine free weights, while maintaining a fit comparable to that of the unrestricted model. We have added the selection criteria and the results of these analyses to the Results and Methods sections.

      We followed a similar approach to determine which inputs meaningfully distinguished depressing and sensitizing PCs. In this case, the effect-size and PCA analyses did not identify a clear subset of parameters, likely because this comparison involved fewer variable inputs. We therefore tested reduced models with different combinations of fixed and variable weights and selected the simplest model that maintained a good quality fit. This result supports local SST and PV inhibition as the principal modelled distinction between depressing and sensitizing PCs. However, because external inputs were not measured experimentally, the reduced model should not be interpreted as evidence that these inputs are necessarily identical. We have clarified both the procedure and this limitation in the revised text.

      In relation to the L1 penalty, we tried an approach similar to that described (Dipoppa et al., 2018) by using the locomotion weights as initial conditions for the rest traces and introducing penalties at later optimization stages. However, the local optimization algorithms failed to reach distant regions of parameter space containing the good fitting solutions for the rest condition. Consequently, the outcome depended strongly on initialization and did not provide a reliable assessment of which changes could be constrained through an L1 penalty. We therefore fitted rest and locomotion using independent global searches and subsequently reduced the model using the effect-size, PC1, and model-refitting procedure described above. We believe this approach provides a robust and interpretable reduction because it has both allowed us to describe circuit changes during internal-state transitions (the present paper) and, more recently, it has made a series of predictions about different learning states that have been confirmed by optogenetic tests (Hinojosa et al., 2026).

      Action taken

      - Adding Supplementary Table 2 showing the effect sizes and PC1 values.

      - At line ~441, “To simplify the model, we then examined which parameters differed consistently between behavioural states using effect sizes and principal component analysis. This allowed 10 parameters to be constrained to the same values at rest and during locomotion without substantially reducing the quality of either fit (Supplementary Table 2; see Methods).”

      - At line ~608, “The simplest model that maintained a good-quality fit kept excitatory drive from PCs and all external inputs fixed and equal across the three PC types, restricting their differences to their local inhibitory connections (Fig. 7D,E)”.

      - At line ~885, “This reduced model provided the simplest account of the data; however, because external inputs were not measured experimentally, their equality across PC subpopulations should not be interpreted as evidence that they are biologically identical.”

      - At line ~1202, In Methods “To reduce the number of free parameters and attempt to fit a simpler model, we measured the magnitude of the difference between rest and locomotion for each parameter…”

      In terms of comparing to previous works, when optogenetic manipulations of SST and PV are done to test various hypotheses, I would like to see some discussion of what is already known from the authors' 2022 paper and what they are adding or testing that wasn't known or tested from that paper. And Dipoppa et al. (2018) also found weight changes to account for the difference between rest and locomotion. They were looking at a fixed point of responses of neurons across retinotopic space to stimuli of various sizes with only one E-cell type, whereas they are accounting for trajectories across time considering 3 E-cell subtypes but without variation in stimuli or retinotopic position of neurons, so the efforts are somewhat different, but still, it would be good to see a bit more discussion of what is in agreement or in contradiction in the conclusions.

      We have now added a section in the Discussion comparing our results with those of Dipoppa et al. (2018). In Heintz et al. 2022 we found that the proportion of depressors and sensitizers did not change significantly during locomotion, concluding through a qualitative analysis that this may be mediated by VIP->SST and SST->PV pathways. Here we have moved this analysis to a quantitative model to better understand how changes in external inputs to layer 2/3 interact with recurrent inhibition.

      Dipoppa et al. (2018) show that locomotion increases external inputs and reduces recurrent excitation, resulting in a reduced effective SST inhibition. We have come to a similar conclusion, but with more information about the dynamics of external inputs. A key difference, however, is that we find that the increase in VIP response amplitude is mostly mediated by external inputs rather than local PCs, We have included these comparisons in the Discussion.

      Action taken

      - At line ~803,” In a previous, smaller dataset, we qualitatively examined the effects of locomotion across the PC population and found that sensitizing and depressing responses remained balanced, consistent with recruitment of the VIP→SST and SST→PV pathways (Heintz et al., 2022). Our expanded quantitative analysis and modelling now suggest that locomotion acts through changes in both external inputs and recurrent connection weights. Similar circuit changes were inferred by modelling the initial responses of V1 neurons to stimuli of different sizes (Dipoppa et al., 2018). That study also predicted increased external excitation and reduced recurrent excitation, resulting in weaker effective SST inhibition, but attributed the locomotion dependent change in VIP responses to recurrent input from PCs rather than external drive…”

      (1) The main result is that sensitizers increase their responses with locomotion ~2X (for dF/F) or about 3.5X (for spikes) more than depressors. But there are other differences between sensitizers and depressors, for example sensitizers have smaller initial stimulus responses at rest, and depressors have larger. What if cells were divided into tertiles by initial stimulus response at rest? Would the authors see the same differences in the effects of locomotion? If so, can they establish whether the difference is really attached to the adaptation properties rather than to, for example, the initial responses, for example, by comparing the regression of response increase against AI vs the regression of response increase against initial resting response? And there might be other controls to be done for other features in which sensitizers and depressors differ.

      Thanks for highlighting this. In the manuscript, cells were categorized as sensitizers, intermediates, or depressors separately according to their adaptation index (AI) during rest and locomotion. Consequently, the traces shown in the previous Fig. 1D–F were not calculated from completely exclusive neuronal populations. We have now preserved cell identity by classifying neurons according to their AI during locomotion alone. This analysis reproduced the greater locomotion-induced gain increase in sensitizers (Fig. 1G), while revealing no difference between sensitizers and depressors in their initial response amplitude at rest (Fig. 1I).

      We further examined the relationships between the locomotion-induced response increase and either AI or initial response amplitude at rest. Response increase was strongly correlated with AI (Fig. 1H; R=−0.77, P<0.001), whereas its relationship with initial response amplitude differed between sensitizers and depressors (Supplementary Fig. 2B). When cells were binned separately according to their initial resting response, sensitizers showed greater response increases than depressors across the overlapping amplitude range. Response increase was positively correlated with initial amplitude among sensitizers but not depressors (Supplementary Fig. 2B). Thus, although initial amplitude influenced the magnitude of the response increase within sensitizers, it could not explain their greater locomotion-induced amplification relative to depressors, which was more strongly associated with their adaptive index.

      Action taken

      - Adding Fig. 1H.

      - Adding Fig. 1I

      - Adding Supplementary Fig. 2B.

      (2) Lines 103 and following: the authors refer to a "second notable change" which is the narrower distribution of adaptive effects, but I think this is trivial. The adaptive index is AI=(R1-R2)/(R1+R2), where R1 is response 0.5-2.5s after stimulus onset and R2 over 8-10s. But if the change is additive, as suggested by the dF/F figures (and I believe the distributions of AI here are based on dF/F measurements) -- adding the same constant to R1 and R2 will shrink |AI| without changing the sign of AI. So this would seem to just be a signature of a change that is primarily additive rather than multiplicative.

      Also, if the authors do decide that they are going to focus on spikes after showing the raw dF/F, then this analysis should be repeated for spikes.

      We thank the reviewer for pointing out that the narrower AI distribution can arise mathematically from an approximately additive increase in responses. We agree that it should therefore not be presented as a separate biological effect of locomotion. We have removed this point and its associated interpretation from the Results and now clarify this property of the AI calculation in the Methods.

      Additionally, we have included the corresponding AI distributions calculated from inferred spikes (Supplementary Fig. 3A). These distributions appear less smooth because spike inference algorithm excluded some of the cells and produces quantized response estimates, but the overall pattern is preserved. We have added this clarification to the manuscript.

      Action taken

      - Adding Fig. 1H.

      - Adding Fig. 1I.

      - At line ~1025, “The adaptive index (AI) was calculated from the GCaMP6f signal as AI = (R1 − R2)/ (R1 + R2) where R1 is the average response over the period 0.5 - 2.5 s after stimulus onset and R2 is the average at 8-10 s. As a result, adding the same constant to R1 and R2 will make all AIs closer to 0 which is what we observe from rest to locomotion.”

      (3) Figure 2, F is supposed to be D minus E, but it doesn't look like it. For example, the initial response under locomotion is very similar in sensitizers and depressors, so the initial difference in F should be small, but it's not; and at rest, depressors initially have larger responses than sensitizers, whereas later depressors have smaller responses than sensitizers, yet the difference at rest is positive at all times. Something seems wrong here.

      We apologize for the confusion. Previous Figure 2F did not represent the difference between sensitizing and depressing PCs from panels D and E. Instead, it showed the time-varying difference between locomotion and rest states of sensitizers (blue, in figure 2D) and depressors (green, in figure 2E). Thus, panel F showed within-population modulation by behavioural state, rather than differences between sensitizing and depressing neurons. After revising the paper, we do not think that this result is central to the main conclusions, so we have transferred the figure to Supplementary Fig. 3E. We have nonetheless amended the figure legend to better explain its nature.

      Action taken

      - At line ~1379, Supplementary Fig. 3E legend. “Time course of the locomotion-induced change in firing rate in sensitizing and depressing PCs.”

      Reviewer #3 (Public review):

      (1) Key concern is the usage of dF/F signals for all analyses, especially when comparing responses.

      (1a) Figure 1G: Comparison of sensitisers and depressors. It is important to consider what the baseline rates are when making these comparisons, especially when comparing the degree of effects between different cell types. For example, if baseline rates for sensitizers were overall higher, it would mean the difference in gain of response would be lower, and could affect the results in the opposite direction of what is claimed. One option to account for this would be to z-score the overall responses, using the same normalization for locomotion and rest. We also suggest plotting differences in sensitisers, intermediates, and depressors as a function of firing rate. Matching for firing rate across each PC categorization and calculating delta AI for each matched firing rate bin.

      (1b) Figure 2A-F: The above is an even more significant issue when it comes to estimating spiking rates. The methods do not state how dF/F is calculated. If these are based on using the pre-stimulus as the reference, the algorithms for spike rate used might not be appropriate if this were used. Using pre-stimulus referencing could result in the estimate going into the wrong range in the calculation of the spike rate.

      (1c) In both cases above, it could be a problem if baseline firing rates are different between cell types, or states (locomotion/stationary). The latter is established to have effects on many cell types measured, and so needs to be accounted for very carefully.

      The increase in gain does not depend on differences in noise levels across PC populations. We agree with the reviewer that noise levels must be considered to calculate the rate of gain change. We have now calculated the z-score on the original traces, before rest and locomotion trials were segregated, to account for a potential difference in baseline activity. Supplementary Fig. 2E and F reveal that baseline activity is similar in both locomotion and rest conditions.

      Initial response amplitude at rest does not differ between sensitizing and depressing PCs. In the previous manuscript we reported a difference in initial response during rest that was the result of dividing the rest and locomotion traces in sensitizers, intermediates and depressors based on AI calculated separately in each state. We have now preserved the cell identity in these classifications by sorting according to AI during locomotion alone: initial response amplitude during rest does not differ (Fig. 1I). We also binned sensitizing and depressing PCs separately according to their response amplitude during rest. Sensitizing PCs showed greater locomotion-related increases than depressing PCs across the overlapping range of initial response amplitudes. Although response increase was positively correlated with initial amplitude among sensitizers, this relationship was absent among depressors (Supplementary Fig. 2B). Thus, initial response amplitude influenced amplification within sensitizers but did not explain their greater amplification relative to depressors.

      Finally, ΔF/F was calculated from the raw fluorescence trace using the mode of the entire recording as F<sub>0</sub>, rather than the pre-stimulus fluorescence of individual trials. The same F<sub>0</sub> was therefore applied throughout the recording. This normalization preserves differences in fluorescence baseline between rest and locomotion and cannot shift individual trials into different ranges according to their pre-stimulus activity.

      Spike inference using MLSpike explicitly models baseline noise and subtracts its effect from that of the spikes calculated from the calcium signal (Deneux et al., 2016). This transformation preserved the difference in amplitude triggered by locomotion between depressing and sensitizing PCs while revealing their similar baseline activity (see Figs. 3E-I). These results indicate that the distinct changes in response amplitude between sensitizing and depressing PCs during locomotion are not driven by baseline differences. We have now added these clarifications to the Results and Methods sections.

      Action taken

      - Adding Supplementary Fig. 2E, F.

      - Adding Supplementary Fig. 2B

      - At line ~1009, Methods: “ΔF/F<sub>0</sub> was calculated from the raw fluorescence trace using the mode of the entire trace as F<sub>0</sub>”

      (1d) It would be informative to see per-neuron comparison for adaptive indices during rest and locomotion states. This could be visualized using a scatter plot with AI-rest vs. AI-locomotion for Figures 1D- 1F and 2J- 2L.

      (1e) Are neurons more strongly modulated between locomotion and rest, also more likely to experience a shift in AI indices (i.e. delta AI). Is there a correlation between the change in firing rate between behavioral states and Delta AI (Loco-Rest)? If so, is this present for all neuron subtypes (e.g. VIP, SST, and PV)?

      We have now added per-neuron comparisons of AI during rest and locomotion for PCs, VIP, SST and PV cells (Supplementary Fig. 2A,G-I). AI during rest and locomotion was significantly correlated in all cell types except SST cells, indicating that adaptation profiles were partially conserved across behavioural states.

      We also tested whether locomotion-related changes in response integral were correlated with ΔAI for each cell type (Supplementary Fig. 2C,J-L). In PCs, the change in response integral was negatively correlated with ΔAI, indicating that cells that become more sensitizing during locomotion experienced greater increases in response gain. Among interneurons, only PV cells showed a similar relationship between ΔIntegral and ΔAI, while these variables were not correlated in VIP and SST cells.

      Action taken

      - Adding Supplementary Fig. 2A, G-I

      - Adding Supplementary Fig. 2C, J-L

      (1f) Optogenetic inhibition of VIP neurons on average abolished the slow depressive effects of adaptation in SST (Figure 3). The strength and prevalence of this effect are unclear. Perhaps one can perform a bootstrap control and opto AI indices and calculate whether AI was significantly reduced following optogenetics inhibition, and if so, on average, how likely was this to occur for the recorded SST neurons? This is important in knowing that the average effects (Figure 3D) aren't driven by a portion of SST neurons, especially as this is later used to confirm the region of parameter space and affects the subsequent results in Figure 4.

      Because AI values with and without VIP inhibition were obtained from the same SST neurons, we assessed the effect using a paired linear model rather than bootstrapping the two conditions. VIP inhibition significantly reduced SST AI (Fig. 4E; Control AI = 0.44 ± 0.04; Opto AI = 0.12 ± 0.02; p < 0.001). We have also added a histogram of the within-cell change in AI (Fig. 4F), showing that this reduction occurred in 90% of the recorded SST neurons rather than being driven by a small subset. These analyses confirm that the average response reflects a loss of slow depression across the SST population.

      Action taken

      - Adding Fig. 4E,F.

      (2) Statistics for the effects. There is a mention of Liner mixed models, but no information is given on the actual models being used and tested. This is particularly for the case of Figure 1G, where there is a composition of effect sizes between different populations. What precise significance test is being used? Are the stats on paired cells when considering locomotion and rest?

      We used linear mixed-effects models to account for the hierarchical and paired structure of the data. For Fig. 1G, locomotion state, adaptive type, and their interaction were included as fixed effects, with mouse and cell identity as random effects. Thus, comparisons between rest and locomotion account for measurements obtained from the same cells. We tested differences among adaptive types separately within each behavioural state and differences between states separately within each adaptive type. The reported interaction (p < 0.001) indicates that the locomotion-related increase in amplitude differed between sensitizers and depressors. We have now revised the Methods section and figure legends to explicitly describe the model and statistical test used.

      Action taken

      - At line ~1312, Methods: “Locomotion state, adaptive type, and their interaction were included as fixed effects, with mouse and cell identity as random effects. We tested differences among adaptive types separately within each behavioural state, differences between states separately within each adaptive type, and finally the interaction between behavioural state and adaptive type which indicates whether the locomotion-related increase in a given variable differed between sensitizers and depressors…”

      (3) Model parameters: It is acknowledged that there is a large range of parameters that can model the responses effectively, up to 11% of initial conditions. At 9000 initial conditions, this is around 1000. The parameter estimates are then considered as the mean of each parameter. This seems like a strange choice for a few different reasons:

      (3a) A mean solution might not be one of the solutions. Let's say the parameters range over a large dimensional space. They could occupy non-overlapping / discontinuous subspaces. In that case, the mean parameters do not necessarily fall within the solution subspaces. Therefore, this reduction to means might not be valid.

      (3b) Compare distributions rather than means. There are multiple distributions of parameters between conditions. All stats should be on the comparison of distributions rather than just the means.

      We agree that a limitation of our previous presentation was that it did not reflect the full range of solutions produced by the model. We now report both the whole population of solutions and describe the differences associated with locomotion in term of their effect sizes rather than averages alone. Most parameter distributions were approximately Gaussian or showed a monotonic decay when distributed close to 0 (Supplementary Fig. 4). The only exception was the PC->SST connection, which was described by two overlapping Gaussian components. Importantly, both components were similarly displaced towards lower values during locomotion (Supplementary Fig. 4E, change in Gaussian centre: component 1 = 0.5, component 2 = 0.47). This bimodality could potentially reflect heterogeneity among SST interneurons and is highlighted in the Discussion.

      To test for meaningful differences, conventional significance testing would be strongly influenced by the number of solutions, which are not independent biological observations. We therefore quantified changes taking into account effect sizes, more specifically the normalized Mann–Whitney U statistic, U<sub>norm</sub> = U/(n<sub>1</sub>𝑛<sub>2</sub>), equivalent to the Vargha–Delaney A effect size (Vargha and Delaney, 2000) (See Methods). We considered a substantial difference when 0 < U<sub>norm</sub> < 0.3 or 0.7 < U<sub>norm</sub> < 1.

      Our original use of the mean was based on the fact that introducing the average for each parameter in the overall model, rendered a solution that would be classified as a “good fit” by our criteria criteria (rest < 3, locomotion < 12). Given this validation and the predominantly unimodal parameter distributions, we have retained the means in the main figures as a concise summary while providing the complete distributions in Supplementary Fig. 4.

      Action taken

      - Adding Supplementary Fig. 4.

      - At line ~517, “Moreover, examination of the distribution of each parameter revealed that they were mostly unimodal (Supplementary Fig. 4)”.

      - At line ~844, Discussion: “In line with this heterogeneity, the PC→SST connection showed a bimodal distribution at rest, with both components shifting similarly towards lower values during locomotion.”

      (4) Visualizing weight matrices: It is very challenging to interpret the weight matrices. Furthermore, it appears that the stationary and locomotion conditions fit independently, and given the large parameter spaces, it is even harder to interpret. Can the fitting instead be done by fitting on one and using those at the initial conditions for the other state? Figure 7 shows an initiative cartoon, but it is not clear how the matrices in Figures 5 and 6 lead to the summary shown in Figure 7. It is also not clear why the connections between inhibitory neurons are not shown in Figure 7. One option is to perhaps run some kind of dimensionality reduction on the parameter space to better interpret the data. When showing delta Weights, was the model initialised with 'Rest' weights and allowed to change? It is not obvious what the difference is between 'relative change in connection weights' and 'relative change in synaptic weights'. This needs to be clarified.

      Thanks for raising these concerns, which prompted us to substantially revise the model presentation and analysis. We applied dimensionality reduction after the initial global sampling step by identifying weights that changed substantially from rest to locomotion. We quantified each change using normalized Mann–Whitney U statistic, U<sub>norm</sub> = U/(n<sub>1</sub>n<sub>2</sub>) (See Methods) and then examined whether any additional weights could be fixed by performing principal component analysis on the original unrestricted solutions and examining the three weights with borderline effect size (w<sub>5</sub>, w<sub>6</sub> and w<sub>12</sub>). PC1 explained approximately 30% of the variance across solutions. Most weights fixed according to their effect sizes contributed little to PC1, whereas the weights that were kept variable generally made larger contributions (Supplementary Table 2). Among the borderline weights, w<sub>12</sub> made only a small contribution to PC1 and was therefore fixed, while w<sub>5</sub> and w<sub>6</sub> made substantial contributions and remained free to vary. Based on these criteria, we fixed a total of 10 weights showing no consistent change and achieved similar model performance ( values: Rest original = 2.9 ± 0.0; Rest reduced = 2.9 ± 0.0; Loco original = 9.2 ± 0.01; Loco reduced = 8.1 ± 0.03; Supplementary Table 2). We have added the selection criteria and the results of these analyses to the Results and Methods sections, simplifying the weight matrices and facilitating its interpretation.

      We previously tried an approach similar to that described by Dipoppa et al.(2018) by using the locomotion weights as initial conditions for the rest traces and introducing penalties at later optimization stages. However, the local optimization algorithms failed to reach distant regions of parameter space containing the good fitting solutions for the rest condition. Consequently, the outcome depended strongly on initialization and did not provide a reliable assessment of which changes could be constrained through penalties. We therefore fitted rest and locomotion using independent global searches and subsequently reduced the model using the effect-size, PC1, and model-refitting procedure described above. We believe that this approach provides a robust and interpretable reduction because it has both allowed us to describe circuit changes during internal-state transitions (the present paper) and, more recently, it has made a series of predictions about different learning states that have been subsequently supported by optogenetic experiments (Hinojosa et al., 2026).

      As a summary to facilitate the interpretation of our results, Fig. 9 (former Fig. 7) puts together the inferred changes in connectivity from Fig. 6 and the differences between depressors and sensitizers (Fig. 7). The reduced model is now easier to summarize in this figure: the schematic focuses on the local connectivity changes from Fig. 6F, and added the change in SST→PC and PV→PC connectivity that differs between sensitizing and depressing PCs from Fig. 7. We have also added the inferred changes in interneuron-to-interneuron connectivity, namely the SST→VIP increase with locomotion, as well as the external connections. We revised the figure legend to link each element of the schematic more clearly to the corresponding quantitative results.

      Finally, relative weight changes were calculated using Equation 4, based on the rest and locomotion weights obtained from independent fits. “Connection weights” (Equation 2), describe the total strength of the connection from population j to population i. “Synaptic weights” (Equation 3) defines the strength of individual synapses by dividing the connection weight by the number of presynaptic cells and the connection probability. This distinction is necessary because the model was fitted to responses averaged across all imaged neurons, whereas estimating the strength of individual synapses requires accounting for both the number of presynaptic cells and their probability of connection. We have added this explanation to the Results and Methods sections, more clearly differentiating between both types of weights.

      Action taken

      - Adding Supplementary Table 2 showing the effect sizes and PC1 values.

      - At line ~441, “To simplify the model, we then examined which parameters differed consistently between behavioural states using effect sizes and principal component analysis. This allowed 10 parameters to be constrained to the same values at rest and during locomotion without substantially reducing the quality of either fit (Supplementary Table 2; see Methods).”

      - At line ~608, “The simplest model that maintained a good-quality fit kept excitatory drive from PCs and all external inputs fixed and equal across the three PC types, restricting their differences to their local inhibitory connections (Fig. 7D,E)”.

      - At line ~1202, In Methods “To reduce the number of free parameters and attempt to fit a simpler model, we measured the magnitude of the difference between rest and locomotion for each parameter…” - Updated Figure 9 and its legend.

      (4a) Model parameters were reduced differently for locomotion and rest (Figure 4). We suggest evaluating the results for locomotion and rest using the same chi-square value of 3 for both behavioral states (at least in controls).

      Setting the same chi-square threshold across conditions would not correspond to an equivalent goodness-of-fit criterion. As defined in equation 12, reduced chi-square is inversely proportional to the standard error of the data which is higher in the rest condition compared to locomotion. As a consequence, the same chi-square threshold would impose a disproportionately strict constraint on the condition with lower variability, where deviations between model and data are more heavily penalized. For this reason, we used condition-specific thresholds to ensure comparable fit quality relative to the noise level in each condition. In addition, to enable direct comparison across conditions independent of their noise levels, we used the RMSE as a complementary metric. We now explain these different metrics in more detail in the Methods section.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      (1) The authors use high-contrast, very long stimuli. This should be specified early on in the results and discussed in terms of how it could influence the results.

      At line ~116, we have added: “The GCaMP6f signal in PCs responding to a prolonged, high-contrast stimulus (20º drifting grating at 1 Hz, 10 s duration) are shown in Fig. 1B”.

      At line ~813, we have added to the discussion “We used prolonged, high-contrast stimuli to provide a high signal-to-noise ratio and reliably evoke slow adaptation, whereas stimuli of different durations or contrasts may engage different patterns of locomotion-dependent modulation.”

      (2) In lines 24-25 (Abstract), the authors write: "These results demonstrate that behavioural state selectively shifts cortical computation toward distinct adaptive regimes". This statement is vague and hard to grasp. Consider rewriting.

      We have made this statement more precise in the new version of the abstract.

      (3) In line 96, the authors should include a brief description of the adaptive index metric.

      At line ~133, we have added: “This was calculated as AI = (R1 − R2)/ (R1 + R2) where R1 is the average response over the period 0.5 - 2.5 s after stimulus onset and R2 is the average at 8-10 s (AI; Methods).”

      (4) In line 85, the authors write: "Locomotion increased the response averaged across all PCs by a factor of 2.2 (plus minus) 0.9". Yet, in lines 99-101, they write "but the amplitude of the visual response increased by a factor of 4.5 (plus minus) 0.7 in sensitizing PCs, 2.5 (plus minus) 0.3 in intermediate group and 2.2 (plus minus) 0.2 in depressors". How can the average across all neurons be 2.2 if all the groups have an increase factor equal to or higher than that, and each group represent a third of the population?

      We thank the reviewer for identifying this inconsistency. After preserving cell identity by classifying PCs according to their AI during locomotion, we recalculated the response increases. The response averaged across all PCs increased by a factor of 1.9 ± 0.2, while the increase was 2.1 ± 0.4 in sensitizing PCs and 1.7 ± 0.3 and 1.7 ± 0.4 in intermediate and depressing PCs, respectively. These values have been corrected in the revised manuscript.

      (5) Figures 1F and 2C do not seem to agree. In Figure 1F, there is a clear increase in response across time in locomotion vs resting, while in Figure 2D, this increase is smaller and only appears in the very late phase. How do the authors explain this? Does it have to do with the spike inference and the different temporal resolution? (Figure 2C loco (calcium) is different from Figure 1F).

      These differences are indeed related to the spike-inference method (but not to a difference in temporal resolution – they are the same). Spike inference revealed the initial rapidly adapting phase of the visual response that was not evident in the calcium signal but is well-documented electrophysiologically. Better definition of this peak reduced the apparent difference between rest and locomotion during the early phase of the response in depressing PCs. Note, however, that the difference in rest and locomoting responses quantified by spike inference remained clear during the later, slower, phase of the visual response.

      (6) The authors observe that SST interneurons do not change their response magnitude during locomotion (Figure 2I, L). How do authors explain their results compared to Dipoppa et al., 2018and Pakan et al., 2016?

      There is a key potential difference between our analysis and that of Dipoppa et al., (2018) and Pakan et al., (2016): we focused throughout on mice that were naïve to the visual stimulus (i.e. the first imaging session) whereas these other studies did not report visual-exposure history or control for session number. We have observed greater locomotion-related modulation of SST responses in later sessions, consistent with experience-dependent changes, and these are now described in the context of a study focusing on the changes associated with simple forms of learning, which is now referenced (A.J. Hinojosa, S.E. Dominiak, Ye. Kosiachkin, L. Lagnado (2026). Distinct Disinhibitory Circuits Link Short-Term Adaptation to Familiarity and Reward Learning in Visual Cortex. bioRxiv 2026.03.24.713929; doi: https://doi.org/10.64898/2026.03.24.713929). The Methods now contains the sentence: “We only analyzed responses to the first day of imaging in mice naïve to the stimulus to limit the introduction of longer-term changes in circuit function reflecting simple forms of learning such as habituation (Hinojosa et al., 2026)”. Differences in stimulus duration and presentation protocols may also contribute to the contrasting results.

      (7) In line 250, the authors state they modelled the feedback of higher visual areas with a 380ms delay after stimulus onset. Yet there is no reference for previous literature supporting this. Why did they choose this delay specifically? In the main text, it says 380ms, whereas in the supplementary material, it is 370ms.

      We modelled feedback with a delay because top-down signals in V1 have been shown to emerge after the initial feedforward response (Kirchberger et al., 2023). However, the 370-ms delay in our model was not intended to represent the minimal axonal transmission delay reported in that study. Rather, it was selected from our experimental responses as the onset of the delayed SST response that the feedback input was introduced to reproduce. Because SST responses became approximately flat when VIP influence was removed, we inferred that their remaining delayed drive arose primarily from feedback, consistent with evidence that LM to V1 feedback strongly targets L2/3 SST interneurons. We have now clarified this rationale, added the relevant references (at line ~360), and corrected the inconsistent value of 380 ms to the correct one of 370 ms.

      (8) In lines 307-309 authors declare: "This third stage could not be usefully applied to data at rest because there were not enough recording episodes across all four optogenetic conditions and responses were smaller and more variable than during locomotion". Does this mean that the model fit better represents synaptic weights during locomotion than during the static state? How can this influence the conclusions drawn from the model?

      We agree that the absence of the third, optogenetic filtering stage at rest means that the inferred rest weights are less strongly constrained than those during locomotion. We did not apply this third step to the rest data because of the lower response amplitudes, smaller number of responsive cells, and smaller number of stimulus trials across all four optogenetic conditions. Nevertheless, the rest data provided sufficiently reliable population responses for the initial model fitting; only their subdivision by optogenetic condition produced traces that were too variable for meaningful additional filtering. We have therefore clarified that the inferred weights should not be interpreted as equally precise estimates of synaptic strength in the two states (at line ~451). The lack of optogenetic filtering at rest increases uncertainty in the magnitude of these changes but does not invalidate the model’s conclusions.

      (9) Are the results presented in Figure 5F a time integral of the connection weights changes?

      No. Figure 5F shows the relative difference between the mean connection weights inferred independently at rest and during locomotion, calculated as:

      Connection weights are time-independent parameters within each condition and were estimated by fitting the model to the full time course of the population responses; therefore, no temporal integration of the weights was performed. We have clarified this in the figure legend: “6F. Relative change between the time-independent connection weights inferred at rest and during locomotion (Equation 4).”

      (10) In lines 435-437, the authors state: "Notably, the model predicted almost zero net change in total input to SSTs, consistent with the negligible change in SST activity observed experimentally (Fig. 2I) but inconsistent with the simple VIP->SST->PC disinhibitory model". The authors should discuss how temporal patterns of activation, depending on nicotinic versus metabotropic receptors, could explain these results. E.g., SSTs inhibit VIPs, and the dynamic of this loop would only be revealed in the ms timescale.

      We thank the reviewer for this suggestion. Our revised analysis indicates that net input to SSTs decreases during locomotion, consistent with increased VIP inhibition, although average SST activity changes little. As the reviewer suggests, rapid nicotinic activation of VIPs could produce a brief SST suppression that is not resolved by our calcium recordings, while slower metabotropic or recurrent effects may subsequently compensate for it. Averaging across the stimulus could therefore obscure these dynamics. We have added this possibility and the temporal limitations of our model to the Discussion (at line ~823).

      (11) Based on the results shown in Figure 6F, the authors conclude that sensitizers are dominantly inhibited by SSTs and depressors by PVs as previously reported. However, Figure 6F only shows differences during SST inhibition and PV activation but not the rest of the manipulations. How do the authors interpret this? How does this relate to previous reports?

      We agree that our original conclusion was too strong. Significant differences between sensitizers and depressors were observed during SST inhibition and PV activation, whereas SST activation and PV inhibition showed tendencies in the predicted direction but were more variable. We therefore interpret these results as qualitative support, rather than confirmation, that sensitizers are more strongly influenced by SSTs and depressors by PVs, and have revised the text accordingly. The previous report referred to Heintz et al. (2022), which showed that SST and PV interneurons promote sensitizing and depressing adaptation, respectively, leading to the proposal that PC adaptation depends on the balance between these inhibitory inputs. Our present results extend this model by suggesting that sensitizing and depressing PC subpopulations differ in their relative sensitivity to SST and PV manipulation. We have now toned down this statement (at line ~638).

      (12) Figure 6G shows a preferential reduction of the dominant source of inhibition (SSTs for sensitizers, PV for depressors). Can this be explained by a regression-to-the-mean kind of phenomenon? The higher the inhibition from one source is, the more it can be reduced.

      The shifts are not attributable to regression to the mean across model solutions, because no solutions were selected according to extreme weight values and the complete distributions, rather than only their extremes, shifted between conditions. We have added Supplementary Fig. 5 to show this. We agree, however, that a stronger inhibitory input has greater scope for reduction, such that a broad weakening of PV and SST transmission can produce a larger effect in the PC population that depends more strongly on that input. Differences in the preexisting PV balance make depressors more sensitive to reduced PV inhibition and sensitizers more sensitive to reduced SST inhibition. Therefore, the baseline connection strength likely contributes to the magnitude of the reduction. We have clarified this possibility in the Discussion section (at line ~867: “More generally, a broad weakening of inhibitory transmission would have a greater functional impact on PCs receiving stronger baseline input from that pathway, without requiring selective modulation of those connections”).

      (13) Discussion lines 500-502 should be moved to the beginning of the results section, when describing the two populations of excitatory neurons with different response patterns.

      The first paragraph now ends “Previous work has shown that receptive field location and orientation tuning are not significantly different between depressing and sensitizing PCs (Heintz et al., 2022)”.

      (14) Figure 1: overlap between sensitisers, intermediate and depressors: choose a bin size that matches the cut-off for the different categories? Do neurons switch from rest to locomotion?

      Figure 1C shows the same matched population of neurons, but ranks their AI values separately within each state to compare the state-specific distributions of adaptive properties. We have now adjusted the bins for each category as suggested. We have also performed the same binning for spike inferred traces (Supplementary Fig. 3A). The paired comparison in Supplementary Fig. 3A directly shows how individual AI values change between rest and locomotion. In the remaining Figure 1 analyses assessing locomotion-related gain differences, PCs are classified according to their AI during locomotion, and the same cell identities and classifications are retained when analysing their responses at rest.

      (15) Row 405: "25-50% reduction", but in Figure 5G, it is between 22% to 51%.

      We have now changed the values to accurately match the new Figure 6 (18-60%).

      (16) Statistics for Figure 6F and the number of cells accounted for were not well described.

      This has now been reported in the legend of Figure 7F.

      (17) Figure 7 is a bit misleading to read. The figure shows a dramatic difference between Depressors at rest and in locomotion, but the actual results did not show such a big change in PV inputs.

      We thank the reviewer for pointing out that the schematic could give the impression that line thickness represents the magnitude of the inferred changes quantitatively. Figure 7 (now 9) is intended as a qualitative summary of the main circuit differences rather than a scaled representation of connection weights. We have now clarified this explicitly in the figure legend. The quantitative changes in PV and SST inputs are shown in Fig. 6.

      Reviewer #2 (Recommendations for the authors):

      (1) Lines 68-69, "Contrary to the prevailing model ... we find that visual responses in SSTs are not inhibited by locomotion but instead weakly enhanced." That was clearly established in Dipoppa et al. (2018) and probably in other papers as well.

      We agree that “prevailing model” overstated the contrast with previous literature. We have therefore revised the sentence to refer more specifically to “a simple model of gain control through the VIP→SST→PC pathway”.

      (2) You call the change in response to locomotion an increase in "gain". Gain usually refers to a scaling, i.e. a multiplicative change, whereas from your Figure 1D-F it looks far more additive, i.e. a roughly constant factor added to the time-varying response. It would be clearer to, for example, just talk about response increases rather than gain increases.

      A related problem is that you use various language to describe responses -- the 'amplitude', which in line 93 is defined as the integral over 10 sec of the dF/F response, but is used in different ways, sometimes without any definition (for example in Figure 6F), throughout the text; you show both dF/F response, and the inferred spike rate response, which are qualitatively different in some ways, without commenting on these differences, or telling us what we should really believe. Re differences: the numbers in lines 100-101 (for dF/F) are different from those in 164-166 (for spikes), particularly for depressing E cells, but the numbers are just presented without any comparison or reference to one another; Figures 2D-E (for spikes) are pretty different from Figures 1D,F (for dF/F), but again, no comment on this, no comparison, no reference from one to the other. While it's good to see the raw dF/F as well as the inferred spikes, it would help to note the differences and say what you believe best represents the biology, e.g. the spikes, and stick to that thereafter (unless there is some specific reason to show the other, in which case you should explain that reason).

      We agree that “gain” was used too broadly in the manuscript. We have therefore replaced “gain increase” with “response increase” or “response amplification” where referring to our experimental measurements. We have also clearly distinguished between amplitude and integral, while using “response” as a general term where applicable and clearly defining the specific measure used beforehand.

      We agree that the rationale for presenting both calcium responses and inferred spike rates was not clear enough and have corrected this. Inferred spike rates provide a better representation of the temporal dynamics of electrical activity, particularly the initial fast component of adaptation that is obscured by the kinetics of GCaMP6f. We therefore use inferred spikes when analysing these temporal dynamics. However, spike inference results in quantized responses and consequently distorts the distribution of AI values towards the extremes (Supplementary Fig. 3A). We therefore used the directly measured calcium signals for population-level analyses of adaptive properties and their dependence on locomotion speed (Fig. 1 and 2). Importantly, both measures support the same central conclusion that locomotion preferentially increases responses in sensitizing compared with depressing PCs (Supplementary Fig. 3B and D).

      (3) Lines 95-97: "we split the population into three groups of equal size" according to adaptive index (AI), i.e. into tertiles; but then "These groups were sensitizing (AI less than zero), intermediate and depressing (AI more than zero)" -- the parenthetical AI<0 and AI>0 are wrong, and confusing, make it sound like the division is by sign and there is no intermediate group. This problem also shows up in Figure 2A legend, where you say "averaged across all sensitizing PCs" when it's actually averaged over the most sensitizing tertile.

      This has now been corrected. We have changed the definition of the three groups so that sensitizing cells clearly means the most sensitizing PCs with the most negative AI. We have adjusted the legend to Fig. 3 accordingly.

      Interneurons have more consistent adaptive properties so we kept the distinction between sensitizers and depressors based simply on the sign of their adaptive index. We have explained this distinction accordingly. Line ~284: “Unlike PCs, interneurons were not divided into tertiles but were classified as sensitizing or depressing according to whether their AI was negative or positive, respectively.”

      Finally, we have removed this calculation to avoid confusion: “The probabilities of a PC being sensitizing (AI <0, P<sub>sens</sub>) or depressing (AI > 0, P<sub>dep</sub>) were both ~0.5”.

      (4) Equation 1 and thereafter, your notation is very awkward and non-standard. It is standard to call the connection from j to i w_ij, which makes sense since the entry of the weight matrix that multiples j's rate to determine the input to i is the matrix entry labeled w_ij, i.e. the total input to neuron i is \sum_j w_ijr_j. But you label it w_ji. You're entitled to your own notation if you insist, but it is very non-standard and so confusing. Similarly, the expression w_inIn is awkward, "In" looks like I times n, and it doesn't indicate there are multiple sources of input. You have three different sources of input, so why not write this term as \sum_i w^in_i I_i where i runs from 1 to 3 and I_i (or h_i or some other letter of your choice) represents the activity of the i^th external input?

      We have now made this adjustment in line with standard matrix notation. Subscripts follow the convention w_ij, with the postsynaptic population listed first and the presynaptic population second (e.g. w_(PC,SST) denotes the SST→PC connection). We have also revised the notation for external inputs, which are now explicitly represented as a sum over , where h<sub>k</sub> is the activity of external input k and its connection weight onto postsynaptic population i.

      (5) On line 217 you describe C_ji as the total number of synaptic connections from cells of type j to those of type i, but just a little ways down in Equation 3 you define it as N_j p_ji which is the expected number of ‘connections’ from ‘responsive’ cells of type j to cells of type i. Please define it correctly to begin with; this is very confusing.

      We thank the reviewer for identifying this ambiguity. We have now defined C<sub>ij</sub> at its first appearance as the number of connections from responsive presynaptic cells and explicitly stated that C<sub>ij</sub> = N<sub>j</sub>p<sub>ij</sub>, where N<sub>j</sub> is the number of responsive presynaptic cells and p<sub>ij</sub> the connection probability.

      (6) In lines 217-218 you write "average strength of an individual synapse between neuron type j and i", 'between' should be 'from'.

      This has now been changed.

      (7) Lines 225-227, for "a PC and a nearby PV interneuron the probability of them being connected is ..." -- you need to specify the direction, PC to PV or PV to PC. "... while the average probability of an SST interneuron is ..." -- probably of what -- of the SST neuron getting an input from a nearby PC? Projecting to it? Something else?

      This has now been corrected to specify the direction of each connection from PV and SST to PCs.

      (8) Figure 3A: You should explain some of your model assumptions. For example, why do SS inputs not go to SST cells? You say (line 276) these include inputs from higher visual areas (HVAs), and SST cells definitely get inputs from HVAs (Shen, ..., & Tolias, 2022). Why no PV- >SST connections (these are seen with comparable strengths to other connections in some studies, not in others). Figures 3C, D: Are these locomoting or at rest? Figure 3E, why is the SS input modeled on VIP response in locomotion, rather than at rest, or the difference between locomotion and rest, or something else?

      We thank the reviewer for pointing out that these model assumptions were not sufficiently explained. The SS input was introduced to reproduce the strong sensitizing dynamics observed in VIPs during locomotion, which were greatly reduced at rest. We did not include a direct SS→SST connection because optogenetic silencing of VIPs largely abolished slow adaptation in SSTs indicating that a separate direct SS input to SSTs was not required to reproduce these dynamics (Figs. 4C-F). This does not imply that SSTs do not receive inputs from HVAs; accordingly, the model includes a separate FB input to SSTs, we have clarified that the anatomical origin of the SS signal remains uncertain (At line ~406). We have also clarified that traces in Figs. 4C-F correspond to the locomotion state.

      We excluded PV→SST connection because it was reported to be very weak in mouse V1 (Pfeffer et al., 2013), although we acknowledge that other studies have reported stronger connectivity (Jiang et al., 2015). We have now clarified that its exclusion represents a simplifying assumption of the model (at line ~423).

      (9) Model: Please tell us in the main text how many solutions you averaged over for rest and for locomotion. From lines 328-329, it sounds like there were about 990 for locomotion? What about at rest? And tell us if the fits for rest and for locomotion are done completely independently or have some dependence - you may say that in the Methods and I have missed it, but in any case, it would be nice to have that info in the main text. As I mentioned above, in addition to the mean weights, it would be nice to show the first few PC's of the weights, if they capture most of the variance across models.

      The final sets comprised 1007 solutions for locomotion and 11657 solutions for rest, fitted independently to the average visual responses of the four cell types. We have now clarified this in the main text.

      We also performed PCA on the fitted weights; however, the first PCs did not provide a low dimensional representation of the solution space, with PC1 explaining ~30% of the variance and the first three PCs together only ~50%. We therefore did not consider visualisation of the first few PCs particularly informative.

      (10) Figure 6: G, H are relative change in locomotion vs. rest; but I says "Change in total input during presentation of the stimulus". This is ambiguous. Is this the change with locomotion in the presence of a stimulus - or the change in response induced by presenting a stimulus, perhaps at rest? Is this any different from the conditions being compared in G and H - are they without a stimulus? If they're all comparing the same two things, please use the same description for them. If 6I is different in what it's comparing than G & H, explain so and explain why. More generally, please make what you're comparing clear and unambiguous.

      We apologise for the ambiguity. Panels G and H show relative changes between locomotion and rest, whereas panel I shows the absolute change (locomotion − rest), as absolute values are required to sum the individual inputs and calculate the net change in total synaptic input. We have revised the figure legend to make this distinction explicit. We have also removed the reference to stimulus presentation, as that is valid for all the results presented in the paper.

      (11) But, if Figure 6I is the change with locomotion vs rest: then how is the change in net input being similar, but even larger, for depressing E-cells vs sensitising ones, consistent with the sensitizing ones showing a much larger increase in response with locomotion?? Please explain.

      Following dimensionality reduction and refitting, the net input now shows a slightly larger locomotion-associated increase in sensitizing than depressing PCs, although this difference is not significant relative to the variability across solutions (U<sub>norm</sub> = 0.4). We have clarified this point and discuss a potential explanation for the remaining discrepancy: our rate model treats inhibition as subtractive, whereas SST inhibition can act divisively. The model may therefore underestimate the effect that a reduction in SST inhibition has on PC responses, particularly in sensitizing PCs.

      (12) Also, here and elsewhere, you give RMSE's. But this is the square root of the sum of the squared differences of all parameters; the number doesn't have any intrinsic meaning, for example, since it depends on how many parameters there are, and weights all differences equally, no matter how big the relative difference and no matter how big the standard error. So the number tells us nothing, except that it's bigger in some cases and smaller in others. Why not use numbers that have some meaning, for example, the Chi-squared reduced, which divides by N, roughly, and also by the standard error; perhaps even better, divide by the data value to get the relative error, and again, per parameter, i.e. divided by N.

      We agree that RMSE does not account for the uncertainty of individual data points and therefore should not be interpreted as a statistical goodness-of-fit measure. We used reduced χ² for model fitting and selection, where weighting by experimental uncertainty is appropriate. As already defined in the Methods, RMSE was additionally used as a descriptive measure of absolute fit error independent of data uncertainty and the number of varied parameters, but dependent on the number of data points N. This allowed comparison across analyses with different uncertainty structures. We have clarified this distinction in the revised text (At line ~1163).

      (11) Line 490-491: Locomotion has "minimal effects on depressing PCs (Figures 1 and 2) - well, that's true for spikes (Figure 2), but not for dF/F (Figure 1) - say this more precisely.

      We have toned down this line to say “smaller effects on depressing PCs”.

      (12) In Figure 7, Summary, it would be helpful to show the external input to each cell type.

      We have now included in the summary figure the external input connections that showed meaningful changes in the model, while omitting unchanged inputs for simplicity.

      (13) Lines 573-576 assert that given low numbers of PV and SST cells and low probabilities of their connection to PCs, simple random connectivity can give rise to the distribution of PV:SST input ratios on PCs inferred from the model - this is a hypothesis, and it would be simple to test it in simulations.

      Thank you very much for this prompt, which has triggered a major addition to the paper. We find that variations in PV:SST input ratio predicted by the model are largely reproduced by simulations in which PV and SST connections are assigned randomly according to experimentally measured cell densities, connection probabilities and synaptic strengths. We now include this point in the Abstract and Introduction and evidence it in a new section of the Results, “Random local connectivity as a driver of functional heterogeneity”, and the accompanying Fig. 8. This random connectivity rule provides a simple and parsimonious explanation for variations in PV and SST inputs, although in the Discussion we point out that we cannot rule out the possibility that more specific local connectivity rules also contribute to variations in the PV:SST input ratios that cause variations in adaptation across the PC population.

      (14) Line 579: "the number of" should be omitted.

      Done.

      (15) Methods: Line 645, what was the spatial frequency of the gratings? Lines 659-660: How many/what percentage of cells of each type were excluded? Line 696, omit 'linear'. Fitting the model, lines 763 and following: you are fitting the average time traces - how many & which time points are you fitting? As you mention somewhere, most of the average traces show some signs of the 1Hz grating frequency. Are the models penalized for not fitting these wiggles, or do you use some smoothed version of the traces, or sample time in a way to avoid the 1Hz oscillations? Line 776, give the values of N_v and N. Lines 772 and 779-780, repeat the same information about standard errors. Line 836, omit 'in'.

      We have now added information about spatial and temporal frequency (line ~996), the percentage of excluded non-responsive cells (line ~1019) and the time points being fitted (line ~1164).

      As described in the Methods, the 1 Hz oscillations are prominent in individual PC responses but are strongly reduced in the population averages because cells with receptive fields at different locations respond at different phases of the grating. Modulation at 1 Hz remains visible in average response of the SST population because these have larger receptive fields and phase differences are smaller. We therefore fitted the population-average traces without explicitly modelling the 1 Hz component. We have also added the values of N and N<sub>v</sub> for the unrestricted four-population fit and made the rest of corrections pointed out by the reviewer in this question.

      (16) Supplementary Figure 4: I can't figure out what these sentences are saying "... and their corresponding fits from the solution with lower (RMSE=0.14) calculated by a model without slow-sensitising (SS) input" and "Same as in A for missing feedback input (FB) (RMSE=0.14)". A solution with lower what? Does the RMSE=0.14 refer to the model before removing the given input, or after? What's the significance of RMSE=0.14? Was that the lowest RMSE across models before omitting inputs, or does it have some other significance?

      RMSE = 0.14 refers to the best-fitting solution obtained after removal of each respective input. We have revised the legend to make this clearer.

      Reviewer #3 (Recommendations for the authors):

      (1) Supplementary Figure 1 - 'AI Rest' is compared to 'Delta AI'. It would be useful to see 'AI Rest' versus AI Locomotion'. In addition, how are these responses related to the baseline rates of the neurons? It would be good to plot 'Delta AI' versus 'Delta mean-rate' (i.e. difference in mean rates between locomotion and stationary conditions).

      As also requested in the public review, we have now added per-neuron comparisons of AI during rest and locomotion for PCs, VIP, SST and PV cells (Supplementary Fig. 2A, G–I). AI during rest and locomotion was significantly correlated in all cell types except SST cells, indicating that adaptation profiles were partially conserved across behavioural states.

      We also examined whether locomotion-related changes in response magnitude were associated with changes in AI (Supplementary Fig. 2C, J–L). We plotted ΔAI against the change in response integral during the stimulus, which is directly proportional to the change in mean response rate requested by the reviewer. In PCs, the change in response was negatively correlated with ΔAI, indicating that cells that became more sensitizing during locomotion showed greater increases in response. Among interneurons, PV cells showed a similar relationship, whereas no significant relationship was observed in VIP or SST cells.

      Finally, potential differences in baseline activity are addressed in Supplementary Fig. 2E, F, where baseline activity was similar between rest and locomotion.

      (2) 'Sensitize' is a term that is not well-established and hence would be worth defining early on.

      We agree this term is not as well stablished as depression. We have now added the definition of sensitizing adaptation early in the introduction of the paper. Later on, we explain in more detail the dynamics of sensitizing PCs in contrast to depressing PCs at line ~119.

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    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public Review):

      In the manuscript "Identification of neurodevelopmental organization of the cell populations of Juvenile Huntington's disease using dorso-ventral HD organoids and HD mouse embryos," the authors establish a fused dorso-ventral system that mimics cortex-striatum interactions within a single organoid and use this system to investigate neurodevelopmental impairments caused by HD. Specifically, they describe certain phenotypes in 60-day HD organoids and the brains of humanized mouse embryos, utilizing both wet-lab and single-cell sequencing techniques. The authors also develop dorsal/ventral and ventral/dorsal mosaic control/HD organoids, showing a capacity to rescue some HD phenotypes.

      The manuscript could be a valuable contribution to the field, however it has relevant drawbacks, the most significant being a lack of clarity regarding the replicates used for each genotype in the sequencing analyses. The lack of information on replicates raises the possibility that only a single replicate was analyzed for each organoid and brain sample. This approach may lead to concerns regarding the reproducibility of the findings, and it may be necessary for the authors to generate additional data to strengthen their conclusions. In addition, the analysis of the HD samples was conducted by pooling distinct cell populations from different brain regions (CTX, HIP, ChP for the dorsal brain, and STR, HYP, TH for the ventral brain). It is unclear why scRNA seq was used on pooled brain regions, which could obscure region-specific insights.

      The information we provided in the manuscript should include more details for a proper assessment of the experimental flow, replicates, and other aspects. The lack of clarity was partly due to the multivariate nature of our experimental system. For example, for scRNA-seq, there were 24 experiments, and we apologize for not including that information. The response to the “Major points” section of this review now offers a detailed description of the setup and a thorough clarification of the replicates. We also introduce a new schematic figure to help clarify the experimental setup and replicates. Additionally, all figure legends have been thoroughly rewritten, and many other changes have been made to better highlight the experimental replicates.

      Another issue pertains to their proposed outcome: "Finally, we found that TTR protein, a choroid plexus marker, is elevated in the adult HD mouse serum, indicating that TTR may be a promising marker for detecting HD". This statement appears to lack statistical support, which makes this set of data potentially misleading and inconclusive.

      We strongly agree that the sentence was inconclusive, and we have now corrected the Figure 11 legend and rewritten the parts of the Discussion and conclusions. We also agree that further studies with a larger number of subjects, investigating a broader age range and using more sensitive methods, such as SIMOA, are necessary to better characterize changes in TTR levels in serum.

      The authors are encouraged to provide evidence of biological replicates, remove outcomes that lack statistical support, and address a series of points as detailed elsewhere.

      Thank you for your thorough and valuable feedback, highlighting the important points. We address the specific points in detail below.

      Reviewer #1 (Recommendations for the authors):

      Major Points:

      (1) In paragraphs 2.4 and 2.5, the authors describe the single-cell sequencing experiment without specifying replicates. If only a single replicate per genotype was sequenced, these analyses should be presented as preliminary and descriptive, with conclusions accordingly tempered.

      As stated in our earlier responses, we acknowledge that the information provided in the manuscript is insufficient for properly assessing experimental replicates and other details. Below is our detailed explanation:

      In our work, we performed 24 independent scRNAseq experiments in total:

      - 17Q/17Q n = 3

      - 21Q/21Q n = 3

      - 71Q/71Q n = 3

      - 77Q/77Q n = 3

      - 21Q/71Q n = 3

      - 71Q/21Q n = 3

      - BAC21/null dorsal n = 1

      - HU128/21 dorsal n = 1

      - YAC128/null dorsal n = 1

      - BAC21/null ventral n = 1

      - HU128/21 ventral n = 1

      - YAC128/null ventral n = 1

      (1) The experimental setup of scRNAseq of 60-day-old HD, and control organoids:

      We performed 18 scRNA-seq experiments, consisting of 6 organoid types with 3 replicates each. Specifically, we used two types of control fused dorso-ventral organoids: 17Q/17Q with n = 3 and 21Q/21Q with n = 3, two types of HD fused dorso-ventral organoids: 71Q/71Q with n = 3 and 77Q/77Q with n = 3, and two types of mosaic HD-control fused dorso-ventral organoids: 21Q/71Q with n = 3 and 71Q/21Q with n = 3.

      (2) The experimental setup of scRNAseq of HD model embryonic brains:

      We performed scRNA-seq, using 3 mouse embryonic brains divided into 3 dorsal and 3 ventral brain parts originating from manual dissection of 1 embryos of each genotype. This resulted in a total of 6 independent scRNA-seq samples, specifically: BAC21/null dorsal n = 1, BAC21/null ventral n = 1, YAC128/null dorsal n = 1, YAC128/null ventral n = 1, Hu128/21 dorsal n = 1, and Hu128/21 ventral n = 1.

      Regarding the possible confusion about embryonic brain region dissection and pooling:

      We collected dorsal and ventral E13.5 embryonic brain parts, assuming they included specific embryonic brain regions. For example, we believed that the hippocampus (HIP) and the choroid plexus (ChP) were collected with the cortex (CTX) as parts of the dorsal region. Similarly, the striatum (STR) was collected with the ventral brain region representing the developing future basal ganglia. This approach of collecting the regions together was necessary because most parts of the E13.5 brains are still in the primordium stage; therefore, manual separation of regions is not feasible. However, it is possible to define populations using RNAseq, which we confirmed in our experiments.

      We now have also included the control analysis of our dissection accuracy in the Results section 2.10: 

      “First, we evaluated the transcriptomes of cell populations from the ventral compartment to assess the robustness of segregation of subpallial structures and to rule out technical artifacts arising from dissection of the ventral and dorsal parts of embryonic brains (Fig. 9). The cell populations from control BAC21/null embryos recapitulated canonical gradients of Foxp1 and Foxp2 across the ganglionic eminences (Ferland et al., 2003; Takahashi et al., 2003). The LGE showed strong Foxp2 expression levels but lacked Foxp1, while the MGE displayed the opposite pattern, with high Foxp1 levels. The CGE populations had an intermediate profile, predominantly expressing Foxp2 with moderate Foxp1. In the STR cluster, both Foxp1 and Foxp2 were consistently expressed across HD and controls, though Foxp1 was slightly reduced in the heterozygous HU128/21 embryo. This consistent spatial pattern of core striatal and subpallial populations after scRNAseq suggests that our tissue dissection was very precise and that our dataset offers high resolution.”

      Therefore, our 6 scRNA-seq experiments are a valuable, high-resolution and exact representation of the cell composition of the mouse embryonic brain.

      To improve the understanding of our experiments, we now provide:

      (1) Figure 1 to more clearly illustrate our manuscript across all experiments, including the number of replicates.

      (2) A thorough revision of the manuscript detailing the sample preparation and number, including the scRNA-seq experiment.

      (3) Enhanced descriptions of Figures with detailed explanations, sample numbers, and statistics.

      (2) Text seems poorly assembled in some parts and experiments lack proper introduction. For example in paragraph 2.2, portions like "Our qPCR (Supplement 1A) and RNA-seq DEG results detected [...]" (line 149) and "[...] which is consistent with the results from GSEA (Supp. Fig. 2A; Supp. 1)" (line 164) seem out of place, as qPCR and RNA-seq generation or GSEA analysis were not previously introduced in the main text.

      We revised these sections carefully to ensure proper text assembly, improve the description, and provide an introduction to the experiments.

      (3) In Suppl. Fig. 1A, the dorsal marker TBR1 and the ventral marker GSX2 in CTRL organoids, as well as the ventral markers DLX2 and NKX2.1 in HD organoids, show similar expression between dorsal and ventral regions. This is unexpected.

      Figure 2 (now main figure set) shows the results of characterizing the organoids using a common set of markers. Although this marker set is widely accepted in developmental studies, it remains a somewhat coarse method for distinguishing different cell stages. While these markers are frequently used in organoid research, they are highly sensitive to even minor variations in organoid development. Currently, our understanding of these markers' functions is better than when they were first incorporated into characterization protocols. For instance, DLX2 plays a crucial role in determining the fate of neuronal and oligodendrocytic cells, as well as in the development of soft facial tissue. In contrast, GSX2 promotes neurogenesis while inhibiting oligodendroglia. Therefore, although both are ventral markers, their functions differ considerably in regulating ventral region development. Variability in the expression of dorsal and ventral markers may be influenced by notable heterogeneity in the organoid formation process, despite careful control. Additionally, the heterogeneity and detailed expression levels have been only sparsely studied in HD organoids, resulting in a lack of comprehensive reference data.

      (4) The authors should better characterize the ventral and cortical identities in both CTRL and HD organoids to clarify whether HD organoids correctly differentiate (in terms of typical dorsal and ventral markers) relative to CTRL organoids. This information is particularly relevant in light of subsequent analyses of WT-HD mosaic organoids.

      A large portion of our work already involves characterizing HD and control organoids on many levels, as well as investigating how HD brain development differs from that of a normal brain in the organoid model. Hence, the simplified question addressed in this work is whether HD organoids correctly differentiate. Unfortunately, as we mentioned earlier, extensive characterization of the organoids using typical markers (via imaging or mRNA analysis) and as single dorsal or ventral organoids does not provide the accuracy needed to draw firm conclusions about the differentiation profile. This is because the abnormal features of HD organoid differentiation, such as the presence of certain cell populations and an increased number of rosettes, were not previously recognized in the early stage of organoid differentiation. In addition, as we demonstrate, the differentiation to brain-like structures in HD organoids is greatly influenced by the fusion of dorsal and ventral primed organoids. To achieve greater precision in investigating the differentiation of HD organoids, we systematically identified cell populations, their markers, and GSEA results across all setups using an advanced organoid characterization method, scRMAseq. To compare how our organoids differentiate, we used an HD mouse brain, where separating into the ventral and dorsal regions is mechanically feasible. This confirmed that similar HD-related processes occur in organoids and brain tissue models.

      (5) Data in Fig. 4 are misleading. In particular:

      The authors find an upregulation of LIMK2 in HD organoids compared with 21Q CTRL organoids, but not with 33Q CTRL organoids. How do they interpret this result?

      The 33Q organoids are derived from iPSCs of individuals who carry the HTT gene with 33 CAGs. This count exceeds the average found in healthy patients. A CAG range between 36 and 39 is considered to exhibit reduced penetrance, while 33 CAGs (27-35 CAGs) is sometimes regarded as placing an individual "at risk" (intermediate) or at risk of transmission to offspring. Our results clearly indicate that this clinical assessment is justified and that the 33Q organoids may show some distinct features of HD organoids, revealing early markers that affect disease progression. However, we do not have a definitive explanation of the observed phenomenon.

      How do they explain that other inhibitory neuron markers show opposite or inconsistent trends compared with LIMK2?

      The Limk2 belongs to the major regulatory network of transcriptionally deregulated genes in HD governed by the SMAD3 pathway. Interestingly, Limk2 within this regulatory network shows upregulated expression in HD models. At the same time, the majority of other genes in this network are downregulated, thus exhibiting the opposite pattern (10.15252/msb.20167435). The possible explanation is that the Limk2 gene is associated with the early organization of inhibitory neuron fate, specifically in astral microtubule organization and mitotic spindle orientation during the early stages of mitosis. In contrast, the other markers we investigated are linked to more advanced neuronal development and maturation stages. Our transcriptional results, including Limk2, indicate a prevalence of early development in HD organoids, while lower expression of late markers suggests reduced maturation in HD organoids. This observation is in line with our key finding that early development of the HD brain is delayed at the level of organoids and embryonic mouse model brain.

      The authors describe upregulation of GPR88 and HS3ST4 in HD organoids (77Q), but this data lacks statistical support.

      The authors state that CCL2 is downregulated in 71Q and 77Q organoids; however, the graph and statistics indicate the opposite result.

      Thank you for carefully reading and identifying inconsistencies in the manuscript. We want to clarify that these are unintended errors that occurred during repeated proofreading of the statistical tests used. Although the analyses are correct in the figure, they are not correct in the results text. The text is now corrected in the new version of the manuscript text.

      (6) Cell Number Balance: the cell count per sample (and thus per genotype, given the probable lack of replicates) is highly unbalanced, ranging from ~500 for 17Q/17Q to ~5000 for 71Q/71Q (Supp. Figures 4 and 5). This imbalance strongly impacts the number of identified cell subtypes. The authors should consider down-sampling cells across genotypes to match the minimum cell count for any genotype, and then report the resulting number of cell types.

      These differences in the number of cells for each genotype are closely related to the cell phenotypes observed during the harvesting, dissociation, and encapsulation processes, which varied among organoid genotypes. We obtained more consistent cell numbers for embryos, where each genotype was clonal with the same background. Some of these challenges could not be avoided, so we decided to utilize the analytical approach presented in our publication. We agree that the number of input cells can lead to the identification of more subtypes, but our previous study demonstrates that more subtypes with this analytical approach occur in highly proliferating and differentiating tissues, such as organoids (https://www.biorxiv.org/content/10.1101/2023.04.20.537649v1).

      However, when comparing the percentages of CTX, MGE, STR, etc., we used the number of cells relative to the total cell count from datasets for this genotype (three replicates for each genotype). This approach was more balanced because it was based on the proportion of each cell type relative to the total number of cells for this genotype, rather than comparing only subtypes. Additionally, we decided to conduct a combined transcriptomic analysis to examine the main changes in developmental pathways between HD and CTRL organoids and embryonic brains, as the expression values are normalized to each cell instead of to the dataset, as in traditional RNA-seq approaches. This method allowed us to highlight the primary changes in developing CTRL and HD brains at the cell level using organoid models and mouse embryonic brains. Furthermore, we narrowed the data to elements consistent across the genotypes of CTRL organoids and similarly for HD organoids, thereby minimizing genotype-related changes in the single-cell analysis. This strategy enabled a more targeted analysis in subsequent DEG and ORA, reducing the impact of genotype-specific variations.

      Summarizing, we preferred to avoid reducing the data (the number of cells) for comparison due to the potential for inaccurate data curation.

      (7) Despite generating single-cell data, the authors decide to pool cells across all cell types to perform a bulk differential expression analysis. Given the nine general populations identified, differential expression results between conditions should be reported for each population.

      We have decided to poll the cell transcriptomes from scRNA-seq datasets, which produce RNA-seq datasets. This is important because such RNAseq enables us to collect more information from different research perspectives, fully explore the data, and enhance comparisons of the identified cell populations.

      The following important information can be collected from conducting the bulk differential expression analysis on datasets with combined cell transcriptomes.

      (1) Investigating total RNA expression enables the identification of a broader set of genes that may vary to a certain degree among populations. Due to the complexity of physiological cellular networks, these genes reflect the activation of similar processes across populations, which is a necessary complement that scRNAseq cannot provide. Additionally, this analysis increases the statistical power of the study.

      (2) Investigating global gene sets provides the opportunity to uncover paracrine processes that may indicate interactions among cell populations affected by mutant proteins.

      (3) Finally, the RNAseq data also provides information about a set of genes reflecting the maturity and developmental advancement of our organoids and brains affected by mutant proteins, greatly supplementing the information about cell populations from scRNAseq.

      (8) Improvement of UMAP Representation: The authors should enhance the clarity of UMAPs (Figures 6 and 7). For instance, they could use one panel to color cells by sample and another to show clusters of the nine main populations (if clustering was performed). Additionally, it would be beneficial to report UMAPs before using the Harmony batch integration algorithm. Lastly, pie charts could be converted to bar plots representing cell proportions, with all samples displayed side by side to facilitate comparisons.

      We have now changed Figures 6 and 7, which are now Figures 8 and 9. We have prepared the figures according to the reviewer's request and updated the UMAP representations. We colored by samples and by main populations. We also report the UMAPs before Harmony in Supplementary Figs. 5 and 6 for organoids and embryo brains. The pie charts are now converted to bar plots.

      Details of the analysis approach and basic analysis steps are at: https://github.com/jkubis96/JSEQ_scRNAseq

      Or

      https://www.biorxiv.org/content/10.1101/2023.04.20.537649v1

      (9) Figure 8 is crowded and difficult to interpret. The authors might consider using a dot plot with associated UMAPs to represent known marker expression in the nine main populations, moving the subpopulation dot plot to the Supplementary section.

      We rethought Figure 8, removed the markers, and introduced a new Figure 10. The analysis in Figure 10 examines positional markers such as dorsal EMX2, FOXG1, LHX2, and TBR1, ventral markers FOXP1, FOXP2, and ETV1, and ciliary markers ARL13B and IFT88, which allow us to better illustrate the developmental defect present in HD in both organoids and the brain. Figure 10 shows that HD organoids and HD mouse brains exhibit neural positional dysorganization. In particular, it shows the MGE and ChP regions as the most affected in HD. Please see the results and discussion for details.

      (10) Despite Figure 9 showing no statistically significant difference in TTR levels between WT and HD mice, the authors claim "Our findings show an increase in the level of TTR monomer (16 kDa) and tetramer (55 kDa) [...] (Figure 9)" (line 375). Since TTR is proposed as a marker based on these inconclusive data, paragraph 2.9 and the corresponding conclusions require revision.

      We agree that the initial phrasing overstated the conclusion, as the necessary statistical power was not achieved in the serum analysis. The experiment is based on sera from only a few HD mice; therefore, the necessary power was not achieved. However, the intention of the sentence was not to highlight the finding in serum but rather to summarize all the evidence in the manuscript, indicating that the “TTR may be a promising marker gene.” The sentence aimed to consolidate in vivo and in vitro results, including increased levels of TTR mRNA in qPCR of HD organoids, elevated TTR in dorsal HD embryonic brain regions and organoids via scRNAseq, and a higher number of ChP cell populations in HD, along with immunofluorescence (IF) data. The serum data show similar TTR levels, supporting this hypothesis, with several mice as biological replicates, indicating the trend; however, more individual mouse sera were needed for better examination and justified statistics. Of note, the co-authors of this study have previously reported elevated levels of this marker in adult patients with CSF (DOI: 10.1093/braincomms/fcac309).

      Therefore, we now mention in the text it is not significant.: We showed that the marker differed between individual YAC<sup>128/null</sup> mice and BAC<sup>21Q/null</sup> controls (Fig. 11), mainly for the Ttr tetramer. We, however, did not observe statistical significance in the mean comparisons.

      (11) The initial part of the "Discussion" (lines 380-426) reads more like an "Introduction"

      Thank you for this suggestion. We now optimized the text for redundancy and incorporated some information to the introduction section to provide better context and flow.

      (12) The phenotypic rescue observed in WT-HD mosaic organoids is particularly intriguing with therapeutic implications for HD. This should be more thoroughly emphasized in the discussion. For example, data in Fig. 2B indicate that "On average, mosaic 21D/71V organoids were close in size to control organoids, while the opposite configuration of mosaic 71D/21V was closer to HD organoids (Fig. 2B)" (lines 143-144). Thus, they observe size rescue only in the 21D/71V mosaic configuration, not in 71D/21V. How do they interpret this finding? Additionally, when examining single-cell data in Fig. 6, they find that the ChP cell population in both WT-HD mosaic configurations (21D/71V and 71D/21V) is reduced or absent, as in control organoids, indicating that the rescue in this parameter is seen in both configurations, unlike the size parameter. The authors should discuss more thoroughly how the combination of WT and HD cells may have beneficial effects or not.

      Using healthy cells to create either the dorsal or ventral side and forming mosaic organoids reverses the effects in fused organoids, where both the dorsal and ventral parts are HD.

      In the discussion section, we have now introduced additional explanations:

      (1) The base size of the HD organoids is increased:

      HD brain organoids display more early proliferative features at the expense of differentiation compared to controls. This has been confirmed through the extended HD organoid structure, rosettes, GSEA patterns, and scRNAseq.

      (2) The size rescue only in 21D/71V but not in 71D/21V mosaic organoids:

      In general, there is consensus that the physiologically dorsal part of the brain proliferates at a higher rate than the ventral side during development; however, both mutant and normal HTT influence proliferation on both sides. This dorso-ventral imbalance, driven by mutant HTT in combination with the mosaic organoid setup, likely results in a much larger 71D/21V than 21D/71V.

      (3) The choroid plexus population rescues in both 21D/71V and 71D/21V:

      During brain development, choroid plexus cells originate from the ectoderm and mesoderm. Additionally, choroid plexus cells are known for their secretory functions and for communicating with surrounding tissues via extracellular mediators. This communication closely regulates NSC proliferation and differentiation, which may also explain size differences between organoids. Moreover, we show that HD organoids and HD mouse brains show positional dysorganisation, being between neural cells and choroid tissue, as seen in the transcriptional profile. Given all this, we cannot definitively say that the choroid plexus in HD organoids comes only from the dorsal side, since many brain regions in HD contribute to its final development due to positional defects. Therefore, both ventral and dorsal parts of the organoid are also likely involved in rescuing the HD phenotype in mosaic. Furthermore, introducing either a dorsal or a ventral healthy part can diminish the choroid plexus phenotype. Lastly, the features of the mosaic organoids (either 21D/71V or 71D/21V) also include a reduced dosage of the mutant allele within the organoid.

      Notably, our mouse model setup allows us to examine the brains of HD embryos (both ventral and dorsal parts) that either contain or lack the healthy allele. Interestingly, the choroid plexus phenotype is milder in YAC128/BAC21 compared to the much more pronounced choroid plexus phenotype in YAC128/null. Therefore, the presence of the healthy allele decreases the number of choroid plexus cells compared to having only the HD allele, thus resulting in the rescue of the phenotype.

      Minor Points:

      (13) Fig. 1B shows a representative slice of an HD fused organoid stained for the dorsal marker TBR1. Authors should include staining for a ventral marker as well, ideally on the same section.

      Figure 1 has now been replaced. The new Figure 1 more thoroughly explains the work in the manuscript. The detailed stainings of organoids are found in Figures 2 and 4.

      (14) The sentence "[...] markers upregulation in 60-day fused brain HD organoids." (line 151) should specify which genotypes the upregulation was compared against.

      The missing information about the genotypes of the organoids and embryonic brains was corrected throughout the manuscript. Thank you for your careful evaluation.

      (15) The authors state, "[...], we observed the regression in the HD phenotype represented by reduced neural rosette occurrence, which is consistent with the results from GSEA (Supp. Fig. 2 A; Supp. 1)" (lines 163-165). A clearer explanation of this consistency is needed.

      The fragment has been revised to provide a more precise explanation of the sentence's specific points.

      (16) The described Gene Set Enrichment Analysis (GSEA) on DEGs to identify enriched Gene Ontology terms seems more like a Gene Ontology Enrichment analysis, as GSEA typically involves pathway-specific co-regulation analysis.

      We have revised Section 4.8 of our Materials and Methods to provide a more detailed explanation of our bioinformatic analysis approach and tools.

      (17) The phrase "Firstly, we compared the expression of several inhibitory neuron markers" (line 179) should specify the technique used, I guess qPCR.

      The sentence has been revised.

      (18) Change "Differentiating" (line 187) to "different."

      The term has been revised.

      (19) The sentence "Such gene deregulations and GSEA profiles indicate that control organoids are more related to maturation processes than HD organoids" is unclear.

      We propose to incorporate the following enhanced explanation into the manuscript content.

      The statistically significant deregulated genes between HD and CTRL organoids, along with the associated biological terms and pathways related to maturation, proliferation, and differentiation, indicate that cells derived from healthy organoids are more aligned with processes involving mature glial and neuronal cells. In contrast, HD cells appear to be arrested in proliferative and differentiation stages. This is reflected in the faster development of certain brain structures in HD organoids, but with fewer processes linked to mature cells, suggesting an incomplete state of maturation.

      (20) Lines 297-300 contain hypotheses that would likely fit better in the Discussion section.

      The sentences were in part transferred into the discussion section.

      (21) Replace "dorsal" (line 420) with "ventral."

      Thank you for careful reading. The term has been revised.

      (22) Why did the authors use the 71Q line instead of the 109Q line to create WT-HD mosaic organoids? In fact, the size parameter graph shows a more pronounced HD-related alteration in the 109Q line.

      The reason for omitting the 109Q line was due to a specific characteristic of all HD organoids. All HD cells showed increased cell-cell adherence during dissociation attempts, making it difficult to properly prepare reproducible samples for single-cell analysis using Drop-seq technology. Unfortunately, this phenotype of cells to quickly build cellular aggregates was particularly pronounced in the 109Q cell line. Therefore, although the HD phenotype in the 109Q organoids was more pronounced (TTR, rosettes, etc.), it was very challenging and costly to perform scRNA-seq compared to 71Q and 77Q. To ensure consistency in our scRNA-seq, we decided to include only fused HD and fused mosaic samples from 71Q and 77Q.

      (23) A recent publication by Galimberti et al. (Nat Comm., 2024) investigated WT-HD mosaic telencephalic organoids containing ventral and dorsal neuron populations. The authors should consider discussing their findings in relation to that work.

      In the manuscript, we cite the work of Galimberti et al.

      Reviewer #2 (Public Review):

      The article titled "Identification of neurodevelopmental organization of the cell populations of juvenile Huntington's disease using dorso-ventral HD organoids and HD mouse embryos" analyses an in vitro human brain organoid model containig dorsal and ventral telencephalum structures derived from human iPSC from Huntington's disease patients or control subjects.

      The authors describe differences in the pattern of expression of genes related to proliferation and neuronal maturation, with a slower pattern of differentiation present in HD cells. Moreover, the authors described a higher differentiation capacity of HD cells to generate choroid plexus identity following dorsal telencephalon prime protocol differentiation when compared to control cells. Whereas the claims related to Choroid plexus identity are intriguing, most of the claims made through the manuscript are not sustained by quantitative data or consistent results in the different conditions analysed, or many experiments seem to be missing to reach final conclusions.

      In addition, the quality of the organoids used for experiments does not seem to have been assessed or satisfactorily presented in the figures of this paper. Many important details related to the experimental execution are missing in the current version of this manuscript.

      Thank you for your insightful feedback. We truly appreciate your thoughtful comments. In the next versions of the manuscript, we will work to address the inconsistencies and clarify the points you have raised. We will also make sure to provide more quantitative data and include any missing experiments to strengthen our conclusions. Additionally, we will pay closer attention to assessing and presenting the quality of the organoids used in the experiments and ensure that all relevant experimental details are properly included.

      Reviewer #2 (Recommendations for the authors):

      Major comments:

      (1) The article needs to be corrected for numerous grammatical errors and imprecisions which hamper the reading/understanding of the manuscript. In addition, the manuscript is poorly written with many details missing from the results, figure legends and materials and methods sections. Specially in figure legends all details concerning days in vitro of the organoids analysed, number of independent differentiations used, and number of organoids stained are recurrently missing!

      The manuscript was proofread once more to eliminate any possible language errors. All figure legends were either rewritten or supplemented with all necessary details.

      To improve the understanding of our experiments, we now provide:

      (1) A figure scheme to better explain our experimental approach.

      (2) A dedicated section of Materials and Methods describing the scRNA-seq sample setup.

      (3) An improved description of Figures, including detailed explanations and statistics, and improvements in all figure legends.

      Explanation for the missing list of replicates throughout the manuscript:

      Since Reviewer 2 reported a similar issue, we copied the response and adjusted it in some parts. As stated above, we acknowledge that the information we provided in the manuscript is insufficient for properly assessing experimental replicates and other details.

      In addition to manuscript corrections, below is our in-depth explanation of replicates.

      In our work, we performed 24 independent scRNA-seq experiments in total:

      - 17Q/17Q n = 3

      - 21Q/21Q n = 3

      - 71Q/71Q n = 3

      - 77Q/77Q n = 3

      - 21Q/71Q n = 3

      - 71Q/21Q n = 3

      - BAC21/null dorsal n = 1

      - HU128/21 dorsal n = 1

      - YAC128/null dorsal n = 1

      - BAC21/null ventral n = 1

      - HU128/21 ventral n = 1

      - YAC128/null ventral n = 1

      The number of organoids stained for Rosette images:

      - 17Q/17Q n = 2

      - 21Q/21Q n = 2

      - 71Q/71Q n = 2

      - 77Q/77Q n = 2

      - 21Q/71Q n = 2

      - 71Q/21Q n = 2

      (1) The experimental setup of scRNAseq of 60-day-old HD and control organoids:

      We performed 18 scRNA-seq experiments, consisting of 6 organoid types and 3 replicates each. In detail, we used two types of control fused dorso-ventral organoids: 17Q/17Q n = 3 and 21Q/21Q n = 3, two types of HD fused dorso-ventral organoids: 71Q/71Q n = 3, 77Q/77Q n = 3 and two types of mosaic HD-control fused dorso-ventral organoids: 21Q/71Q n = 3, 71Q/21Q n = 3.

      (2) The experimental setup of scRNAseq of HD model embryonic brains:

      We performed scRNA-seq using 3 mouse embryonic brains divided into 3 dorsal and 3 ventral brain parts originating from manual dissection of 1 embryo of each genotype. Therefore, there were 6 independent scRNAseq in total, namely: BAC21/null dorsal n = 1 of BAC21/null ventral n = 1, YAC128/null dorsal n = 1, YAC128/null ventral n = 1, Hu128/21 dorsal n = 1, and Hu128/21 ventral n = 1.

      Regarding the possible confusion about embryonic brain region dissection:

      We collected the dorsal and ventral embryonic E13.5 brain parts, assuming they would contain certain embryonic brain regions. For example, we believed that the hippocampus (HIP) and the choroid plexus (ChP) were collected alongside the cortex (CTX) as part of the dorsal part. Similarly, the striatum (STR) was collected with the ventral brain region representing the developing future basal ganglia. Such an assumption of collecting the regions together was necessary since most of the parts of the E13.5 brains are in the stage of primordia; hence, the separation of regions is not possible manually, however, it is possible by defining populations using RNAseq, which we confirmed in our experiments.

      We have now included the analysis assessing the robustness of our scRNA-seq and our dissection accuracy in the Results section 2.10:

      “First, we evaluated the transcriptomes of cell populations from the ventral compartment to assess the robustness of segregation of subpallial structures and to rule out technical artifacts arising from dissection of the ventral and dorsal parts of embryonic brains (Fig. 10B). The cell populations from control BAC21/null embryos recapitulated canonical gradients of Foxp1 and Foxp2 across the ganglionic eminences (Ferland et al., 2003; Takahashi et al., 2003). The LGE showed strong Foxp2 expression levels but lacked Foxp1, while the MGE displayed the opposite pattern, with high Foxp1 levels. The CGE populations had an intermediate profile, predominantly expressing Foxp2 with moderate Foxp1. In the STR cluster, both Foxp1 and Foxp2 were consistently expressed across HD and controls, though Foxp1 was slightly reduced in the heterozygous HU128/21 embryo. This consistent spatial pattern of core striatal and subpallial populations after scRNAseq suggests that our tissue dissection was very precise and that our dataset offers high resolution.”

      Therefore, our 6 scRNA-seq experiments are a valuable, high-resolution, and exact representation of the cell composition of the mouse embryonic brain.

      (2) In general, the main figures do not seem to be in a correct acceptable final format for submission to eLife. For instance, Figure 3 is the only figure in the whole manuscript that shows full-size fused organoid pictures, which is missing a nuclear staining marker such as DAPI to assess overall organoid viability. In addition, the tile view shown in this figure for full organoid image acquisition does not meet minimal requirements of overlap during image acquisition for stitching to minimize image artefacts.

      In the present version of the manuscript, we incorporated the DAPI staining as a separate column set of picture.

      The images were captured using the Opera Phenix HCS Nipcov spinning disk microscope with 5% overlap. This overlap area is common for many confocal microscopes. However, producing these images involves certain technical limitations and balances the speed of image collection, the volume of digital data, resolution, and final quality. While LSM systems are slower and provide better quality, spinning disk microscopes are very fast. Still, even with an Opera spinning disk, acquiring images takes about a day per organoid and results in terabytes of data. Stitching these images is a complex process that requires hours of processing on a powerful workstation with a dedicated program we developed. Despite this, preventing cross-shaped artifacts caused by overlapping regions, which sometimes appear in Fig. 4, is difficult. In the worst case, the entire dataset may not be stitchable, forcing us to repeat the acquisition. Currently, this presents a technical limit for the stitched images shown in the manuscript, obtained with the spinning disk Opera microscope. For more details about this imaging process, please visit our GitHub repository: https://github.com/jkubis96/JIMG.

      (3) There are NO details about the number of independent experiments and of the total number of organoids analysed for the different immunofluorescence stainings, qPCR experiments or single-cell RNA-seq analysis.

      To improve the understanding of our experiments, we now provide:

      (1) A figure scheme to better explain our experimental approach and list the n and N values.

      (2) A dedicated section of Materials and Methods describing the scRNA-seq sample setup.

      (3) Improved description of Figures 6, 7, and 8, and other figures including detailed explanations and statistics, and improvements in all figure legends

      We included the missing information regarding the genotypes of the organoids and embryonic brains throughout the manuscript.

      (4) Line 127: Correction: TBR1 is a transcription factor expressed in subplate neurons and layer VI neurons of the cortex, and as such is a postmitotic projection neuron marker

      (5) Line 127: Correction: Pax6 is a marker of V Z and SVZ of the cortex (and not TBR1)

      Thank you for this correction. We have rearranged the sentence to: “We detected immunostaining for PAX6, which is a marker of ventricular zone (VZ) and subventricular zone (SVZ) of the developing neocortex (respectively), and TBR1 as dorsal forebrain markers.”

      (6) The two parameters discussed, number of rosettes per area of organoid, and mean area of rosettes need to be quantified in the different genotype fused brain organoids. Pictures should include the presence of a nuclei marker like DAPI (absent in Figure 3). These quantifications need to be performed from different experiments, each analysing various organoids and for all of the genotypes compared.

      We quantified the number of rosetes in all types of organoids (Figure 4B).

      (7) Fused organoids seem to present an overall presence of dorsal-specific markers through all the fused organoid structure, opening the question of the effects of the fusion of dorsal and ventral regions at the early stage of day 16. Are the ventral regions still present at day 60 in fused organoids? To answer this, the authors need to stain fused organoids with a combination of dorsal and ventral markers and show full fused organoid pictures to understand the size of both structures at different time points from the time of fusion to day 60.

      The question about the presence of the ventral region in 60-day organoids is addressed in the manuscript. In Figure 6, we show that nearly every genotype of the organoid contains a large percentage of ventral regions, such as cell populations that express prominent markers of the striatum and ganglionic eminence (typically around 60%). Additionally, we include immunostaining of ventral markers (DLX2, NKX2.1, GSX2) and dorsal markers in 60-day organoids in Supplementary Figure 1B. The images demonstrate that DLX2 (although DLX2-positive interneurons usually migrate toward dorsal brain areas) and NKX2.1 markers mainly stain the areas outside the rosettes in both control and HD organoids. The GSX2 marker also stains the rosettes to some degree. However, GSX2 is characteristic of progenitors www.pnas.org/doi/10.1073/pnas.1008824108 that can be located near Pax6-positive cells and tends to disappear later in development. Because of the importance of Supplementary Figure 1, we decided to move it from the supplementary materials to the main figures.

      (8) One of the many imprecisions through the manuscript: Line 148: reference to qPCR data from Sup Figure 1A is made concerning levels of expression of PAX6 and TBR1 in fused brain organoids, however, Sup Figure 1 legend describes that these results are NOT from fused brain organoids, but from separated brain organoids patterned towards either dorsal or ventral telencephalic identities.

      We apologize for the mistake in describing the PAX6 and TBR1 qPCR data from Supplementary Figure 1A (now Figure 2) in line 148 of our manuscript. The results in Figure 2A and B are from separate brain organoids patterned to have either dorsal or ventral telencephalic identities, as indicated in the figure legend. Conversely, Figure 2C and D show immunostaining of fused brain organoids, which may have led to a mismatch in the description and caused the mistake. The mistakes are now corrected.

      (9) In addition to the above comment, line 149 describes results from RNA-seq data, however, the experiment is not explained until much later in the manuscript (line 303).

      Some sections of the manuscript were rearranged during the final stages of editing, which may have affected the flow of the text. We carefully revised these sections.

      (10) All details of the conditions analysed, number of differentiations, organoids used for this analysis are lacking as well. In addition, the reference of the figure showing the results mentioned in this line 149 is also missing! The same is missing for the number of mouse embryos used for isolating the cells used for single-cell RNA-seq for the embyo analysis.

      We apologize for the limited information about the replicates. The number of replicates is duly stated at the beginning of the response to the reviewers' comments (Reviewer 1; Major Points; Point (1), and in this response (Major Comments; Point (1) and partially in Point (6)). We have now taken full care to clearly and thoroughly present this information in both the text and the figure legend in the manuscript

      (11) Line 161: This conclusion needs to be based on quantified results on the number of cells expressing PAX6; TBR1 and mature neuronal markers such as NeuN, MAP2, etc... from the immunofluorescence experiments. Quantifications need to be done on several differentiations, each using several independent organoids.

      The sentence has been removed from the manuscript. The quantification of the PAX6-positive rosettes was performed.

      (12) Line 180: The conclusions on the changes of LIMK2 pattern of expression are not consistent between control lines and therefore should not be mentioned as important when compared to HD lines.

      We reevaluated our analysis of neuronal marker expression and found that while NXPH2, GRIN3A, and FOXO1 are clearly GABAergic, LIMK2 and CKB are expressed throughout the types of neurons, and we removed the analysis from the figure.

      (13) Line 193: DARP32 should be described as protein phosphatase 1 regulatory subunit 1B, present in striatal medium-sized spiny neurons that express dopamine D1 receptors.

      Thank you for the suggestion. We will correct the gene names consistently throughout the manuscript. However, providing a definitive description of gene localization in cells can be difficult, especially for PPP1R1B. Its presence is not limited to MSN but is also found in other neurons and is very highly expressed in choroid plexus cells (https://www.proteinatlas.org/ENSG00000131771-PPP1R1B/brain), where it plays a role in regulating CSF production. We have optimized the description of DARPP32.

      (14) Line 224 states that the GSEA shows pathways upregulated in fused HD brain organoids when compared to fused CTRL organoids, related to early differentiation stages whereas downregulated pathways are related to later mature stages such as neuronal and glia cells maturation. However, BOTH upregulated and downregulated pathways show entries for DEG in the same classifications: Neuronal and glia cell development and maturation; mitotic spindle and cell polarity; and programmed cell death (Sup Figure 2).

      We thank the reviewer for this important observation. We would like to clarify the presentation of our ORA data in (now Supplementary Figure 1.)

      The boxed titles in Supplementary Figure 1 (e.g., "Neuronal & glial cells development & maturation", "Mitotic spindle & cell polarity", "Programmed cell death") represent broad thematic meta-categories used solely to visually cluster individual Gene Ontology (GO) terms into functional domains, rather than individual biological pathways.

      While both upregulated (blue) and downregulated (red) groups contain terms belonging to these overarching meta-categories, the specific individual GO terms within them reflect distinct developmental stages and opposite biological directions:

      (1) Neuronal & Glial Development & Maturation:

      The upregulated GO terms within this cluster correspond specifically to early progenitor processes, stem cell state maintenance, and early lineage specification (e.g., pathways regulating early neurogenesis and negative regulation of cellular differentiation).

      In contrast, the downregulated GO terms correspond to late-stage structural and functional maturation (e.g., synaptic vessel transport, axonogenesis, postsynaptic assembly, and mature glial differentiation).

      (2) Mitotic Spindle & Cell Polarity:

      Upregulated terms center on active cell-cycle regulation, spindle assembly, and mitotic division in expanding progenitor pools.

      Downregulated terms relate to structural polarity required for tissue organization, planar cell polarity in differentiating neurons, and post-mitotic structural stability.

      (3) Programmed Cell Death:

      Upregulated terms reflect pro-apoptotic signaling and cellular stress pathways activated during aberrant development, whereas downregulated terms involve anti-apoptotic / cell survival processes.

      In the results text we incorporated a following text:

      “In general, while terms enriched in both up- and downregulated datasets cluster under broad functional headers (such as 'Neuronal & glial cells development & maturation'), individual upregulated GO terms were specific to early progenitor maintenance and early differentiation steps, whereas downregulated GO terms selectively enriched for late-stage synaptic assembly, dendritic spine formation, and mature neuronal/glial function.”

      (15) Line 258 should explain the differences between the two HD mouse models used for single-cell RNA-seq analysis

      The detailed description of the models, including how the HD and Control models were generated was included in methods section “4.4. HD mouse tissue”

      (16) Similar comments for line 263 (repetition from comment to line 224) for the GSEA from HD mouse brain models compared to control mouse brain analysis. In addition, no details are given on the number of individual mouse brain samples and total number of cells used for single-cell RNA-seq experiments.

      (2) The experimental setup of scRNAseq of HD model embryonic brains:

      We performed scRNA-seq using 3 mouse embryonic brains divided into 3 dorsal and 3 ventral brain parts originating from manual dissection of 1 embryo of each genotype. Therefore, there were 6 independent scRNA-seq datasets in total, namely: BAC21/null dorsal n = 1 of BAC21/null ventral n = 1, YAC128/null dorsal n = 1, YAC128/null ventral n = 1, Hu128/21 dorsal n = 1, and Hu128/21 ventral n = 1.

      We have now included the analysis assessing the robustness of our scRNA-seq and our dissection accuracy in the Results section 2.10:

      “First, we evaluated the transcriptomes of cell populations from the ventral compartment to assess the robustness of segregation of subpallial structures and to rule out technical artifacts arising from dissection of the ventral and dorsal parts of embryonic brains (Fig. 10B). The cell populations from control BAC21/null embryos recapitulated canonical gradients of Foxp1 and Foxp2 across the ganglionic eminences (Ferland et al., 2003; Takahashi et al., 2003). The LGE showed strong Foxp2 expression levels but lacked Foxp1, while the MGE displayed the opposite pattern, with high Foxp1 levels. The CGE populations had an intermediate profile, predominantly expressing Foxp2 with moderate Foxp1. In the STR cluster, both Foxp1 and Foxp2 were consistently expressed across HD and controls, though Foxp1 was slightly reduced in the heterozygous HU128/21 embryo. This consistent spatial pattern of core striatal and subpallial populations after scRNAseq suggests that our tissue dissection was very precise and that our dataset offers high resolution.”

      Therefore, our 6 scRNA-seq experiments are a valuable, high-resolution and exact representation of the cell composition of the mouse embryonic brain.

      (17) Venny representations of the DEG upregulated and downregulated in common and different between the various in vitro and in vivo conditions analysed should be added.

      Due to manuscript length considerations and the inclusion of our comprehensive DEG lists in the supplementary data, we opted not to include a Venn diagram.

      (18) Stainings of embryo brain sections at the same stage as single-cell RNA-seq data should be performed for the choroid plexus comparing HD and control mice.

      Due to limitations in available embryonic tissue, we are unable to provide these additional stainings.

      (19) Did the authors analyse and compare the level of expression of morphogens and signaling pathways between HD and Control cells (dorsal or ventral)?

      We have now performed a range of new analyses of our results and a new set of experiments to test the influence of paracrine, secreted signals on the HD neurodevelopmental phenotypes. To selectively capture paracrine signals from HD or WT, we conditioned media within individual genotypes (e.g., HD media to HD organoids and WT to WT, always across V to D and D to V). Our new results are now shown in Figure 5, where we demonstrate that both dorsal and ventral sides of organoids from both wt and HD genotypes are subject to regulatory developmental paracrine influence that controls tissue growth along the striatocortical axis. The expansion of HD organoids is twice as prominent as that of WT organoids and cannot be completely halted by conditioning. This suggests that soluble paracrine signals influence the HD phenotype, but also that cell-cell contact or localized niche factors are necessary for a full rescue (two-hit mechanism).

      To investigate this niche, we examined the positioning of neural cells in HD. We found ectopic expression of several positioning factors in ChP and aberrant positioning of MGE interneurons in HD. We constructed a conceptual model in which massive ChP overgrowth creates an altered paracrine environment that triggers a switch in gene expression in interneuron progenitors. The soluble secretome can modulate the proliferative tissue environment, and direct cell-cell contacts or localized extracellular matrix (ECM) niche factors are essential for preserving spatial boundaries and cell migration. This insight aligns with recent patient cohort data demonstrating structural ChP modifications and abnormal CSF dynamics prior to clinical onset.

      (20) The authors should differentiate human iPSC lines from HD patients and control subjects following a second independent protocol to differentiate dorsal telencephalic structures that uses a directed strategy for differentiation (dual SMAD protocol or a combination of TGFbeta and Wnt signaling inhibition), in order to corroborate their claims on increased choroid plexus identity fate of HD dorsal cells fate of HD dorsal cells.

      Conducting proposed experiments using an alternative iPSC differentiation protocol would certainly be interesting. While we agree an alternative dual-SMAD protocol would be interesting, our current protocol robustly aligns with our in vivo mouse data. We believe the current methodology sufficiently supports our conclusions regarding choroid plexus identity

      Minor comments:

      (21) Details about the different HD and CTRL cell lines used in the manuscript should be clearly written in the first block of the results section.

      Detailed information has now been provided in the Materials and Methods section 4.1.

      (22) Line 149: No figure reference is written for the RNAseq data

      The reference are now updated.

      (23) Figure Sup 1A: Graphs need to be presented comparing CTRL and HD organoids for the different gene expression markers for dorsal and ventral identity.

      Now Figure 2A and B present the graphs in the proposed format.

      (24) Figure legend text needs to include when relevant "Tile Scan view".

      We revised the figure legends to make sure they include all necessary information and adhere to the correct format.

    1. Author response:

      The following is the authors’ response to the previous reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      Using cryofixation and serial block-face electron microscopy (SBEM), P. Vijayakumar and K. Cauwenberghs characterize extracellular vesicles (EVs) and non-vesicular extracellular particles (NVEPs) within native Drosophila olfactory sensilla. The study provides a unique and valuable dataset comprising approximately 7,800 extracellular particles, systematically describing their morphology, size, density, and distribution. The ultrastructural analysis across different sensillum classes offers insights into the potential biogenesis and functions of these extracellular particles.

      Strengths:

      Cryofixation preserves EVs and NVEPs within native tissue conditions. The detailed quantification of a very large dataset provides a unique source of information on extracellular particle number, categories, distribution. The expertise of the group in the method and the tissue explored as well as their detailed quantification provide confidence in the dataset and observations.

      Weaknesses:

      All weaknesses previously observed have been addressed.

      Reviewer #2 (Public review):

      Summary:

      This paper presents a large structural survey of extracellular vesicles (EVs) and non-vesicular extracellular particles (NVEPs) in the olfactory sensilla of Drosophila melanogaster. Using high-pressure freezing and serial block-face SEM, the authors avoid many of the artifacts associated with conventional fixation and analyze more than 7,800 particles across 352 sensilla. The manuscript maps the distribution of these particles, describes their morphological heterogeneity, and examines their likely origins across different sensillum classes in both normal and degenerating tissue.

      Strengths:

      The strongest aspect of the paper is the imaging. Preservation is painstakingly controlled. The cryofixation appears to preserve the sensillum lymph in a convincing native state than standard preparation methods, giving this work gravitas. Further the authors characterized thousands of particles, further making this data strong.

      The figures are strong. They are clear, easy to read, and generally well designed, I think people will use this paper as a model on how to present complex data in a concise and straightforward manner. The manuscript is careful in how it presents the dataset and does not overinterpret the descriptive observations. As an ultrastructural resource, this paper will be useful to the field. The identification of auxiliary support cells as major secretory sites, together with the striking accumulation of EVs in degenerating tissue, will provide a useful starting point for future work.

      Comments on revised version.

      The authors have completely addressed my concerns from the initial review. The revised text and Methods now clearly explain the vesicle categorization specifically how "dense," "cargo-filled," and "double EVs" are defined as strictly morphological groupings rather than verified biological classes. This is a rigorous and valuable ultrastructural resource.

      Reviewer #3 (Public review):

      Using cryofixation-based serial block face electron microscopy of several subregions of the Drosophila antenna, the authors segment and assemble a high-resolution atlas of the anatomical structure, density, and spatial distribution of extracellular vesicles (EVs) and non-vesicular extracellular particles (NVEPs) in different Drosophila olfactory sensilla types. This systematic and thorough description is an important prerequisite to understanding the function of extracellular particles in intercellular signaling in the nervous system. Additionally, they describe examples of putative biogenesis events (budding/fusion), as well as neuronal and axillary cell degeneration events and measure the changes in particle accumulation in these altered microenvironments. Overall, this is a significant and comprehensive analysis and represents an invaluable resource to this burgeoning field. The authors assemble an important dataset and their claims match the level of evidence provided.

      Strengths:

      (1) The authors use segmentations from four different patches of the antenna to provide the systematic ultrastructural survey of extracellular particles in native insect sensilla. The dataset captures the diversity of sensilla types and reconstructs ~7800 particles.

      (2) We commend the authors from making the EM volumes and the segmented 3D models publicly available, through Dryad Digital Repository and the Cell Image Library, respectively. These datasets will be valuable resources to the community in future work.

      (3) The sample preparation technique appears to minimize typical artifacts associated with chemical fixation, as evidenced by the high reported sphericity of EVs.

      Comments on revised version.

      The authors have succinctly and effectively addressed all our major concerns, which mostly related to clarification of methods and analysis/categorization choices. The inclusion of continuous data visualizations to complement categorical descriptions (for particle position along the sensillum length and vesicle size) is very nice and gives the reader a fuller view of the dataset. The revised manuscript answers all our remaining questions and allows the reader to better understand the motivations for the specific categorical analyses applied.

      We thank the editors and reviewers for their careful evaluation and constructive feedback. We are pleased that the reviewers consider the manuscript to have addressed their previous concerns and to provide a rigorous and valuable resource for the field.

      Recommendations for the authors:

      Reviewer #3 (Recommendations for the authors):

      We found the bars designating 95% CI of the median in Fig. 5E/H to be confusing on initial reading. After thinking through and discussing the possible distributions of the data, we think we understand why they look the way they do, and they are undoubtedly correct. However, we wonder whether including the raw data distribution (in a bar graph or histogram type chart) would help the reader understand this dataset more quickly. This is just a very minor comment/suggestion, and we defer to the authors' preferences.

      We have revised Figures 5 and 6 to include the raw data points, allowing readers to more readily appreciate the underlying data distributions.

    1. Author response:

      Our paper presents both a novel method for identifying barrier loci and a key biological finding derived from it. On reading both reviews, we realise that the key biological finding was not conveyed with sufficient clarity. We will try to make this point more clearly in the Discussion and by revising the Abstract to end with:

      The recovery of a single multi-locus partition shows that the previous focus on flower colour barrier loci was not an arbitrary consequence of visual salience to ecological geneticists. Instead, complex traits with a signalling role, like colour patterns, may lend themselves to the formation of multi-peaked fitness landscapes in a common environment because the same signal can be conveyed in multiple ways.

      Reviewer #1 (Public review):

      We thank the reviewer for their thoughtful comments and summary of the paper. The reviewer makes several helpful suggestions that will help us improve the manuscript by clarifying the relative importance of overall tree similarity (c) and depth of root division (SRB) for our method.

      (1) The choice of c=0.5 and 0.002 as thresholds for SRB was not explained. It is unclear how readers would make their own decisions about threshold cutoffs should they apply to their own data. The manuscript would be improved if the authors address this important issue of whether and how their approach, as presented, can reproducibly identify sets of trees that represent outliers in genomic variation.

      Our choices were based on empirical rules of thumb, equivalent to choosing F<sub>ST</sub> peaks because they “stand out”. Using a more stringent c threshold of 0.6 led to partition trees being split over multiple forests (Supp Fig. 3 red circles) and partition islands no longer stood out as clearly (Supp Fig. 4c). Thus, a c threshold of 0.5 seemed most informative for our data, as it was the maximum stringency that returned clear partition islands. The SRB threshold of 0.002 also seemed most informative, as lowering the threshold to 0.0015 recovered a high density of windows as the largest forest was captured (Supp Fig. 5). Whether the threshold choices return genuine barrier loci can be evaluated using statistical arguments and criteria based on other approaches as outlined below in points 2 and 3. We will clarify these points in the Results and Discussion.

      (2) A related issue is that by first binning trees based on similarity, then filtering on mean SRB value, the method potentially returns outlier forests containing individual trees with low SRB values. Should such trees be considered barrier loci?

      This important point revolves around the question of what causes low SRB values. Plotting SRB for a well-studied locus, ROS (Fig. 8g), shows that island windows giving low SRB tend to be on the flanks of the causative loci, where you might expect barrier strength to be lower because of recombination. It is therefore likely these windows are valid but correspond to weak barriers because they are on the coastal regions, as it were, of islands. For some islands, such as island 2, only trees with low SRB (i.e. less than 0.002) are recovered. The question arises of whether these are genuine weak barriers or background. We believe this island likely harbours a genuine barrier locus for four reasons: (1) it harbours the key yellow pigment biosynthetic gene, AS1, (2) it is linked to a locus affecting yellow flower colour, (3) it exhibits clines across the hybrid zone, (4) like ROS and other well-studied barrier loci, the island exhibits the A partition, which is only one out 18!/(9!x9!) = 48,620 possible partitions for a 9:9 division, making its occurrence by chance unlikely given that there are of the order of 100 trees with a 9:9 division (Fig. 2a). Island 2 therefore most likely harbours a weak barrier locus. Similarly, islands 5 and 7 may be weak barriers, though evidence based on homology to a gene with known function in yellow pigmentation is less compelling. Thus, partition windows with low SRB can arise either because they are on the flanks of a strong barrier or because they derive from a weak barrier. We will clarify this point in the revised version.

      (3) If so, it might be worth revisiting/softening some of the conceptual framing throughout the paper, because trees with lower SRB values would be consistent with gene flow across the partitions (i.e., not barrier loci). Would a more conservative approach be to first summarize SRB length in the set of non-singleton trees, filter individuals based on an empirically derived SRB threshold, and then cluster the set of SRB-outlier trees? The paper would be improved by clarifying whether and how the method, as presented, reproducibly identifies barrier loci corresponding to deep divergence events.

      To address these weaknesses, the authors should provide a more nuanced discussion of the nature of the genomic regions returned from their algorithm and suggest/demonstrate approaches to reproducibly return genuine barrier loci.

      Following the reviewer’s helpful suggestion, we have explored the other option of using SRB as the first filter. We plotted frequency histograms for SRB values for all trees and non-singleton trees:

      Author response image 1.

      The distribution is a unimodal decline with SRB (note vertical log scale) without a clear threshold. Presumably this distribution reflects fluctuations in gene flow, mutation rate, the effects of limited pool size, window size, and tree construction approximations. SRB values extend to higher values than with our forest analysis (where maximum SRB is 0.0035, Fig. 3b) because high-SRB trees are often grouped into forests with low-SRB trees, giving a low forest mean. 14.4% of all trees and 6.1% of non-singleton trees have SRB >0.002, the threshold used for identification of outlier forests. The SRB distribution helps clarify where the resolving power of our method comes from for different partitions.

      Consider the 9:9 division, which has 48,620 possible partitions. The observed flower colour forest mainly comprises about 50 trees, of which 30 give the A partition that divides according to flower colour (Supp Fig. 2). The probability of an A tree occurring by chance within a 9:9 division is 1/48,620 = 2 x 10<sup>-5</sup>. Taking the observed number of 100 trees with a 9:9 division, and assuming that an A tree is identified, the probability of a second one occurring by chance among the 100 trees is of order of 10<sup>-3</sup>, and the probability of a third one occurring is 10<sup>-6</sup>. The probability of a forest containing 30 A-partition trees, even allowing for window overlaps, is negligible. Together with the high mean SRB for this forest, the evidence that the forest contains barrier loci is strong from blind-tree scanning alone.

      The evidence in favour of the partition B forest harbouring barrier loci based on blind-tree scanning alone is much weaker. This forest derives from only two overlapping windows, so the argument based on repeated independent recovery of the same partition cannot be used. The forest is recovered because of its high SRB value (> 0.003) and distinctive tree architecture which prevents it from being grouped with lower-SRB trees. Other criteria, such as clines and linkage to trait loci need to be considered in evaluating its candidacy as a barrier locus.

      We thank the reviewer for raising this point as it clarifies the contributions of tree similarity and division depth (SRB) to identifying barriers. We will incorporate the histogram and discuss these points in the revised version.

      (4) Finally, we suggest the authors include a brief discussion of how variation in the rate of molecular evolution across loci affects the results, given that the SRB threshold is an absolute (not relative) threshold.

      This comment suggests that the reviewer attributes low SRB to low rates of molecular evolution rather than low barrier strength. This is understandable as we did not discuss the possible causes of low SRB. We will remedy this omission in the revised manuscript as outlined in response to points 2 and 3 above.

      Reviewer #2 (Public review):

      We thank the reviewer for their valuable comments and summary of the paper. The reviewer’s comments have been invaluable in helping us to clarify the biological implications of our findings and relating our method to others. We address issues concerning hybrid incompatibility, Dxy and power in turn below.

      (1) Hybrid incompatibility

      Unfortunately, the biological implications of our findings did not come across clearly to the reviewer because of a misunderstanding concerning hybrid incompatibility.

      The model presented to explain the flower barrier loci is in essence driven by divergent selection. Overall, little effort is made in the paper to explain conceptually different processes, and the ambiguity of the text makes interpretation difficult and inconclusive.

      The model we propose is a two-peaked fitness landscape which is fixed rather than needing to change according to environmental conditions (Fig. 10 d and e). Thus, the fitness landscape can be the same either side of a hybrid zone. What differs is flower colour allele frequencies: striatum alleles near fixation on one side of the hybrid zone, underlying one peak, and pseudomajus alleles near fixation on the other side, underlying the other peak. Flow of flower colour alleles between the two sides is reduced because of lower fitness of hybrid genotypes which fall in the fitness valley between the peaks. These hybrids form in the contact zone. Thus, in contrast to the reviewer’s interpretation, we are not proposing that divergent selection through environmental differences underlies the barrier, because the fitness landscape is fixed. It is the fitness valley that creates the barrier rather environmental variation. We will revise the paper to make this point clearer.

      The authors present two competing hypotheses: (i) that flower color genes act as barrier loci because they are eco-adaptive, and (ii) that the fitness landscape for flower color has two peaks within the same environment. The alternative framing of these two hypotheses is confusing because having multiple peaks in a fitness landscape is not mutually exclusive to being eco-adaptive, as they actually mention in the discussion.

      We wonder if confusion has arisen here because we did not explicitly state that with the hybrid incompatible hypothesis alone, it is not only that the fitness landscape has two peaks in a given environment, but that the fitness landscape need not vary from one environment (or geographical location) to another. By contrast, with a pure eco-adaptive hypothesis the position of a single peak varies with environment (i.e. it tracks the environment), and there is no valley between peaks in the fitness landscape (i.e. no hybrid incompatibility). Based on our findings and those of others, we argue that the eco-adaptive (single peak) hypothesis alone is an unlikely explanation for the data. A hybrid-incompatibility (two peak) hypothesis alone could account for the data. However, so could a mixed model, involving both mechanisms. Thus, in the Discussion we write: “The two-peak hypothesis does not rule out eco-adaptive effects: the relative heights of the two peaks may vary according to environment.” We will clarify these points in the revised version.

      It is unclear how the double-peak hypothesis is consistent with the geographic separation of the populations. Following the rationale presented in the manuscript, the two phenotypes should be able to co-occur, but, as far as I understand, this is not realised in nature.

      The reviewer interprets our hypothesis as suggesting that because there are two peaks in the fitness landscape, both can be occupied at the same time and same location. This is not what we are suggesting. Instead, we propose one peak is occupied on one side of a hybrid zone, and the other peak occupied on the other side. Given that the loci controlling magenta and yellow flower colour map to 6 different chromosomes, recombination (segregation) would prevent the two morphs from co-occurring in substantial frequencies. This expectation is borne out by the range of phenotypes observed at a hybrid zone. Thus, geographical separation of the two morphs not only consistent with our double-peak hypothesis; it is a requirement, given the number of unliked loci involved. The unlinked nature of the loci is mentioned throughout the text, but we will further clarify the point in the revised version.

      Taken together, the reviewer’s comments reveal that we did not convey our hypothesis with sufficient clarity. The resulting misunderstandings have nevertheless been helpful for us to identify potential ambiguities in the paper that will be remedied in the revised version.

      (2) Dxy

      This lack of conceptual elaboration also hinders interpretation of the Dxy-based distance trees in general. For example, it is unclear what the genome-wide Dxy tree (which appears distinct from the consensus phylogeny) is supposed to reflect, what evolutionary mechanisms could generate alternative tree topologies (partitions), how much of this is due to technical noise and skewed sampling versus demographic history and lineage sorting, and how such alternative partitions should be treated. The theoretical basis for distinguishing barrier from (old) adaptive loci, the properties of Dxy relative to other metrics, and the relationship between Dxy trees and these fundamental concepts need to be explained in light of the evolutionary mechanisms that generate the signal captured by this metric.

      We agree that giving more background on the use of Dxy would be helpful. Dxy is not typically used as a primary metric for trees or for identifying barrier loci because it confounds within-population diversity with between-population diversity. As shown in the trees of Fig.2, the lengths of the terminal branches reflect within-population divergence, while the length of root branches reflects between-population divergence. Dxy genome scans also tend to be quite noisy, which is why Fst is preferred: it subtracts within- from between-population diversity. Dxy is typically used as a secondary metric to investigate the basis of Fst peaks. However, Dxy has a major advantage for detecting barrier loci, in that it is not sensitive to sweeps or inbreeding if sampled over a sufficiently large region of the genome. We show that when used for genomic scanning, Dxy trees can identify barrier loci at least as effectively as Fst comparisons, and with the advantage of not having to use prior pairwise assignments of populations. We will give this additional background in the revised version of the paper.

      (3) Power of the method

      The paper would benefit from power analyses to assess the method's sensitivity and specificity under a range of evolutionary parameters (e.g. divergence time, migration rate), i.e., how old and how reduced must the local migration rate be (in comparison to the genome-wide distribution) for this method to be able to detect a significant signal? Knowledge of the sensitivity, specificity and limits of this approach is crucial, especially for the method's target application, i.e., less well-studied organisms with poorly characterized phenotypes. The most convincing results presented in the paper fall back to the partition corresponding to loci underlying divergent phenotypes that were already known a priori (i.e., the flower color loci), therefore questioning the primary scope of the new method. Further, the implementation presented currently lacks statistical procedures to discern significant forests from potential false positives. Guidance on model parameters (SRB and cophenetic correlation coefficient c thresholds, which are shown to have large effects on the results) should be proposed beyond heuristics, ideally based on an empirical null and probabilistic framework, and accounting for multiple hypothesis testing, to properly quantify model power.

      We perform a sensitivity analysis by exploring the effect of different c and SRB thresholds (Supp Figures 3-5). We agree that it would be desirable to perform further sensitivity analysis through simulations of various scenarios. While such analysis is beyond the scope of the paper, following points raised by both reviewers, we will incorporate a more extensive discussion about resolving power along the following lines: See Author response image 1.

      Frequency histograms of SRB for all trees and non-singleton trees exhibit a unimodal decline with SRB (note vertical log scale). Presumably this distribution reflects fluctuations in gene flow, mutation rate, the effects of limited pool size, window size, and tree construction approximations. SRB values extend to higher values than with our forest analysis (where maximum SRB is 0.0035, Fig. 3b) because high-SRB trees are often grouped into forests with low-SRB trees, giving a low forest mean. 14.4% of all trees and 6.1% of non-singleton trees have SRB >0.002, the threshold used for identification of outlier forests. The SRB distribution helps clarify where the resolving power of our method comes from for different partitions.

      Consider the 9:9 division. The observed flower colour forest mainly comprises about 50 trees, of which 30 give the A partition that divides according to flower colour (Supp Fig. 2). There are 18!/(9!x9!) = 48,620 possible partitions for a 9:9 division, so the probability of an A tree occurring by chance within a 9:9 division is 1/48,620 = 2 x 10<sup>-5</sup>. Taking the observed number of 100 trees with a 9:9 division, and assuming that an A tree is identified, the probability of a second one occurring by chance among the 100 trees is of order of 10<sup>-3</sup>, and the probability of a third one occurring is 10<sup>-6</sup>. The probability of a forest containing 30 A-partition trees, even allowing for window overlaps, is negligible. Together with the high mean SRB for this forest, the evidence that the forest contains barrier loci is strong from blind-tree scanning alone.

      The evidence in favour of the partition B forest harbouring barrier loci based on blind-tree scanning alone is much weaker. This forest derives from only two overlapping windows, so the argument based on repeated independent recovery of the same partition cannot be used. The forest is recovered because of its high SRB value (> 0.003) and distinctive tree architecture which prevents it from being grouped with lower-SRB trees. Other criteria, such as clines and linkage to trait loci need to be considered in evaluating its candidacy as a barrier locus.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Reviewer #1 (Public review):

      Summary:

      Is peristimulus alpha (8-14 Hz) frequency and/or phase involved in shaping the length of visual and audio-visual temporal binding windows, as posited by the discrete sampling hypothesis? If so, to what extent and perceptual scenario are they functionally relevant? The authors addressed such questions by collecting EEG data during the completion of the widely known 2-flash fusion paradigm, administered both in a standard (i.e., visual only, F2) and audio-visual (i.e., 2 flashes and 1 beep, F2B1) fashion. Instantaneous frequency estimation performed over parieto-occipital sensors revealed slower alpha rhythms right after stimulus onset in the F2B1 condition, as compared to the F2, a pattern found to correlate with the difference between modality-specific ISIs (F2B1-F2). Of note, peristimulus alpha frequency differed also between 1- vs 2-flash reports, although in the visual modality only (i.e., faster alpha oscillations in 2-flash percept vs 1-flash). This pattern of results was reinvigorated in a causal manner via occipital tACS, which was capable of, respectively, narrowing down vs enlarging the temporal binding window of individuals undergoing 13 Hz vs 8 Hz stimulation in the F2 modality alone. To elucidate what the oscillatory signatures of cross-modal integration might be, the authors further focused on the phase of posterior alpha rhythms. Accordingly, the Phase Opposition Sum proved to significantly differ between modalities (F2B1 vs F2) during the prestimulus time window, suggesting that audio-visual signals undergo finer processing based on the ongoing phase of occipital alpha oscillations, rather than the speed at which these rhythms cycle. As a last bit of information, a computational model factoring in the electrophysiological assumptions of both the discrete sampling hypothesis and auditory-induced phase-resetting was devised. Analyses run on such synthetic data were partially able to reproduce the patterns witnessed in the empirical dataset. While faster frequency rates broadly provide a higher probability to detect 2 flashes instead of 1, the occurrence of a concurrent auditory signal in cross-modal trials should cause a transient elongation (i.e. slower frequency rate) of the ongoing alpha cycle due to phase-reset dynamics (as revealed via inter-trial phase clustering), prompting larger ISIs during F2B1 trials. Conversely, the model provides that alpha oscillatory phase might predict how well an observer dissociates sensory information from noise (i.e., perceptual clarity), with the second flash clearly perceived as such as long as it falls within specific phase windows along the alpha cycle.

      Strengths:

      The authors leveraged complementary approaches (EEG, tACS, and computational modelling), the results thereof not only integrate, but depict an overarching mechanistic scenario elegantly framing phase-resetting dynamics into the broader theoretical architecture posited by the discrete sampling hypothesis. Analyses on brain oscillations (either via frequency sliding and phase opposition sum) mostly appear to be methodologically sound, and very well supported by tACS results. Under this perspective, the modelling approach serves as a convenient tool to reconcile and shed more light on the pieces of evidence gathered on empirical data, returning an appealing account on how cross-modal stimuli interplay with ongoing alpha rhythms and differentially affect multisensory processing in humans.

      Weaknesses:

      Some information relative to the task and the analyses is missing. For instance, it is not entirely clear from the text what the number of flashes actually displayed in explicit short trials is (1 or 2?). We believe it is always two, but it should be explicitly stated.

      Moreover, the sample size might be an issue. As highlighted by a recent meta-analysis on the matter (Samaha & Romei, 2024), an underpowered sample size may very well drive null findings relative to tACS data in F2B1 trials, in interplay with broad and un-individualised frequency targets.

      Some criticality arises regarding the actual "bistability" of bistable trials, as the statistics relative to the main task (i.e., the actual means and SEMs are missing) broadly point toward a higher proclivity to report 2 instead of 1 flash in both F2B1 and F2 trials. This makes sense to some extent, given that 2 flashes have always been displayed (at least in bistable trials), yet tells about something botched during the pretest titration procedure.

      Coming to the analyses on brain waves, one main concern relates to the phase-reset-induced slow-down of posterior alpha rhythms being of true oscillatory nature, rather than a mere evoked (i.e., not sustained over time). Another question calling for some further scrutiny regards the overlooked pattern linking the temporal extent of the IAF differences between F2 and F2B1 trials with the ISIs across experimental conditions (explicit short, bistable, and explicit long). That is, the wider the ISI, the longer the temporal extent of the IAF difference between sensory modalities. Although neglected by the authors, such a trend speaks in favour of a rather nuanced scenario stemming from not only auditory-induced phase-reset alpha cycle elongation, but also some non-linear and perhaps super-additive contribution of flash-induced phase-resetting. This consideration introduces some of the issues about the computational simulation, which was modelled around the assumption of phase-resetting being triggered by acoustic stimuli alone. Given how appealing the model already is, I wonder whether the authors might refine the model accordingly and integrate the phase-resetting impact of visual stimuli upon synthetic alpha rhythms. Relatedly, I would also suggest the authors to throw in a few more simulations to explore the parameter space and assay, to which quantitative extent the model still holds (e.g. allowing alpha frequency to randomly change within a range between 8 and 13 Hz, or pivoting the phase delay around 10 or 50 ms). As a last remark, I would avoid, or at least tone down, concluding that the results hereby presented might reconcile and/or explain the null effects in Buergers & Noppeney, 2022; as the relationship between IAFs and audiovisual abilities still holds when examining other cross-modal paradigms such as the Sound-Induced Flash-Illusion (Noguchi, 2022), and the aforementioned patterns might be due to other factors, such as a too small sample size (Samaha & Romei, 2024).

      We thank Reviewer 1 for the detailed and constructive comments. The main revisions are summarized below:

      (1) We clarified the task design, the definition of the temporal integration window, and the interpretation of the bistable reports.

      (2) We expanded the Methods to specify the POS time-frequency decomposition, posterior ROI, label-permutation procedure, leakage control, non-aligned KL analysis, and the complete simulation workflow and parameters.

      (3) We corrected the bistable-report calculation using the actual valid-trial counts and added the corresponding frequentist and Bayesian results, together with the alpha-peak estimate, multiple-comparison corrections, and ITC/power controls.

      (4) We revised the tACS interpretation so that the interaction is the primary result and the F2B1 null finding is treated cautiously.

      (5) We expanded the computational model description and added the requested time-resolved simulated IAF and POS analyses.

      Reviewer #1 (Recommendations for the authors):

      (1) Line 64 - “Temporal windows, a fundamental attribute of the visual system, refer to time intervals during which discrete stimuli interact to influence perception”. I would delve a little deeper into the notion of temporal binding windows, given their relevance throughout the manuscript. Although the definition provided is broadly right, the way stimuli interact is dictated by the observer's degree of perceptual tolerance and/or sensitivity to noise. Hence the term “windows”.

      We thank the reviewer for the suggestion. The Introduction now defines the temporal integration window and clarifies how its width is quantified in the double-flash paradigm. Specifically, a higher fusion-threshold ISI indicates that two flashes can remain susceptible to fusion across a longer temporal separation.

      We have therefore added the following text to the Introduction: “The temporal integration window defines the range of separations over which distinct visual events can interact and be fused into a single percept (Samaha and Romei, 2024). Sensory uncertainty influences audiovisual simultaneity judgments, and stimulus reliability affects the temporal integration of successive visual inputs (Cary et al., 2024; Rangelov et al., 2021). In the double-flash paradigm, its width is indexed by the fusion-threshold ISI, defined as the separation at which one-flash and two-flash reports are equally likely. A higher threshold therefore indicates a wider integration window.”

      (2) Line 107 - “Upon comparing different conditions, our investigation revealed that the introduction of auditory stimuli effectively prolonged the temporal window of integration by reducing the instantaneous frequency of alpha oscillations.” This sentence is a bit difficult to follow. It is not clear how the temporal window of integration prolongation has been measured. Moreover, it is not clear what you mean by the reduction of instantaneous frequency. Is it a reduction in the frequency of alpha?

      We thank the reviewer for identifying this ambiguity. The temporal integration window was quantified behaviourally using the fusion threshold, defined as the interstimulus interval (ISI) at which one- and two-flash reports were equally likely. This threshold shifted from 52.68 ± 12.25 ms in F2 to 65.19 ± 13.17 ms in F2B1, indicating an extended integration window.

      Instantaneous alpha frequency was calculated from the local temporal derivative of the unwrapped alpha phase. A lower value therefore indicates slower local phase progression. In F2B1, this slowing occurred transiently during the 0–280-ms post-stimulus interval and should not be interpreted as a sustained change in trait-like individual alpha frequency. We have therefore added the following sentences to the Introduction: “Behaviourally, the auditory beep shifted the fusion threshold to longer ISIs, indicating an extended temporal integration window. This behavioural extension was accompanied by a transient post-stimulus reduction in instantaneous alpha frequency.”

      We have also clarified the correlation analysis to specify that the auditory-induced increase in post-stimulus alpha-cycle length (ΔCycle, F2B1 − F2; defined as the inverse of mean instantaneous frequency) was positively associated with the increase in fusion threshold across participants (Pearson’s r = .45, p = .008; Figure 2D–E). Thus, participants showing greater auditory-induced alpha-cycle lengthening also showed a larger extension of the temporal integration window.

      These changes have been incorporated into the Psychophysical Results, the alpha-frequency Results, and the correlation analysis.

      (3) Line 117 - “Our simulation results indicate that the introduction of auditory input resets the phase of alpha oscillations, subsequently extending the temporal window through a reduction in alpha frequency. This modification significantly influences the predictive roles of both phase and frequency.” Here you imply that phase reset is accompanied also by a slowdown of the frequency following the phase reset? Just want to make sure I get this right, and if so it should be more clearly stated.

      We thank the reviewer for requesting this clarification. Yes, in our model, the auditory-induced phase reset is accompanied by a transient slowing of instantaneous alpha frequency. The phase reset delays the ongoing phase trajectory and temporarily lengthens the current cycle. Because instantaneous frequency is defined as the local temporal derivative of phase, this perturbation appears as a brief reduction in instantaneous frequency. Importantly, the slowing is time-limited and does not represent a sustained change in trait-like alpha frequency.

      We have therefore stated this more clearly in the Results on the phase-resetting model: “In the model, the auditory event delays the ongoing phase trajectory; because instantaneous frequency is the local temporal derivative of phase, this delay temporarily lengthens the current cycle and appears as a brief reduction in instantaneous frequency shortly after the auditory event. The slowing is time-limited, recovering as the trajectory continues, and is distinct from a sustained change in trait-like individual alpha frequency.”

      (4) Line 692 - Although reasonable, the sample size (34 and 30 participants, respectively) might turn out to be slightly underpowered in light of a recent meta-analysis on the matter (around 50 participants according to Samaha & Romei, 2024). That is, there might be some chances that weaker and more subtle effects exerted by alpha frequency effects in F2B1 trials have been overshadowed due to an underpowered sample size.

      We thank the reviewer for raising this important point. We agree that the sample sizes of the EEG and tACS experiments may have limited sensitivity to small condition-specific effects, particularly in the F2B1 condition. We have therefore interpreted the corresponding null findings cautiously.

      In the EEG experiment, the absence of an alpha-frequency difference between one- and two-flash reports in F2B1 was accompanied by a Bayes factor of BBFF<sub>(01)</sub> = 4.88. In the tACS experiment, the principal finding was the stimulation-frequency × sensory-condition interaction rather than the F2B1 contrast considered in isolation; the latter yielded BBFF<sub>(01)</sub> = 5.05. These Bayes factors provide moderate evidence for the null under the present design, but do not exclude smaller effects that may require larger samples to detect. We have therefore revised the Discussion to describe the influence of alpha frequency as reduced in F2B1 relative to F2, rather than concluding that alpha frequency plays no role in the audiovisual condition. We also acknowledge that larger studies using individualized stimulation frequencies would provide a stronger test. 

      The corresponding interpretation and limitations have been clarified in the Discussion.

      (5) Line 717 - 90% accuracy in explicit short trials (30ms ISI)? How did participant bistable ISIs (50% 2-flash report) range between 55–65 ms across modalities then?

      Accuracy in the practice/explicit trials was scored against the predominant report (one flash at 30 ms and two flashes at 100 ms), although two physical flashes were always displayed. The condition-specific fusion threshold is instead the fitted ISI at which one- and two-flash reports are equally likely. The two measures answer different questions: the 90% criterion confirms task comprehension at the easy extreme ISIs, whereas the titration locates the point of maximal ambiguity, so there is no contradiction between them.

      We have clarified this distinction in the Methods.

      (6) Line 723 - For the sake of clarity, it should be outlined what kind of logistic function (along with a brief description of the relative parameters) and fitting algorithm were employed (for both the pretest psychometric procedure and tACS protocols), and whether any constraint to said parameters was applied to allow better fits (higher R<sup>2</sup>). On the same rationale, it would also be helpful to explicitly add the resulting ISIs on each participant's panel (Supplementary Figure 1).

      We thank the reviewer for requesting further clarification of the psychometric fitting procedure. Both the pretest and tACS data were fitted using the same two-parameter binomial logistic model. In this model, ββ<sub>0</sub> represents the intercept and ββ<sub>1</sub> represents the change in the log odds of a two-flash report per millisecond. The parameters were estimated by maximum likelihood using MATLAB glmfit, and the fusion threshold was defined as the ISI corresponding to a two-flash probability of 0.5.

      No parameter constraints were imposed during fitting. Because the dependent variable consisted of binomial counts, model fitting was based on the binomial likelihood rather than ordinary least-squares R2. We have also added the fitted fusion-threshold ISIs to the corresponding participant panels in Figure 1—figure supplement 1.

      We have therefore revised the Methods subsection “Psychophysical pretest and threshold estimation” accordingly.

      (7) Line 735 - Germane to what is underlined at 5, the employment of explicit long vs short trials seems to somehow gainsay the concurrent psychometric approach. For instance, to participants displaying narrow vs enlarged temporal window (short vs long ISIs), explicit short trial should turn out to be less (if not) vs more challenging (and vice versa), while the adoption of individually-titrated ISIs rules out such inter-individual perceptual variability, which may jeopardize the way the associated neural effects are interpreted. However, if the authors deem these analyses relevant (and not redundant) to the manuscript, I suggest that they at least move their relative results and charts into the Supplementary Information.

      We thank the reviewer for raising this important distinction. We agree that the fixed short- and long-ISI trials were not designed to equate subjective difficulty across participants. Instead, they served as physical-ISI controls: within each fixed-ISI trial type, the visual sequence was identical between F2 and F2B1, allowing us to assess the effect of the auditory input while holding visual timing constant.

      By contrast, the individually titrated bistable trials were used for the primary analyses relating neural activity to alternative perceptual outcomes. Because the fusion threshold was estimated separately for each participant and sensory condition, these trials approximately equated perceptual ambiguity and reduced the influence of inter-individual differences in temporal integration.

      Following the reviewer’s suggestion, we have clarified the distinction between the fixed-ISI and individually titrated trials in the Results. The fixed-ISI behavioural analyses are presented in Figure 1—figure supplement 3, and the corresponding detailed neural analyses are presented in Figure 2—figure supplement 1.

      (8) Line 738–739 - It has not been thoroughly clarified whether, for each trial type (explicit short and long, plus bistable), the same amount of F2 and F2B1 conditions occurred

      We thank the reviewer for requesting this clarification. Yes, within each trial type—explicit short-ISI, explicit long-ISI, and individually titrated bistable trials—F2 and F2B1 trials were scheduled in equal numbers. Thus, the two sensory conditions were equally represented within each trial type by design.

      Following artifact rejection, the number of retained trials could differ slightly between conditions. All artifact-free trials were retained for the explicit short- and long-ISI analyses, whereas trial counts were matched across the sensory-condition × perceptual-report cells for the primary bistable IAF and POS analyses. We have clarified both the experimental allocation and the subsequent trial-count handling in the Methods.

      (9) Line 751–753 - What kind of low-pass and high-pass, or band-pass filters have been used, besides the notch filter? More importantly, at line 738, you have mentioned that the fixation time ranged randomly between 500 and 1500 secs. Such a time window turned out to be the prestimulus interval after trial epoching (since there is no mention of any inter-trial jitter), spanning from −1300ms to stimulus onset. How then have you dealt with trials wherein the fixation time (i.e., to-be prestimulus interval) was < 1300 ms?

      We thank the reviewer for raising this concern. We apologize that the original description did not make the complete trial timing sufficiently clear. Following the second flash, each trial contained a fixed 2,000-ms interval. This interval always elapsed in full, regardless of how quickly the participant responded, and the 500–1,500-ms fixation period of the next trial began only after this interval had ended. Thus, the interval between the end of one stimulus sequence and the onset of the next was 2,500–3,500 ms.

      Because the EEG data were epoched from −1,300 to 1,000 ms relative to first-flash onset, even the earliest sample of each epoch occurred at least 1,200 ms after the preceding stimulus sequence. Moreover, the observed times were substantially shorter than this interval (condition means of approximately 0.73 s; Figure 1—figure supplement 4), and the observed response-time range confirmed that responses were completed before the next epoch began. Therefore, the extracted epochs did not temporally overlap with either the stimulus presentation or the behavioural of the preceding trial, including on trials with the shortest fixation duration.

      Regarding filtering, the only filter applied during initial preprocessing was a 49.5–50.5-Hz bandstop filter; no broadband high-pass, low-pass, or band-pass filter was used. Band-pass filtering was applied only for the analysis-specific extraction of alpha activity (8–13 Hz; least-squares finite impulse filter, forward–reverse).

      To make the temporal structure of the paradigm explicit, we have also revised Figure 1B to show the fixed 2,000-ms interval and to clarify that the fixation period of the subsequent trial began only after this interval had elapsed.

      (10) Line 758 - On a broader level, it appears that no visual inspection allowing rejection of trials characterized with excessive noise or residual artifacts has been carried out. Does this imply that you retained each and every trial from all participants? On the same vein, no interpolation of a bad channel seems to have been performed.

      We thank the reviewer for requesting this clarification. No, we did not retain every recorded trial without inspection. Bad channels were identified for individual participants and interpolated using a weighted average of neighbouring electrodes. Independent component analysis was then used to identify and remove components associated with ocular, muscular, and other stereotyped artifacts. Following ICA, the cleaned data were visually inspected, and trials containing residual artifacts or excessive noise were excluded. We have clarified these preprocessing and artifact-rejection procedures in the revised Methods.

      (11) Line 768 - Using a fixed frequency output during the tACS protocol might have been troublesome in many ways. Entrainment-induced shifts to posterior alpha oscillations are known to be maximally effective when tailored around the individual alpha frequency peak (IAF, Cecere et al., 2015; Di Gregorio et al., 2022; Trajkovic et al., 2024). Let's take, for instance, the case of a participant whose on-task oscillatory speed cycled at 12 Hz. In such a case, 8Hz stimulation might have resulted in null effects due to the wide distance between the tACS output and an “optimal” target frequency, which should be ~ 10 or 11 Hz. Conversely, 13 Hz stimulation administered to a participant with an on-task IAF around 9 Hz would not be as beneficial as one delivered at 10 or 11 Hz. These issues, along with a slightly underpowered sample size (see 1), might have yielded null effects with regard to the F2B1 condition.

      We thank the reviewer for this important point. We agree that fixed-frequency stimulation does not account for inter-individual variation in alpha frequency and may therefore be less effective than stimulation tailored to each participant’s alpha frequency. Because the tACS experiment was conducted in an independent sample for whom individual alpha-frequency estimates were not available, the two stimulation frequencies were selected to sample the lower and upper portions of the alpha range around the group-level alpha peak. This design allowed us to test whether the effect of stimulation frequency differed between the visual-only and audiovisual conditions, but it did not provide an individualized test of frequency-specific entrainment.

      The primary tACS finding was the significant stimulation-frequency × sensory-condition interaction, indicating that stimulation frequency affected fusion thresholds differently in F2 and F2B1. The F2B1 contrast yielded BF<sub>01</sub> = 5.05, providing moderate evidence for the null under the present design; however, this does not exclude smaller effects or effects that may emerge with stimulation tailored to individual alpha frequency. We have acknowledged this limitation and now state that individualized stimulation would provide a stronger test of the role of alpha frequency in audiovisual temporal integration in the revised Discussion.

      (12) Line 776 - I reckon that the fitting procedure employed the same logistic function and parameters implemented on data relative to the titration session. This should be specified, and it may be useful to display the fitting curves resulting from this procedure in separate charts (F2 vs F2B1), perhaps in the Supplementary section, akin to what has been done for the fitting curves relative to the titration session (Supplementary Figure 1).

      We thank the reviewer for this suggestion. In our reply to Comment 6, we described the psychometric fitting procedure for the pretest in detail; the tACS curves were fitted with the same two-parameter binomial logistic model and 50% threshold definition as the pretest, separately for each participant, stimulation session, and sensory condition. The individual fitted curves are provided in Figure 5—figure supplements 2 and 3.

      We have clarified the fitting procedure in the Methods and Results.

      (13) Line 779–787 - Many technical details regarding the FFT are missing (what kind of tapering was applied to the data? Zero-padding?). Please add a few explanations to amend this.

      We thank the reviewer for requesting these methodological details. For each trial, the power spectrum was computed over the −600 to 600 ms interval using a Hanning taper. The 1.2-s data segments were zero-padded to 10 s, yielding a frequency-bin spacing of 0.1 Hz. We clarify that zero-padding increased the frequency-bin density but did not increase the intrinsic spectral resolution determined by the original data segment. These details have now been added to the Methods.

      We have revised the EEG analysis section in the Methods accordingly.

      (14) Line 803–807 - Given that in the bistable condition the number of types (1 flash vs 2 flashes) issued by each participant should be roughly the same, I guess something during the psychophysical titration procedure went wrong. However, can the authors articulate a bit further on the specific approach adopted to match the number of trials across type?

      We thank the reviewer for raising this point. The fusion threshold was defined as the ISI at which one- and two-flash reports were equally likely. Because this threshold was estimated in a separate psychophysical session, modest deviations from an exactly equal report distribution could arise from trial-to-trial sampling variability and changes in perceptual state between sessions. Nevertheless, the proportions of two- and one-flash reports remained comparable in both the F2 condition (54.8% ± 4.1% versus 45.2% ± 4.1% (mean ± SEM), t<sub>(33)</sub> = 1.18, p = .248, two-tailed, BF<sub>01</sub> = 2.89) and the F2B1 condition (53.8% ± 3.3% versus 46.2% ± 3.3%, t<sub>(33)</sub> = 1.16, p = .255, two-tailed, BF<sub>01</sub> = 2.94; Figure 1E).

      To prevent these modest differences in report frequency from affecting the EEG comparisons, artefact-free bistable trials from each participant were divided into four sensory-condition × report cells: F2 with one-flash reports, F2 with two-flash reports, F2B1 with one-flash reports, and F2B1 with two-flash reports. We identified the smallest trial count among these four cells and randomly subsampled each cell to this number. Thus, all four cells contributed an equal number of trials to the primary bistable IAF and POS-map analyses.

      We have therefore clarified this in the revised Results and Methods.

      (15) Line 829 - Comment 13 applies to the POS analyses as well.

      Thank you for identifying that the POS method needed a more transparent account. We introduce the complex time-frequency coefficient, normalize it to a unit phase vector, define ITC for each report group and their pooled trials, and then define POS as ITC (one flash) + ITC (two flashes) − 2 × ITC (pooled). A positive POS therefore requires the two report groups to be phase concentrated around different angles; it is not merely a larger phase-locking value. The inferential test permutes report labels within participant while preserving group sizes and applies the cluster procedure to the resulting POS maps.

      We thank the reviewer for pointing this out. Unlike the FFT analysis described in to Comment 13, the POS analysis was based on wavelet time–frequency decomposition; therefore, no separate taper was applied. Specifically, complex time–frequency coefficients were obtained using FieldTrip with wavelets whose number of cycles increased logarithmically from 2 at the lowest frequency to 7 at the highest frequency. The analysis included 60 logarithmically spaced frequencies from 2 to 50 Hz, evaluated from −600 to 400 ms in 20-ms steps, with zero-padding to 10 s. The resulting complex coefficients were normalized to unit phase vectors and used to calculate POS. These methodological details have now been clarified in the Methods.

      We have revised the POS analysis subsection accordingly.

      (16) Line 859–870 - This is a suggestion rather than a comment, but I would appreciate the information about the POS statistics to be moved into the “statistical analyses” section. In doing so, I believe they would improve the overall clarity of the analysis pipeline.

      We thank the reviewer for this helpful suggestion. As recommended, we have moved the POS-specific inferential procedures, including label permutation, pointwise significance estimation, cluster correction, and the direct F2B1−F2 comparison, to the Statistical analyses section. The Alpha oscillation analysis subsection now focuses on the time–frequency decomposition and definition of POS. This reorganization separates the computation of POS from its statistical inference and clarifies the overall analysis pipeline.

      We have revised the Statistical analyses section accordingly.

      (17) Line 872 - All the information regarding the statistics adopted to test the behavioural data is missing. Although pretty much intuitive, adding a few lines that specify whether any normality check was performed, and what kind of t-tests and correlation metrics were employed, would greatly benefit the quality of the manuscript from a formal standpoint.

      We thank the reviewer for this helpful suggestion. We have expanded the Statistical analyses section to clarify the procedures used for the behavioural data. Factorial comparisons were evaluated using repeated-measures ANOVAs, whereas pairwise comparisons used two-tailed paired-samples t-tests unless a directional contrast had been specified a priori. Before applying parametric pairwise tests, the corresponding within-participant difference scores were assessed using Shapiro–Wilk tests together with Q–Q plots. When normality was rejected, the parametric result was supplemented with a Wilcoxon signed-rank test and a bias-corrected bootstrap confidence interval. Between-participant associations were assessed using Pearson’s r. We also clarify that this normality screening was not applied to permutation, circular, or cluster-based analyses, whose inference does not rely on the same parametric normality assumption.

      We have revised the Statistical analyses section accordingly.

      (18) Line 887 - Given the relevance the computational model retains, I would add a detailed explanation of the steps performed to build it (i.e., those nicely rendered in Supplementary Figure 8), the parameters involved in the equations, as well as the rationale behind them. For instance, why have you opted for normally-distributed noise (line 893)? Why was the phase delay set to be centred around 25 ms (with ± 25 ms random variability, line 900)? Further, it would perhaps be interesting to explore the parameters space, in order to compare, for instance, what kind of outcome the simulation produces as the frequency of these synthetic alpha oscillations changes (i.e. 8, 10 and 12 Hz, thereby incorporating widely known interindividual differences relative to the IAF), not to mention the phase delay.

      We thank the reviewer for this constructive suggestion. We have substantially expanded the description of the computational model to clarify its construction, the role of each model component, and the procedure used to derive the simulated perceptual outcomes. In particular, we now distinguish the generation of the underlying oscillatory signal, the introduction of the auditory perturbation, the assignment of the latent perceptual outcome, and the phase-dependent reliability of the simulated report. The complete model workflow is illustrated in Figure 8—figure supplement 1.

      We also clarify that the independent, zero-mean Gaussian innovation was used as a simple neutral representation of stochastic variability, without introducing a systematic temporal drift. The temporal jitter and phase-shift parameters were intended as phenomenological representations of variability in the timing and magnitude of the auditory perturbation, rather than as precise estimates of a physiological auditory latency.

      Finally, following the reviewer’s suggestion, we conducted sensitivity analyses across a range of oscillator frequencies and perturbation delays while holding the remainder of the model pipeline constant. The frequency-sensitivity results are presented in Figure 8—figure supplement 3, and the delay-sensitivity results are presented in Figure 8—figure supplement 4. These analyses characterize how the simulated outcomes vary across parameter settings and show that the principal model behavior is not restricted to a single arbitrary parameter choice.

      We have expanded the Simulations of EEG data subsection accordingly and added the model workflow and parameter-sensitivity results to Figure 8—figure supplements 1, 3, and 4.

      (19) Line 909 - The authors need to emphasize a bit more the conceptual difference between perceptual outcome (alpha frequency) and perceptual clarity (alpha phase). Along this line of reasoning, the model provides that the phase at which the second flash occurs should dictate the higher vs lower probability of issuing an incorrect response, regardless of whether the “synthetic” outcome hits 1 vs 2 flashes. If so, this needs to be clearly stated in the manuscript.

      We thank the reviewer for highlighting this important conceptual distinction. In the model, alpha frequency determines the latent perceptual outcome by determining whether the two flashes fall within the same or different alpha cycle. By contrast, the phase at which the second flash occurs does not change this latent outcome; instead, it determines how reliably the latent outcome is translated into the simulated report.

      Importantly, this phase-dependent reliability applies symmetrically to both latent outcomes. An unfavorable phase increases the probability that the reported does not match the latent cycle-based outcome, regardless of whether that outcome is one flash or two flashes. Thus, frequency determines perceptual outcome, whereas phase determines perceptual clarity rather than favoring a particular category. This distinction is now explicitly stated in the Results and simulation Methods and is illustrated in the model workflow (Figure 6 and Figure 8—figure supplement 1).

      We have revised the Results section on the phase-resetting model and the Simulations of EEG data subsection.

      (20) Line 919 - The approach through which Hit Rates and False Alarms are defined is quite convoluted and a bit detached from the formal assumptions of signal detection theory. If the overall scope of this analysis was highlighting a link between subjective perception and reported outcome, the authors might very well compute subjective Hits and False Alarms, and then employ their ratio without assuming an equal-variance scenario. Plus, I would rather avoid using the term d', which I feel is somehow misleading in this context.

      We thank the reviewer for pointing out that the original signal-detection terminology could be misleading. We agree that the conventional notation d' may imply an empirical estimate of participants’ perceptual sensitivity under the assumptions of standard signal detection theory, which was not the purpose of this model-based analysis.

      In the simulation, the model-defined latent one-flash and two-flash states provide the reference categories, and the simulated one-flash and two-flash reports provide the corresponding categories. We therefore define the hit rate as the proportion of latent two-flash trials reported as two flashes and the false-alarm rate as the proportion of latent one-flash trials reported as two flashes. The standardized difference between these two rates is used only to summarize how reliably simulated reports discriminate the model-defined latent states.

      To avoid implying a conventional behavioural d', we have renamed this quantity the model-based discriminability index, denoted DD<sub>mmmmmmmmmm</sub>, throughout the manuscript. This index should not be interpreted as an estimate of participants’ perceptual sensitivity, criterion, or underlying equal-variance sensory distributions. This terminological revision does not alter the calculation or conclusions of the simulation. The corresponding labels have also been updated in Figure 8F and Figure 8—figure supplement 4.

      We have revised the Simulations of EEG data subsection accordingly, together with the corresponding equation, figure labels, and legends.

      (21) Line 157 - “In the main EEG experiment, each condition comprised three types of trials: the explicit short-ISI trials (30 ms, typically reported as one flash), the explicit long-ISI trials (100 ms, typically reported as two flashes)”. However, in the Methods section (lines 716–717) there is no mention of short vs long explicit trials differing in terms of number of flashed displayed, implying that 2 flashes were always emitted [.. prior to the psychophysical pretest, participants completed a practice block consisting solely of explicit short (30 ms) and long trials (100 ms) until accuracy reached at least 90%..], in line also with lines 737–741 [..Each trial began with a central fixation lasting 500 to 1500 ms, followed by a 10 ms presentation of the first visual stimulus, accompanied by an auditory beep or not. After a variable ISI (30 ms, 100 ms, or the participant's individual fusion threshold), the second frame was displayed for 10 ms,.], and Figures 1A and B. This point should be promptly addressed (see also 5 within the “Methods” comments), as it is hard to reconcile around 90% accuracy rates in explicit short trials wherein 2-flashes were always displayed, with bistable ISIs (50% accuracy rates) centred around 55 - 65ms.

      We thank the reviewer for identifying this ambiguity. Two physical flashes were presented in every trial; the labels “short” and “long” refer exclusively to the ISI between the two flashes, rather than to the number of physical flashes presented. At the short ISI, the two flashes were typically integrated and reported as one flash, whereas at the long ISI they were typically resolved and reported as two flashes.

      Accordingly, accuracy in the explicit trials was operationally defined relative to the predominant percept expected at each ISI: a one-flash report was scored as correct for the explicit short-ISI trials, whereas a two-flash report was scored as correct for the explicit long-ISI trials. This explains why accuracy could approach 90% even though two physical flashes were presented in both trial types. In contrast, the bistable trials used each participant’s fusion-threshold ISI, at which one- and two-flash reports were approximately equally likely.

      We have therefore revised the psychophysical Results and clarified the physical stimulus sequence and operational definition of accuracy in the psychophysical Methods.

      (22) Line 162 - Stating that 1 vs 2 flash reports were comparable across modalities (F2 vs F2B1) in the bistable condition is somehow misleading, as both t-tests proved to be marginally significant (all p-values < .075), suggesting a subtle trend that should be accounted for when interpreting the results. That is, participants appear to more often report 2 flashes, rather than 1. Approaching this via Bayesian t-tests might help the reader in understanding how actually comparable trials were in terms of perceptual ambiguity. For the sake of clarity, it would also be useful to add means and S.E.M. for each condition across sensory modality in the main text, as well as change Figure 1E into a double raincloud plot (with mean point and S.E.M. error bars), similar to that in Figure 1D. Related to the above, looking at Figure 1E, it is not clear what the y-axis stands for by saying percentage of percepts. Do you mean percentage of 2-flash percept? This should be clarified. It clearly seems that the two conditions are not completely balanced even in ambiguous trials. And I wonder whether the veridical 1 flash condition could be used as a catch trial for computing d prime and criterion measures to test for the impact of sensitivity and bias in this type of effect.

      We thank the reviewer for raising these points. During revision, we recalculated the bistable-report proportions using the actual number of valid trials retained for each participant and condition. Reinspection of the raw log files revealed that the trial counts used in the initial analysis did not match the actual valid-trial counts for a number of participants: the first nine participants had completed 520 rather than 560 trials (fewer bistable trials per condition), and for two further participants, whose sessions had been interrupted and split across log files, the counts included missed trials. We apologize for this counting error. In the revised analysis, two-flash reports were numerically more frequent than one-flash reports, but the imbalance was not statistically reliable in either F2 (54.8% ± 4.1% versus 45.2% ± 4.1% (mean ± SEM), t<sub>(33)</sub> = 1.18, p = .248, two-tailed, BF<sub>01</sub> = 2.89) or F2B1 (53.8% ± 3.3% versus 46.2% ± 3.3%, t<sub>(33)</sub> = 1.16, p = .255, two-tailed, BF<sub>01</sub> = 2.94; Figure 1E). The Bayes factors modestly favored the null hypothesis over the presence of a systematic report imbalance. Moreover, the percentage of two-flash reports did not differ between F2 and F2B1, t<sub>(33)</sub> = 0.21, p = .834. We have therefore revised the text to describe the report proportions as approximately, rather than completely, balanced.

      The requested means and SEMs are now reported in the main text. We retained the paired distribution plot in Figure 1E because it displays all participant-level observations, their within-participant pairing, and the distribution summary for each report category. However, we clarified the y-axis and figure legend to indicate that the values represent the percentage of valid bistable trials assigned to each perceptual report.

      A conventional behavioural d' and criterion analysis cannot be calculated from this experiment because every physical trial contained two flashes. In particular, the explicit short-ISI trials were not veridical one-flash catch trials; they also contained two physical flashes that were typically fused into a one-flash percept. Consequently, there is no physically defined signal-absent category from which standard hit and false-alarm rates could be constructed. The separate model-based discriminability index uses model-defined latent states and should not be interpreted as a behavioural d'.

      We have revised the psychophysical Results, clarified the physical stimulus sequence in the psychophysical Methods, and revised Figure 1E and its legend accordingly.

      (23) Line 168 - Can the authors report the mean Hz of such a clear peak (along with the associated S.E.M)?

      The mean participant-level alpha peak was 10.12 ± 0.24 Hz (mean ± SEM), obtained as the 8–13 Hz maximum of each participant's trial-averaged FFT spectrum.

      We have therefore revised the Results.

      (24) Line 174 -“Building upon our behavioral observations, we noted a significant extension in the temporal window for visual integration when auditory input was introduced.” Germane to point 1 within the “Introduction” comments, I see the authors use this concept of extended temporal window of integration without describing what it means. I think this should be defined clearly. The authors may define it as the proportion of time within which the fusion effect takes place by inducing the participants to report one visual flash when in fact two flashes were presented. In the two-flash conditions, this window seems to last much less than in the two-flash one-beep condition. So, I suggest that the authors explicitly define what they mean by temporal window of integration (period where the fusion takes place).

      We thank the reviewer for requesting a clearer definition. In the present study, the temporal window of integration refers to the range of ISIs over which two physically presented flashes tend to be integrated and reported as a single flash. We operationalized the boundary of this window as the fusion threshold—the ISI at which one- and two-flash reports were equally likely, as estimated from the psychometric curve.

      Accordingly, a rightward shift of the fusion threshold indicates that fusion remains likely over longer temporal separations between the two flashes and therefore reflects an extended temporal integration window. This operational definition and the corresponding threshold estimates are illustrated in Figure 1C–D and Figure 1—figure supplement 1.

      We have clarified this definition in the Psychophysical Results.

      (25) Line 176–178 - “If we assume that alpha frequency serves as an indicator of the temporal window within the visual cortex, it is plausible to hypothesize that alpha frequency in the F2B1 condition might decrease compared to the F2 condition.” Or that a phase reset takes place without calling alpha frequency into account. As a matter of fact, phase reset may be the mechanism by which integration is prolonged, and considering this as a slowed alpha frequency may be an artefact, unless you demonstrate that it is more sustained in time than just the period around the sound is played. The authors use instantaneous alpha frequency, which may be, paradoxically, less sensitive to sustained effects and read change in phase as a change in frequency. Unless one says that a change in phase is by definition a change in frequency, and the fact that it is induced by an external stimulus, doesn't diminish the fact that it results in a slowing down of the ongoing alpha frequency. My question is rather whether this effect is evoked by the stimulus and ends with the stimulus or whether it reverberates over a few cycles, which would make it more of an oscillation and less of an evoked to the external stimulus. I wonder whether the effect would still be there for longer time windows or by using a more classical FFT over a longer time window post-stimulus? Distinguishing between these two conditions could tell us more about the effects found here of a lack of correlation between IAF and F2B1, which may have to do with stimulus-evoked phase modulation rather than the slowing down of IAF. This does not diminish the impact of IAF on time integration, as it clearly appears in more sustained conditions, such as the 2F for example, but doesn't account for the fusion illusion when the auditory input is presented. This is intriguing, as previous research has also attempted to find a relationship between the auditory-induced fusion effect and IAF with no success. However, it should be mentioned that work by Noguchi has recently shown that the change in the beta frequency may account for this effect. Maybe the authors may want to comment on this and I wonder whether they might test whether changes in the beta band frequency may alternatively explain the effects?

      We thank the reviewer for raising this important distinction. Instantaneous alpha frequency was calculated from the local temporal derivative of the unwrapped phase. Consequently, a stimulus-induced phase reset can manifest as a transient reduction in instantaneous frequency. We have therefore clarified that the present finding reflects a transient poststimulus slowing of alpha-phase progression, rather than a sustained or trait-like change in individual alpha frequency. The difference between F2B1 and F2 was detected during the 0–280-ms poststimulus interval and was not evident beyond this interval (Figure 2B), consistent with a time-limited perturbation spanning a few alpha cycles.

      As a complementary analysis, we estimated peak alpha frequency using a conventional FFT over the poststimulus interval. This analysis also showed a lower alpha peak in F2B1 than in F2 (Figure 2—figure supplement 2A). However, because the FFT summarizes spectral content across the analysis window, it cannot by itself distinguish a sustained change in the underlying oscillator frequency from a transient phase perturbation. We therefore treat this result as convergent evidence for an alpha-frequency difference during the poststimulus interval, rather than as evidence for a lasting frequency change. The accompanying increase in intertrial phase coherence without a corresponding increase in alpha power is also consistent with stimulus-induced phase reorganization rather than a simple additive evoked (Figure 7A, C).

      We also agree that alpha may not be the only frequency mechanism contributing to audiovisual fusion. In particular, Noguchi (2022) reported that lower prestimulus beta frequency was associated with greater susceptibility to audiovisual fusion. We now discuss this finding as a potentially complementary beta-band timing mechanism when auditory input contributes to fusion. A systematic beta-band analysis would require a separate set of beta-focused hypotheses and validation analyses and is therefore beyond the alpha-focused scope of the present study. We have identified this as an important direction for future work rather than implying that the observed effect is exclusively mediated by alpha activity.

      Corresponding revisions have been made in the Results section and the Discussion section. The complementary FFT analysis is presented in Figure 2—figure supplement 2A.

      (26) Line 180 - It is still not entirely clear to me the reason why you need to ensure an equal number of trials in each condition (F2 vs F2B1), since this number should already be as such (see 6 within the “Methods” comments).

      We thank the reviewer for highlighting the need to clarify this distinction. F2 and F2B1 trials were indeed scheduled in equal numbers within each trial type. However, the relevant EEG analyses were performed after artifact rejection and, for the bistable trials, after further separating trials according to one-flash and two-flash reports. Consequently, the numbers of valid trials could differ across the four sensory-condition × report cells, even though the two sensory conditions had been equally represented in the original design.

      Trial-number matching was therefore not intended to correct an imbalance in the experimental design. Rather, it ensured that the F2–F2B1 comparisons were not influenced by differences in perceptual-report composition or by trial-count-dependent differences in the precision of the neural estimates, particularly the POS/ITC measures. We have revised the Methods to make clear that this matching was applied specifically to the primary bistable IAF and POS-map analyses.

      The relevant experimental-design information is provided in the EEG experimental procedures, and the trial-matching procedure is described in the Recording and preprocessing subsection. The corresponding IAF comparison is reported in the Results.

      (27) Line 194 - The correlation results seem pretty robust. However, upon inspecting the psychometric curves at Supplementary Figure 1, I wonder whether the same pattern of results holds when removing a few participants displaying too huge (and not much plausible) ISI differences across modalities (e.g., sub03, sub08, sub11, sub18).

      We thank the reviewer for this helpful suggestion. We performed the requested sensitivity analysis by excluding sub03, sub08, sub11, and sub18. The correlation between the auditory-induced change in poststimulus alpha-cycle length and the change in fusion threshold was attenuated and was no longer statistically significant after their exclusion (r = .21, p = .271, n = 30; full sample: r = .45, p = .008, n = 34).

      We have reported this result transparently, but we did not adopt this exclusion for the primary analysis. These participants were identified on the basis of relatively large F2B1−F2 fusion-threshold differences, which constitute the behavioural variable being correlated. In the absence of an independent indication that their data were invalid, excluding participants according to the magnitude of this variable would selectively remove the upper end of its distribution and impose range restriction.

      We therefore assessed the influence of individual observations using complementary procedures that retained the full sample. The full-sample correlation remained significant in a permutation test (p = .006) and had a bootstrap 95% confidence interval that excluded zero [.08, .68]. A bisquare robust regression, which down-weighted observations deviating from the overall trend, also showed a positive association (slope = 4.30, p = .033). In addition, leave-one-participant-out correlations were positive in all 34 iterations (r = .29–.50) and remained significant in 33 of them; only the exclusion of sub18 produced a non-significant result (Figure 2—figure supplement 3). Thus, although the association is attenuated when the four participants with the largest behavioural differences are jointly removed, it is not attributable to any single participant.

      The robustness analyses are reported in the Results and Figure 2—figure supplement 3.

      (28) Line 211 - The results hereby reported aligns with those relative to bistable trials, but I suggest the authors to perform a few more correlation analyses (which may eventually be added to the Supplementary section) relating the differences in accuracy rates between F2B1 vs F2 (∆Accuracy F2B1-F2, in %) to those in alpha cycle length (∆Cycle Lengths F2B1-F2, in ms) per each trial type (explicit long vs short). This is also in light of an interesting trend toward a double dissociation across trial types and sensory modality in terms of accuracy rates (see lines 158–159), which has not been further investigated nor graphically depicted.

      We thank the reviewer for this suggestion. We performed the requested between-participant correlation analyses separately for the explicit short- and long-ISI trials. The auditory-induced change in accuracy (ΔAccuracy, F2B1 − F2) was not significantly associated with the auditory-induced change in poststimulus alpha-cycle length (ΔCycle length, F2B1 − F2) at either the short ISI (r = -.01, p = .946) or the long ISI (r = -.08, p = .671; n = 34). These correlations are now shown in Figure 1—figure supplement 3B–C, together with the explicit-trial accuracy results in Figure 1—figure supplement 3A.

      We agree that the accuracy interaction warrants clarification. We do not interpret it as evidence for a double dissociation involving two independent auditory effects. Rather, the auditory beep shifted perception in the same direction—toward fusion—at both ISIs. At the short ISI, where a one-flash report was scored as correct, this shift increased accuracy; at the long ISI, where a two-flash report was scored as correct, the same shift reduced accuracy. Thus, the opposite directions in the accuracy measure can arise from a single fusion-directed effect because the expected differs between the two ISIs.

      The absence of significant correlations indicates that we found no evidence that individual differences in the auditory-induced accuracy changes at the fixed ISIs covaried with changes in poststimulus alpha-cycle length. Because performance in these explicit conditions was generally close to the respective behavioural extremes, we interpret these null correlations cautiously. By contrast, in the bistable condition, the more sensitive fusion-threshold measure was associated with the auditory-induced change in alpha-cycle length.

      The fixed-ISI behavioural pattern is summarized in the Results. The accuracy interaction and the additional correlation analyses are reported in the Supplementary Results subsection “Explicit-trial accuracy” and Figure 1—figure supplement 3A–C.

      (29) Line 216 - To broadly summarize, instantaneous frequency estimation yielded the same pattern of results across different trial types, i.e., a post-stimulus frequency decrease in F2B1 trials, as compared to F2 trials. The authors construe this oscillatory slowdown as a transient elongation of the ongoing alpha cycle, engendered by auditory-induced phase-reset mechanisms. As far as I agree with such interpretation, I do believe there is more to speculate about. Specifically, there is no mention or remark commenting on the post-stimulus significant windows length (e.g. 0-180ms, 0280ms, 0-370ms) being somehow intertwined with the ISI duration. That is, the larger the ISIs, the longer the time window in which the IAF appears to significantly differ between conditions (F2B1 vs F2), depicting an underexplored scenario where auditory-triggered phase-reset mechanisms may only partially contribute to the alpha frequency decrease (i.e. cycle “elongation”), perhaps along with an additional role putatively played by flash-induced phase resetting dynamics.

      We thank the reviewer for this insightful observation. We agree that the progressively longer significant F2B1−F2 intervals should be reported descriptively rather than interpreted as evidence that the auditory–visual interaction itself lengthens with ISI. We now state that the temporal extent of a significant cluster depends on the magnitude and variability of the condition difference and on the statistical threshold.

      Because F2 and F2B1 contained identical visual sequences within each ISI, the F2B1−F2 contrast controls for the direct visual-sequence effect while retaining the beep contribution. The contrast therefore identifies the interval over which the two conditions are statistically distinguishable; how that interval relates to the duration of phase reorganization remains uncertain.

      We revised the Discussion accordingly and removed the mechanistic explanation that the significant window should lengthen because the later second flash interacts with the auditory perturbation.

      The relevant empirical results are reported in the Results and Figure 2—figure supplement 1A– C. The interpretation of the cluster durations has been revised in the Discussion, and the limitation concerning visual-stimulus-induced resetting is stated in the Discussion.

      (30) Lines 235–250 - The results hereby reported are quite straightforward, although I can't help but wonder whether we should witness the same patterns when comparing 1 vs 2 flashes report in explicit long and explicit short trials (perhaps via the counterbalancing approach mentioned at lines 803–805, to match the different number of trials per each report type).

      We thank the reviewer for this suggestion. We considered performing the corresponding one-flash versus two-flash report comparisons in the explicit short- and long-ISI trials. However, the non-predominant report was rare in these conditions and was entirely absent for some participants. Trial-number matching can control unequal group sizes when both report categories contain sufficient trials, but it cannot recover a report category that is absent. Moreover, matching the two report categories to the small number of non-predominant reports would discard most of the available trials and produce unstable participant-level neural estimates.

      Such an analysis would also require excluding participants who never produced the non-predominant report, leaving a selected subset of participants for whom the explicit trials were relatively ambiguous. The resulting comparison would therefore differ systematically from the full-sample, within-participant analysis used for the bistable trials.

      We consequently retained the report-specific IAF comparison for the individually titrated bistable trials, which were designed to provide sufficient numbers of both perceptual outcomes. The explicit short- and long-ISI trials instead serve as physical-ISI controls and are analyzed according to sensory condition and ISI. We believe that presenting an underpowered and selectively sampled report-specific analysis of the explicit trials would be less informative than clearly explaining why it was not performed.

      The role of the explicit trials as physical-ISI controls is described in the Results, and the trial number matching procedure for the primary bistable analyses is described in the Recording and preprocessing subsection.

      (31) Lines 260–261 - What kind of statistical correction has been implemented for the post-hoc tests?

      Thank you for requesting this clarification. The two condition-specific follow-up comparisons— one-flash versus two-flash reports within F2 and within F2B1—were treated as a single family and corrected using the Benjamini–Hochberg false-discovery-rate procedure at q = .05. Both comparisons were evaluated using two-tailed paired-samples t-tests.

      In F2, instantaneous alpha frequency was higher for two-flash than for one-flash reports (t<sub>(33)</sub> = 3.11, uncorrected p = .004, FDR-corrected p = .008). In F2B1, the corresponding comparison was not significant (t<sub>(33)</sub> = −0.49, uncorrected p = .630, FDR-corrected p = .630). We now report both the uncorrected and FDR-adjusted values in the Results and specify in the Figure 3 caption that the within-condition follow-up comparisons use FDR-adjusted two-tailed paired tests, whereas the interaction uses a repeated-measures ANOVA with an uncorrected p-value.

      The Results report both uncorrected and FDR-adjusted values, the general correction procedure is specified in the Statistical analyses subsection, and the Figure 3 caption distinguishes the repeated-measures ANOVA interaction from the FDR-adjusted two-tailed paired comparisons within conditions.

      (32) Line 265 - I believe a raincloud plot would be a better graphical option for Figure 3C.

      We thank the reviewer for this helpful suggestion. We agree that the revised panel should show the participant-level distribution rather than only a group summary. Figure 3C therefore displays every participant, the within-participant pairing, the median and interquartile range, the non-outlier range, and the mean. We retained this paired box-and-dot presentation rather than adding a kernel-density layer because the central comparison is within participant and the sample comprises 34 paired observations. The revised legend now describes each distributional element explicitly.

      (33) Line 283 - Phase-based measures are known to be more prone than other EEG metrics to temporal smearing. That is because computing the oscillatory phase at a given time-point via wavelet decomposition ends up collapsing into said time-point electrophysiological information gathered all along the kernel, which might be hundreds of milliseconds long at lower frequencies. This means that the oscillatory phase at a prestimulus time-point within the low-frequency range might also contain information relative to post-stimulus time-points (see Williams et al., 2024, Curr Bio). Have the authors addressed and/or factored in this issue?

      We thank the reviewer for raising the issue of temporal smearing in phase-based analyses. To address this concern, we repeated the complete phase-opposition analysis using one-cycle wavelets, which provide substantially improved temporal resolution. We additionally plotted the frequency-specific half-cycle boundary to identify estimates whose wavelet support could extend beyond stimulus onset (Figure 4—figure supplement 1).

      The one-cycle maps showed a similar prestimulus F2B1 alpha-band pattern without a comparable F2 pattern. This control reduces concern that the result was driven solely by wavelet support extending beyond stimulus onset. Because no cluster-level inference was applied to the one-cycle control, we use it as a descriptive temporal-smearing check rather than as an independent significance test.

      (34) Line 297–304 - Have the authors employed linear statistical tests or circular statistical tests (e.g., Watson-Williams, etc)?

      We thank the reviewer for requesting this clarification. Circular rather than linear statistics were used to analyse the phase-direction data. For each participant, the circular mean phase direction was calculated separately for one-flash and two-flash reports. The resulting distributions of participant-level mean directions were then compared using the Watson–Williams test. We have clarified the statistical details in the revised Results and Methods and in the Figure 4 legend.

      (35) Line 325 - Using circular statistics, rather than looking for quadratic effects via standard ANOVA, may turn out to be a better way to address the experimental question the authors are asking.

      We thank the reviewer for this important suggestion. We agree that circular statistics are appropriate when the inferential variable is the raw phase direction. Accordingly, as clarified in our to Comment 34, participant-level mean phase directions for one-flash and two-flash reports were compared using the Watson–Williams circular test.

      The quadratic contrast addresses a different aspect of the phase–percept relationship. After each participant’s phase profile was circularly aligned to their preferred phase, the dependent variable was the proportion of two-flash reports across bins of relative phase distance, rather than a set of raw angular observations. A Watson–Williams test is therefore not applicable to this aligned response-probability profile. The quadratic contrast was used to characterize whether the probability declined as phase moved away from the participant-specific preferred phase.

      Nevertheless, to ensure that the conclusion did not depend on either the alignment procedure or the assumed quadratic profile, we added a complementary non-aligned analysis. For each participant and sensory condition, we quantified the divergence of the complete phase-profile from uniformity using Kullback–Leibler divergence and standardized the result against a participant-specific response-label permutation distribution. Phase-dependent modulation was significant in F2B1 (permutation p = .009) but not in F2 (permutation p = .819), and modulation was significantly stronger in F2B1 than in F2 (paired permutation p = .014; Figure 4—figure supplement 3). We now state this alongside the POS permutation procedure in Statistical analyses: KL z scores were tested against zero with right-tailed sign-flip permutations within each condition, and the F2B1−F2 difference was tested with a two-tailed paired sign-flip permutation.

      Thus, the conclusion is supported both by circular analysis of the original phase directions and by a non-aligned permutation analysis that does not assume a common preferred phase or a quadratic profile. We have clarified the respective roles of these analyses in the revised manuscript.

      (36) Line 362 - Would it be possible for the authors to provide (perhaps as additional figures in the supplementary materials) each participant's psychometric curves resulting from the different tACS protocols and conditions?

      We thank the reviewer for this suggestion. Participant-level psychometric curves for all participants are provided in Figure 5—figure supplement 2 (F2) and 3 (F2B1), showing the observed and fitted responses under the 13 Hz, 8 Hz, and sham conditions.

      (37) Lines 377 - Issues raised at 31 apply to these post-hoc tests as well.

      We thank the reviewer for raising this point. The two planned condition-specific comparisons between 8 Hz and 13 Hz stimulation were treated as one family and corrected using the Benjamini– Hochberg FDR procedure at q = .05. Both uncorrected and corrected p values are now reported (F2: p = .023, FDR-corrected p = .045; F2B1: p = .578, FDR-corrected p = .578). Because the interaction difference scores were not normally distributed, we additionally confirmed the interaction using a Wilcoxon signed-rank test and a bootstrap confidence interval. We have clarified these procedures in the revised Results and Methods.

      (38) Lines 420–421 - Keeping in mind the results shown in Figure 2 (B, D, E) and remarks at 29, the choice of modelling the data without accounting for any flash-induced phase-reset mechanism might be the main limitation of the approach hereby implemented. I wonder whether it might be feasible for the authors to update the model accordingly, and simulate not only bistable trials, but also explicit short and long ones.

      We thank the reviewer for this important suggestion. We agree that a visual-stimulus-induced phase reset could contribute to the absolute oscillatory dynamics. Because the visual stimuli were identical in F2 and F2B1, the present model was designed to isolate the additional perturbation produced by the auditory input. This simplified account assumes that any shared visual reset contributes similarly to both conditions; possible non-additive interactions between visual- and auditory-induced resets are not captured and represent an important direction for extending the model.

      We also clarify that the model already simulated all eight ISIs from 30 to 100 ms, including the explicit short- and long-ISI trials, as shown by the simulated psychometric curves in Figure 8A. The report-dependent frequency and phase analyses were performed at the condition-specific fusion threshold because the explicit trials produced near-floor or near-ceiling distributions and therefore provided too few trials from both perceptual categories for stable within-condition comparisons.

      We have clarified these points in the revised Methods.

      (39) Lines 451 - For visualization purposes, it would be interesting to plot time-resolved simulated IAFs (from −600 to 600 ms), beside time-collapsed IAFs (Figure 7C).

      We thank the reviewer for this suggestion. We have added time-resolved simulated IAF traces from −600 to 600 ms for one- and two-flash percepts in both F2 and F2B1 (Figure 8—figure supplement 2). The traces show a transient decrease in simulated IAF around stimulus onset in F2B1, followed by recovery within approximately 200 ms, complementing the time-collapsed results.

      (40) Lines 457 - Based on what the authors mentioned, a POS analysis on synthetic data was performed. However, beside the permutation histogram (Figure 7D), nothing more about it from a quantitative standpoint has been reported. Plus, such analysis seems to have been run on data at stimulus onset (line 483), while POS significant differences uncovered in the empirical dataset are associated with a prestimulus (earlier) time window. This is a critical point suggesting how the model, although insightful, struggles in capturing some of the core patterns embedded within the empirical data. A possible way to shed some further light on the issue would be plotting the simulated time-resolved phase-based metrics (i.e., ITC, Supplementary Figure 7) from −600ms to 600ms, as a function not only of sensory modality (F2B1 vs F2), but also the number of flashes reported (1 vs 2). As long as some kind of difference emerges over the prestimulus time window between the 1 vs 2 flash reports relative to F2B1 trials only, it could be stated that the model simulates quite faithfully the predictive role of prestimulus alpha phase in audiovisual trials (i.e., as uncovered in the empirical dataset).

      We thank the reviewer for this important suggestion. To address this concern, we performed time-resolved phase-opposition analyses separately for F2B1 and F2 after balancing the numbers of one- and two-flash trials. We applied the same analysis pipeline and time–frequency parameters as in the empirical analysis, with 100,000 response-label permutations for the simulated POS analysis. The resulting time–frequency p-value maps are presented in Figure 8—figure supplement 5. The simulated F2B1–F2 POS difference at stimulus onset also exceeded the 97.5th percentile of the permutation distribution (Figure 8D).

      The time-resolved analysis showed report-dependent phase opposition around stimulus onset in both conditions, with a stronger effect in F2B1. Thus, the model captures the relative enhancement of phase-dependent perceptual modulation in F2B1. However, it does not reproduce the empirical finding of significant phase opposition only in F2B1 or its earlier prestimulus timing. We now state this limitation explicitly and describe the model as a qualitative account of condition-dependent phase sensitivity rather than an exact reproduction of the empirical temporal POS pattern.

      We have revised the simulated phase-analysis Results and Methods accordingly.

      (41) Line 622 - Concerning the interpretations of a reconciliation with Buergess and Noppeney, I disagree on the extent that while they might have found the same null findings as in this work concerning the relationship between IAF and fusion effect, this is not the case for the sound-induced flash illusion. Other factors may play a role, notably the number of participants employed, the details of the experimental design, and as more in detail described in the meta-analysis by Samaha and Romei 2024.

      We thank the reviewer for highlighting the limits of this comparison. We agree that our original use of “reconciles” was too strong. The distinction between fusion threshold and two-flash discrimination sensitivity may provide one explanation for the difference from Buergers and Noppeney (2022), but it cannot fully account for the divergent findings across audiovisual paradigms. Differences in sample size, stimulus and task design, psychometric measures, and IAF estimation may also contribute, as discussed by Samaha and Romei (2024). We have therefore revised the Discussion to present our model-based interpretation as one possible explanation specific to the present two-flash fusion paradigm.

      We have revised the Discussion accordingly.

      Reviewer #2 (Public review):

      Summary:

      The authors used a visual flash discrimination task in which two flashes are presented one after another with different inter-stimulus intervals. Participants either perceive one flash or two flashes. The authors show that the simultaneous presence of an auditory input extends the temporal window of integration, meaning that two flashes presented shortly after one another are more likely to be perceived as a single flash. Auditory inputs are accompanied by a reduction in alpha frequency over visual areas. Prestimulus alpha frequency predicts perceptual outcomes in the absence of auditory stimuli, whereas prestimulus alpha phase becomes the dominant predictor when auditory input is present. A computational model based on phase-resetting theory supports these findings. Additionally, a transcranial stimulation experiment confirms the causal role of alpha frequency in unimodal visual perception but not in cross-modal contexts.

      Strengths:

      The authors elegantly combined several approaches-from behavior to computational modeling and EEG-to provide a comprehensive overview of the mechanisms involved in visual integration in the presence or absence of auditory input. The methods used are state-of-the-art, and the authors attempted to address possible pitfalls.

      Weaknesses:

      The use of Bayesian statistics could further strengthen the paper, especially given that a few p-values are close to the significance threshold (lines 162 & 258), but they are interpreted differently in different cases (absence of effect vs. trend).

      Overall, these results provide new insights into the role of alpha oscillations in visual processing and offer an interesting perspective on the current debate regarding the roles of alpha phase and frequency in visual perception. More generally, they contribute to our understanding of the neural dynamics of multisensory integration.

      We thank Reviewer 2 for the constructive suggestions. The main revisions are summarized below:

      (1) We corrected the bistable-report calculation using the actual valid-trial counts, added Bayesian tests for the revised comparisons, and made the interpretation of non-significant results consistent.

      (2) We moved the ITC and power-control evidence into the main Results, added a focused power-by-phase control, and retained the RT analysis as a supplementary behavioural check.

      (3) We clarified trial exclusion, trial balancing, instantaneous-frequency estimation, and the use of the term characterize.

      (1) The use of Bayesian statistics could further strengthen the paper, especially given that a few p-values are close to the significance threshold (lines 162 & 258), but they are interpreted differently in different cases (absence of effect vs. trend).

      We thank the reviewer for this helpful suggestion. We agree that non-significant p values should not be interpreted inconsistently as either evidence for the absence of an effect or as a “trend.” To distinguish a lack of statistical significance from positive evidence favoring the null hypothesis, we have added Bayes factors to the key comparisons for which the absence of a difference is relevant to our interpretation.

      For the bistable percept proportions, the evidence modestly favored the null hypothesis (F2, BF<sub>01</sub> = 2.89; F2B1, BF<sub>01</sub> = 2.94); we therefore describe the report proportions as comparable rather than claiming definitive equivalence. The evidence favoring the null was stronger for the bistable reaction-time comparison (BF<sub>01</sub> = 3.60), the one- versus two-flash instantaneous-frequency comparison in F2B1 (BF<sub>01</sub> = 4.88), the instantaneous alpha-power comparisons (F2, BF<sub>01</sub>= 5.14; F2B1, BF<sub>01</sub> = 3.31), and the stimulation-frequency comparison in F2B1 (BF<sub>01</sub> = 5.05).

      Conversely, where the Bayes factor was insensitive—for example, the nonsignificant main effect of sensory condition on instantaneous alpha frequency (BF<sub>01</sub> = 0.83)—we report the result as inconclusive and interpret it as neither evidence for the null nor a statistical trend. We have revised the wording throughout the Results to apply this distinction consistently. Bayes factors were calculated using a default Cauchy prior (r = 0.707), with the directionality of the tests specified in the Statistical analyses subsection.

      We have revised the Results on bistable percept proportions and reaction times (Figure 1E and Figure 1—figure supplement 4), the perceptual-report analysis (Figure 3C), the instantaneous alpha-power control (Figure 3—figure supplement 2), and the tACS results (Figure 5). The Bayes-factor procedure has also been clarified in the Statistical analyses subsection.

      Reviewer #2 (Recommendations for the authors):

      (2) The authors did not find any significant effect of alpha power. Given that excitability is dependent on both power and phase, did the authors analyze the interaction between the two? This might offer an additional layer of explanation for the phase-related findings.

      We thank the reviewer for this important suggestion. Alpha power and phase are closely related but not redundant: power reflects how strongly the oscillation is expressed, whereas phase indicates the position of the cortex within its excitability cycle (Jensen and Mazaheri, 2010; Mathewson et al., 2011, 2009). Both have been linked to visual perception, raising the possibility that phase-dependent perceptual modulation may be more clearly expressed when ongoing alpha power is high (van Dijk et al., 2008; Williams et al., 2024).

      We therefore recomputed phase opposition separately for high- and low-power trial subsets, using a median split of posterior prestimulus alpha power within each participant, sensory condition, and perceptual-report category while maintaining balanced trial numbers. The Results now state concisely that the F2B1 alpha-band cluster was significant in the high-power subset (cluster p = .004, −420 to −20 ms, 5.96–16.79 Hz) but not in the low-power subset; neither F2 subset showed an alpha-band cluster, and the high-minus-low contrasts were non-significant (Figure 4—figure supplement 2).

      Importantly, the direct high-versus-low contrast was not significant in either condition (F2B1, p = .088; F2, p = .328). Thus, the presence of a significant cluster in the high-power subset but not in the low-power subset does not by itself establish a difference between power levels. Nevertheless, the concentration of the F2B1 phase-opposition effect in high-power trials is consistent with the pulsed-inhibition account, according to which phase-dependent modulation should be most detectable when the underlying oscillation is strongly expressed (Mathewson et al., 2011), and it echoes previous evidence that prestimulus alpha power and phase jointly shape visual perception (van Dijk et al., 2008; Williams et al., 2024). We therefore present this analysis as an exploratory control rather than evidence for a formal power × phase interaction.

      We have added this analysis to the Results (Figure 4—figure supplement 2), described the power stratification and permutation procedures in the Methods, and revised the corresponding theoretical interpretation in the Discussion.

      (3) Additionally, the analysis of reaction times might be of interest, as slower RTs could indicate increased ambiguity. This could reveal more about how alpha power (which has sometimes been related to RTs in attention tasks), phase, and frequency in the different conditions influence decision-making processes (see Samaha et al. 2020).

      We thank the reviewer for this helpful suggestion. We examined reaction times in the bistable trials, because these were the trials in which the perceptual outcome was maximally ambiguous and perceptual ambiguity was equated between F2 and F2B1 using condition-specific fusion thresholds. Reaction times did not differ between the two conditions (F2, 725.29 ± 19.19 ms; F2B1, 733.35 ± 19.39 ms; t<sub>(33)</sub> = −0.95, p = .350, BF<sub>01</sub> = 3.60; Wilcoxon signed-rank p = .174; Figure 1—figure supplement 4). Thus, there was no evidence for a systematic condition-level difference in decision time.

      We agree that the absence of a mean reaction-time difference does not exclude possible trial-level relationships between reaction time and alpha power, phase, or frequency. However, comprehensively testing these relationships would require multiple exploratory, trial-level models across several neural measures and temporal windows, without a pre-specified hypothesis regarding their direction. Such analyses would extend beyond the central question of the present study and would require a separate analysis framework with appropriate control for multiple comparisons. We therefore report the reaction-time comparison as a supplementary behavioural check and restrict our interpretation to the absence of a systematic condition-level difference in decision time.

      We have added the reaction-time results to the main Results and present the participant-level data in Figure 1—figure supplement 4.

      (4) The phase reset results, currently in the supplemental material, are crucial for understanding the proposed model. Moving them to the main text would provide a clearer narrative and strengthen the model presentation.

      We agree that this evidence is central to the model. The poststimulus ITC and alpha-power control, which provide the phase-reorganization evidence underlying the model, are presented in the main text as Figure 7.

      (5) Although the authors state that trials were balanced and some were excluded (lines 805, 829), the details of how this was done are unclear. It would be helpful to explain the criteria for trial exclusion and the exact balancing process.

      We thank the reviewer for requesting this clarification. Trials containing blinks, muscular activity, or other EEG artifacts were first corrected using independent component analysis. The data were then visually inspected, and trials containing residual artifacts or excessive noise were excluded.

      After artifact rejection, the primary bistable IAF and POS-map analyses used a common balanced trial set. Within each participant, the F2B1 one-flash, F2B1 two-flash, F2 one-flash, and F2 two-flash cells were randomly subsampled to the size of the smallest cell. This prevented unequal report frequencies or valid-trial counts from influencing comparisons across conditions and perceptual outcomes.

      The phase-bin and KL analyses retained all artifact-free bistable trials because they estimate each participant’s within-condition phase–report function rather than comparing cell means. Retaining all valid trials improves the precision of these response-proportion estimates, while the label permutation procedures preserve the original report counts.

      We have revised the Recording and preprocessing subsection, the aligned phase-bin analysis, and the non-aligned KL analysis.

      (6) Is the observed decrease in frequency compared to the baseline significant in the F2 condition, especially for long ISI trials? If it is the case, how do the authors interpret this result?

      We thank the reviewer for raising this point. Relative to the prestimulus baseline, instantaneous alpha frequency decreased reliably in F2 at the long ISI (Δ = −0.076 Hz, t<sub>(33)</sub> = −2.82, p = .004, FDR-corrected p = .012), but not in the short-ISI or bistable trials after correction. In F2B1, the decrease was reliable in the bistable trials (Figure 2C) and at both fixed ISIs (Figure 2—figure supplement 1C).

      The F2 long-ISI result indicates that the visual sequence itself can also produce transient alpha slowing, particularly when the two flashes are separated by a longer interval. The beep is therefore not the only possible source of poststimulus slowing. Because F2 and F2B1 contained identical visual sequences, the direct F2B1−F2 comparison isolates the additional auditory contribution. Thus, the F2 result complements rather than contradicts our interpretation: auditory input adds to a visually induced slowing and makes it more consistent across trial types.

      We have clarified this interpretation in the main Results, where the bistable baseline comparisons are reported with Figure 2C. The fixed-ISI baseline comparisons are detailed in the Supplementary Results and Figure 2—figure supplement 1C.

      (7) Line 799–801: The description of the filtering process (median filtered ten times with 10-time windows) is unclear to me. Could the authors rephrase or provide a visual explanation?

      We thank the reviewer for pointing out this ambiguity. The signal was not median-filtered ten times using a 10-ms window. At each time point, local medians were calculated separately within ten centred windows spanning widths from 10 to 400 ms, and the final estimate was the median of these ten window-specific values. This multiscale procedure reduces the high-frequency noise introduced by phase differentiation while limiting dependence on any single smoothing window. We have rephrased the Methods accordingly.

      We have revised the instantaneous-frequency analysis subsection of the Methods.

      (8) Line 87: Replace “confirm” with “characterize” to better reflect the exploratory nature of the study.

      We thank the reviewer for this suggestion. We agree that “characterised” more appropriately reflects the scope of the study. We have revised the Introduction.

      Reviewer #3 (Public review):

      Summary:

      The authors investigated the impact of an auditory stimulus on visual integration at the behavioral, electrophysiological, and mechanistic levels. Although the role of alpha brain oscillations on visual perception has been widely studied, how the brain dynamics in the visual cortices are influenced by a cross-modal stimulus remains ill-defined. The authors demonstrated that auditory stimulation systematically induced a drop in visual alpha frequency, increasing the time window for audio-visual integration, while in the unimodal condition, visual integration was modulated by small variations within the alpha frequency range. In addition, they only found a role of the phase of alpha brain oscillations on visual perception in the cross-modal condition. Based on the perceptual cycles' theory framework, the authors developed a model allowing them to describe their results according to a phase resetting induced by the auditory stimulation. These results showed that the influence of well-known brain dynamics on one modality can be disrupted by another modality. They provided insights into the importance of investigating cross-modal brain dynamics, and an interesting model that extends the perceptual cycle framework.

      Strengths:

      The results are supported by a combination of various, established experimental and analysis approaches (e.g., two-flash fusion task, psychometric curves, phase opposition), ensuring strong methodological bases and allowing direct comparisons with related findings in the literature.

      The model the authors proposed is an extension and an improvement of the perceptual cycle's framework. Interestingly, this model could then be tested in other experimental approaches.

      Weaknesses:

      There is an increasing number of studies in cognitive neuroscience showing the importance of considering inter-individual variability. The individual alpha frequency (IAF) varied from 8 to 13 Hz with a huge variability across participants, and studies have shown that the IAF influenced visual perception. Investigating inter-individual variations of the IAF in the reported results would be of great interest, especially for the model.

      Although the use of non-invasive brain stimulation to infer causality is a method of great interest, the use of tACS in the presented work is not optimal. Instead of inducing alpha brain oscillations in visual cortices, the use of tACS to activate the auditory cortex instead of the actual auditory stimulation would have presented more interest.

      We thank Reviewer 3 for the helpful comments. The main revisions are summarized below:

      (1) We specified how participant-level alpha peaks were extracted from the FFT spectra.

      (2) We clarified the rationale for the posterior tACS montage and the group-level scope of the model.

      (3) We clarified the operational relation between perceptual reports and responses, added the instantaneous-frequency equation, and specified the circular test used for the participant-level phase-angle analysis.

      (1) There is an increasing number of studies in cognitive neuroscience showing the importance of considering inter-individual variability. The individual alpha frequency (IAF) varied from 8 to 13 Hz with a huge variability across participants, and studies have shown that the IAF influenced visual perception. Investigating inter-individual variations of the IAF in the reported results would be of great interest, especially for the model.

      We thank the reviewer for this important suggestion. We now report how participant-level alpha peaks were extracted and show the individual estimates in Figure 2—figure supplement 2. Each participant’s alpha peak was defined as the frequency with maximal power within 8–13 Hz after averaging the trial-level spectra. The group mean was 10.12 ± 0.24 Hz (mean ± SEM), corresponding to a between-participant SD of approximately 1.40 Hz. The condition- and report-specific FFT comparisons were also performed at the participant level, thereby retaining individual variability.

      We agree that participant-specific model fitting would be valuable. However, the present model was designed as a group-level proof of principle, and its parameters were not fitted separately to individual participants. Individual fitting would require estimating participant-specific frequency and phase-reset parameters and therefore represents a substantial extension beyond the scope of the present model.

      We have revised the alpha-peak extraction procedure in the Methods, the corresponding Results, and Figure 2—figure supplement 2.

      (2) Although the use of non-invasive brain stimulation to infer causality is a method of great interest, the use of tACS in the presented work is not optimal. Instead of inducing alpha brain oscillations in visual cortices, the use of tACS to activate the auditory cortex instead of the actual auditory stimulation would have presented more interest.

      We thank the reviewer for this constructive suggestion. We agree that auditory-cortex stimulation would provide an informative complementary experiment. However, the posterior montage was chosen to address the central hypothesis of the present study: that alpha oscillations in the visual cortex determine the temporal window of visual integration. Posterior tACS therefore directly tests the causal role of the proposed oscillatory mechanism. Previous stimulation studies show that alpha-frequency stimulation can alter oscillatory activity and phase-dependent perception (Neuling et al., 2012) and that posterior alpha frequency predicts audiovisual temporal illusions (Cecere et al., 2015).

      In contrast, auditory-cortex stimulation would test whether engaging the auditory pathway is necessary for the effect of the beep, rather than directly testing the downstream visual-alpha mechanism. We therefore view the two approaches as complementary and have noted auditory-cortex stimulation as a valuable direction for future research.

      We have clarified this distinction in the Discussion.

      Reviewer #3 (Recommendations for the authors):

      (3) Lines 150–153: I did not understand how the authors disentangle the choice/from the perception per se. Clarification would be valuable.

      We thank the reviewer for this question. We did not attempt to recover a veridical percept independently of the participant’s response. Instead, the perceptual outcome was operationalized as the participant’s two-alternative report of perceiving one or two flashes, which is the standard psychophysical definition used in the present study. The relevant concern is therefore whether or decision biases could account for the reported condition effects.

      The counterbalanced mapping reduces systematic key or motor preferences, and the within-participant comparison uses identical requirements in F2 and F2B1. These controls argue against a simple bias that remains constant across sensory conditions. A constant criterion would not by itself explain the difference between F2 and F2B1 (Green and Swets, 1966). We therefore interpret the findings as consistent with an auditory influence on perceptual integration, while acknowledging that a condition-specific shift in criterion cannot be excluded (Knotts and Shams, 2016).

      We have revised the Results to clarify why the findings argue against a simple, condition-independent bias and have stated the remaining limitation in the Methods.

      (4) Instantaneous frequency computation: Could the authors provide the mathematical equation and the theoretical explanation, i.e., in which manner the temporal derivative of the phase indicates the instantaneous frequency?

      We thank the reviewer for requesting this clarification. Instantaneous frequency was calculated from the temporal derivative of the unwrapped Hilbert phase:

      where φφ<sub>uu</sub>(tt) is the unwrapped phase of the alpha-band signal. Phase is measured in radians, and its temporal derivative represents the instantaneous angular velocity in radians per second. Dividing by 2ππ converts angular velocity into cycles per second, or hertz (Boashash, 1992; Cohen, 2014). Thus, a lower instantaneous-frequency value indicates slower local phase progression rather than necessarily reflecting a sustained change in trait-like individual alpha frequency.

      We have added the equation and theoretical explanation to the instantaneous-frequency analysis subsection of the Methods.

      (5) I suggest replacing Figure 4 with Supplementary Figure 4, and only presenting in the text the results and statistics from Supplementary Figure 4.

      We thank the reviewer for this suggestion, and we take it to refer to Figure 3 (instantaneous alpha frequency and perceptual report); Supplementary Figure 4 of the original submission showed the same analysis after removal of the 1/f component, whereas Figure 4 presented the prestimulus phase results, which are addressed in Comment 6 below. We have repeated the 1/f-removal analysis in full and report it as Figure 3—figure supplement 1, with its statistics in the Supplementary Results, but we have retained the original analysis as the main figure. The 1/f-attenuated data do not eliminate the F2 frequency effect: in F2 the two-flash versus one-flash difference was, if anything, slightly larger after 1/f removal (0.079 Hz) than before (0.071 Hz), so the frequency effect cannot be attributed to the aperiodic component. What changed was the precision of the estimate, whose standard error approximately doubled (0.043 vs. 0.023 Hz), and the condition × percept interaction did not survive 1/f removal (F<sub>(1, 33)</sub> = 0.64, p = .430, versus p = .004 in the main analysis). This loss of precision is an expected property of the transform rather than of the data: the anti-1/f modulator divides, rather than subtracts, the log spectrum, so it compresses the alpha peak relative to its neighbours. A measure that flattens the very feature being quantified is therefore not, in our view, the appropriate primary analysis.

      We also provide a more direct test of the concern that motivates the suggestion: mean instantaneous alpha power did not differ between perceptual reports in either condition (F2, p = .727; F2B1, p = .308), so neither the aperiodic slope nor oscillatory amplitude offers an alternative account of the frequency effect. We therefore report the 1/f-removed analysis completely and transparently in the supplement, including the non-significant interaction, and discuss the discrepancy explicitly.

      (6) What are the statistical tests used in Figure 4B?

      We thank the reviewer for requesting this clarification. Figure 4B was analysed using circular statistics. For each participant, we calculated the circular mean phase direction separately for one-flash and two-flash reports at the illustrative maximum-effect point (−300 ms, 10.28 Hz, Oz). The participant-level mean directions were then compared using Watson–Williams tests (Berens, 2009). The preferred-phase directions differed significantly between perceptual reports in F2B1, F<sub>(1, 66)</sub> = 15.31, p < .001, but not in F2, F<sub>(1, 66)</sub> = 3.30, p = .074. We have now specified this statistical test in the Results, Methods, and Figure 4 legend.

      We have revised the Results section on the polar-angle analysis, the Methods section describing the phase analyses, and the Figure 4 legend.

    1. Author response:

      We thank the editors and the three reviewers for their careful and constructive reading. We are glad that all three reviewers regard the central empirical findings as valuable, and we are grateful for their insightful comments. In this provisional response, we address central concerns raised in the reviews and outline the plans for the revision.

      Reviewer #1 (Public review):

      Although this main argument is convincing, the study's framing of INs as the primitives for brain-level activity is not adequately justified. ICA aims to identify latent sources (here, INs) in the data, but taking these as representations of the data from which generative arguments can be made is not presently justified. Several prior works by Braga and colleagues have shown that resting-state networks can become more subject-specific and decouple when the single-subject data is sufficiently sampled (Braga et al., 2017, Neuron, among others). This raises a question about whether group-level INFs performing similarly to single-subject INFs may simply be due to the group-level INs that enter the single-subject DMD. Fully subject-specific analyses would be beneficial, but even in HCP it remains unclear whether the INs that could be identified are truly as subject-specific as some of the above-referenced works show they can be in principle.

      We thank the reviewer for this point. We would first like to clarify that our generative description concerns the flows rather than the INs: the framework specifies how observed brain activity and its diverse features underlying cognition (e.g., stable FC topology and diverse task activation) can arise from fixed spatiotemporal structures (flows) (as well as how this common structure is expressed differently across individuals). We do not propose INs as generative primitives of brain activity, although we do not exclude this possibility. Rather, in our framework, INs serve as spatial coordinates, i.e., dominant coherent spatial patterns that efficiently describe the large-scale dynamics, in terms of which these common coordination structures are estimated and described. We agree that defining flows in terms of INs may have suggested that INs are proposed as generative primitives. We will address this point more explicitly where INs are first introduced.

      Regarding subject-specific network organization, we would clarify that the subject-specific INF modes in the predictive comparison were estimated entirely within each subject: INs were identified by ICA applied to that subject’s data alone, and DMD (the dynamic coherence modeling step in our framework) was then performed on the resulting time courses. The comparison therefore does not reflect group-level INs imposed on single-subject DMD. We apologize for the lack of clarity and will make this procedure explicit in the manuscript. Group-level modes nonetheless predicted individuals’ BOLD signals better than these fully subject-specific modes. This result indicates that the coordination structure is stable enough to be shared across individuals, since group-level modes would otherwise reduce rather than improve prediction. This does not, of course, rule out individual-specific flow structure that may emerge with denser within-subject sampling, and we thank the reviewer for prompting us to make the procedure explicit and to discuss this point in the revised manuscript.

      Along a similar point, the AR(1) null-model analysis seems like a relatively weak null, and alternative comparison or null models could better justify the primacy of INs. For example, INs could be spatially randomized (the authors already do spatial randomization for their correlational statistics) and then used in DMD to identify modes with similar between-mode phase (θ) relationships. Or more generally, if the dimensionality reduction was in the form of parcels, as commonly is the case in connectomics, do similar DMD modes appear? The authors in the discussion position their findings in relationship to geometric modes and connectome harmonics, which in principle could also enter a DMD algorithm to identify analogous INF modes. The DMD algorithm is what creates the spatiotemporal modes, and the basis for defining y(t) to enter DMD has many possible choices. Additionally, at least one previous analysis did analyze spatiotemporal structure: they used the eigenmodes of a complex Laplacian with propagation delays corresponding to phases between brain regions, and they showed that these modes themselves relate to INs (Xie et al., 2021, NeuroImage). This appears much more generative than the present article. If the authors want to claim the ICA-based INs as the decisive generators, a competition between these alternative choices would decide that result and significantly strengthen the generality of the article's main argument.

      Following from our response above, we do not regard INs as decisive generators. Thus, the relevant point is whether the flow structure is robust to the choice of spatial basis (e.g., parcel). We addressed this in previous work (Song et al., 2025), in which DMD applied to parcel-level time series (Glasser cortical parcellation with the Cole-Anticevic partition for subcortical and cerebellar regions; 716 ROIs) yielded major modes highly similar to those reported here. Moreover, in that work, in addition to AR(1) null model, DMD outperformed both the linear model and the nonlinear manifold model that had shown the best performance in a recent systematic evaluation of macroscopic brain dynamics models (Nozari et al., 2024). Having established this previously, in this manuscript, we focus on the predictive comparison simple here, to examine how the flows relate to established features of functional organization and task-related dynamics. We now recognize that these previous comparisons are worth to briefly summarize in the revised manuscript.

      As the reviewer notes, geometric eigenmodes and connectome harmonics could also serve as inputs to DMD; they provide a spatial Fourier basis onto which time series can be projected. Because DMD is invariant to the choice of basis, we would expect the dominant INF modes to be recovered when a sufficient number of geometric eigenmodes or connectome harmonics are used. In the Discussion, our comparison with these approaches concerned the decompositions themselves, not excluding their use as alternative inputs to DMD.

      Finally, we thank the reviewer for pointing to Xie et al. (2021), whose complex-Laplacian eigenmodes provide a structurally derived counterpart to our data-driven flows, and we will discuss its relationship to the INF framework in the revised manuscript.

      Along this point, the authors spend considerable space in the article describing the correspondence to the principal functional gradients, yet the heart of their argument, as I understood it, is about the primacy of phase relationships in whole-brain dynamics. True, these INF modes now recontextualize the principal gradients in terms of phases, but the most convincing piece is the 23-task classification, which is relegated to the final panel of the final figure. Moreover, other convincing analyses, such as the heritability analysis and its relationship to INF amplitude, are not shown in the main text and instead placed in the supplemental figure. Related to the above comment about alternative bases to define DMD, could the relationship between principal functional gradients and the INF modes be a result of defining those very modes by INs which we already know correspond to principal gradients?

      We thank the reviewer for this helpful suggestion regarding the structure of the manuscript. We agree that the task classification and heritability analyses are important to our argument. Following the reviewer’s suggestion, we will restructure the Results to give these analyses greater emphasis, moving the heritability analysis to the main text, while condensing the description of the gradient correspondence.

      Regarding the last comment, the principal gradients are likely well represented in the subspace spanned by INs. However, which pattern within this subspace emerges as the principal mode (i.e., INF mode 1) is determined by the temporal dynamics rather than the INs themselves since the coherence modeling step (STEP 2; i.e., group-level DMD) weights the INs according to their coordinated temporal evolution. The correspondence is therefore unlikely to reflect mere spatial configuration of INs. Consistent with this, the principal mode obtained from our previous parcel-level DMD also aligned with the functional gradients (Song et al., 2025), indicating that the gradient correspondence mainly arises from the temporal dynamics.

      Reviewer #2 (Public review):

      Relation to prior work:

      The stability-flexibility problem and the role of relative phase are central to coordination dynamics and metastability theory (Tognoli & Kelso, Neuron 2014), and connectome models have shown that dynamic phase flows coexist with stable time-averaged FC (Roberts et al., Nat. Commun. 2019). The correspondence between FC gradients, networks, the global signal and a few propagating patterns was also established previously with complex PCA on HCP data (Bolt et al., Nat. Neurosci. 2022). Readers should view the gradient and network results as a replication with a different decomposition.

      We thank the reviewer for pointing us to this literature, which we should have engaged with and will incorporate in the revision. As the reviewer notes, our work is closely related to these studies, in particular, the phase-based perspective they established. We would like to clarify how the question we address relates to and is distinct from theirs. Coordination dynamics identifies relative phase as the key variable through which neural ensembles coordinate, emphasizing that coordination patterns form and dissolve continually (Tognoli & Kelso, 2014), and connectome-based modeling has shown that continually reconfiguring wave patterns coexist with a stable time-averaged FC (Roberts et al., 2019). These works concern the ongoing dynamics in coordination, and the latter one showed their relation to time-averaged structure.

      The duality we address is of a related but different kind: it concerns two time-averaged quantities, one of which is largely invariant across tasks (FC topology, i.e., inter-regional correlation) while the other varies substantially (task-evoked activation, i.e., the average response). This coexistence is a long-standing puzzle in neuroimaging, because the prevailing activation-based view identifies task-specific regions, which would in turn require task-specific interactions among them. Our framework addresses this through the phase dynamics of a fixed set of flows, offering a view complementary to this prevailing view underlying task-related analysis.

      In addition, phase here refers to the global phase of each flow, which sets the timing of the pattern as a whole, rather than to the relative phase between individual neural ensembles emphasized in coordination dynamics. As the reviewer’s comment indicates, however, the two are closely related if an INF mode is interpreted as a coordination pattern that recurrently forms across the brain. In the revised manuscript, we will situate our work in relation to coordination dynamics and metastability, state this distinction explicitly, and clarify the contribution of INF. We thank the reviewer for the opportunity to make this connection.

      Regarding Bolt et al. (2022), we agree that our gradient and network results converge with theirs and will state this more clearly in the revision. We see this convergence as reassuring, but in the context of our study, these results also play a further role. Beyond providing a parsimonious description of resting-state organization, the same fixed structure that carries these resting-state features also yields task-evoked activation patterns through phase modulation alone, which is how diverse task states can arise without disrupting intrinsic organization. The correspondence with resting-state features thus serves as the link between resting-state organization and task-evoked activity. We will make this role of the gradient and network results explicit in the revision.

      Mechanism:

      The framework is descriptive: task phases are estimated from data, not generated by a model. The work therefore does not show how phase alignments are selected or sustained, and claims that cognition "emerges from" phase dynamics should be read as compatibility rather than demonstration.

      We thank the reviewer for this point, and we agree with the distinction being drawn. We make no claim about what generates the flows themselves, or about what selects or sustains a particular phase alignment. Accordingly, “emerges from” should be read in a more limited sense: the features tied to task-related cognition, namely task-evoked activation patterns and the information that discriminates cognitive states, can be accounted for by a single generative principle, which is “phase modulation of a fixed set of flows.” We will define this usage explicitly in the Introduction and Discussion, and state that the mechanisms governing phase selection remain to be established.

      Baselines and null models:

      The reconstruction is not compared with the ceiling set by projecting maps onto the 27 networks, or with amplitude-only and random-phase reconstructions. The decoding compares feature sets of different sizes. The only dynamical null is AR(1), and the gain over it during tasks is small.

      We thank the reviewer for these suggestions, which we will adopt. For reconstruction, we agree that comparison with the ceiling set by the 27-network projection and random-phase reconstruction will clarify how much of the attainable and chance reconstruction accuracy is achieved by phase alone, and we will report it in the revision.

      For decoding, the aim of the analysis was to assess how much task information each representation carries, and the dimensionality of each feature set follows from the representation itself. Nonetheless, we agree that a comparison with amplitude at matched dimensionality would be more directly interpretable: we already observed that using only the cosine or only the sine components (13 features each) yielded substantially higher accuracy than amplitude, which we will report this in full in the revision.

      Regarding AR(1), we agree the margin during task is small, and we will present it with that caveat. Two points bear on its interpretation. First, this analysis was intended to test whether modes estimated from resting-state data retain predictive value during task performance, not to maximize the gain over a null. Second, the size of the margin is specific to the MDTB data, which were band-pass filtered at 0.008–0.15 Hz; under this filtering, lag-1 autocorrelation is high and AR(1) is already a strong baseline (R<sup>2</sup> = 0.828). The task-state gain, although small, was consistent across participants (R<sup>2</sup> = 0.832 versus 0.828, p = 1.4 × 10<sup>-6</sup>, N = 18, paired t-test). We will make this dependence on preprocessing explicit and will note that the central claims of the manuscript rest on the reconstruction and decoding analyses rather than on the size of this prediction margin.

      Internal consistency:

      FC is argued to be invariant because phases decorrelate over time, yet the task analysis assumes phases held in specific alignments within blocks. These assumptions need to be reconciled.

      We thank the reviewer for raising this point, which we agree deserves explicit clarification. The two assumptions are compatible once task activation is understood as a time-averaged quantity rather than a fixed spatial configuration. In our framework, the same intrinsic flows remain in place and continue to evolve during task performance. The “specific alignment” captured by a task activation map reflects a systematic bias in the phase distribution over the course of the task block, i.e., a tendency toward certain alignments rather than phases held fixed. As derived in Supplementary Result 3, the correlation structure is primarily determined by the fixed relative lags between regions and by the mode amplitudes. Thus, as long as the flows continue to evolve, the phase-dependent contributions to the correlation largely integrate out, and FC topology is preserved. We will clarify this distinction in the revised manuscript.

      (Possible) Physiological confounds:

      HCP data were analyzed without nuisance or global signal regression. The principal flow likely overlaps with the global, arousal-linked signal, whose apparent sequence partly reflects vascular transit delays. Recent work in mice shows that the leading propagating mode of infra-slow cortical activity, identified with the same DMD approach, can be reconstructed from pupil diameter alone, indicating that it largely reflects arousal dynamics (Raut et al., Nature 2025). This caveat extends to the heritability and cognition associations of flow amplitude, and to the interpretation of the flows as separate, cognitively specific processes.

      We thank the reviewer for this point. We note that the HCP data were denoised with ICA-FIX, although global signal regression was not applied. We agree that arousal and other physiological factors likely contribute to flow dynamics, and we view this as compatible with the framework rather than as a confound of its main argument. In the manuscript, we primarily consider that phase alignment reflects task-related cognitive input, but it does not exclude contributions from other physiological influences, such as arousal or respiratory signals. The central claim, that task states are characterized by phase modulation of a stable set of flows, holds regardless of the (additional) sources that drive this modulation. We also note that Raut et al. (2025) interpret arousal-related dynamics not as mere noise confounding the observation but as a process that actively organize/accompany with this large-scale spatiotemporal structure. We will discuss this point, including Raut et al. (2025), more thoroughly in the revised manuscript.

      Reviewer #3 (Public review):

      In the static-map reconstruction, changing a coefficient's phase changes the mixture of a mode's fixed real and imaginary spatial components; no temporal trajectory is reconstructed. Fixing amplitudes imposes a meaningful constraint, but successful reconstruction establishes representational capacity rather than temporal generation. I recommend comparisons with reconstructions retaining both task-derived amplitudes and phases, to quantify the information lost by fixing amplitudes, and with phase configurations exchanged between tasks, to distinguish task-specific reconstruction from recovery of shared spatial structure.

      We thank the reviewer for this precise characterization, which we accept. The reconstruction analysis was designed to test representational sufficiency, i.e., whether 13 phase values suffice to represent task activation maps, rather than to reconstruct temporal trajectories. We will state this scope more explicitly in the main text. We agree that quantifying the information lost by fixing amplitudes would be informative, and we will report this in the revision. We will also report reconstructions with phase configurations exchanged between tasks, which will help distinguish task-specific reconstruction from the mere recovery of shared spatial structure.

      Both reconstruction and classification should also be compared with alternative complex-valued bases spanning the same spatial subspace, with matched dimensionality and scaling. A clean comparison could use instantaneous spatial projection for both the original and alternative bases, with resting-state reference amplitudes recomputed for each basis. This would test whether the particular organization identified by DMD is advantageous, separately from the contribution of the temporally informed coefficient estimator.

      We thank the reviewer for this suggestion, which offers a direct way to isolate the contribution of the flow organization we identified. We will compare reconstruction and classification between the INF basis and alternative complex-valued bases spanning the same spatial subspace, with matched dimensionality and scaling. This comparison will more clearly demonstrate whether our INF modes confer an advantage beyond the representation itself.

      In classification, the phase time courses are mathematically equivalent to magnitude-normalized real and imaginary coefficients. Their advantage may therefore reflect a useful nonlinear transformation that reduces irrelevant magnitude variability, without uniquely implicating retiming. I recommend comparisons with unnormalized real and imaginary coefficients and with activation features normalized for instantaneous magnitude before GLM estimation, rather than simply standardized across time. Moreover, coefficient estimation incorporates three adjacent time points, whereas an analogous operation is not described for the activation baseline. This issue concerns the comparison with network activation, since INF phase and amplitude share the same estimator; its contribution should be assessed by comparing instantaneous and temporally informed estimates and matching temporal information across representations.

      We thank the reviewer for this insightful point. We agree that the effect of this nonlinear transformation should be tested to strengthen our argument. We will include this analysis in the revision. We also agree on the need to match temporal information across representations, which would further strengthen our point. We will compare classification performance between phase and network activation features under matched temporal information.

      Finally, an informative control would apply the pipeline to simulated data containing conventional task-evoked responses added to stationary, temporally correlated background activity, without task-dependent retiming. Simulations should approximately match the relevant spatial covariance, temporal structure, and signal-to-noise characteristics. This would test whether ordinary activation changes can produce a similar phase advantage. Task-locked phase trajectories should also be evaluated against this null model, since an additive response can itself change the phase of a complex coefficient without retiming the background activity.

      We thank the reviewer for this thoughtful suggestion. We would like to clarify that our claim is not that task responses are non-additive. As the reviewer rightly notes, an additive response can itself be described as a phase modulation. Rather, our claim is that phase modulation of a fixed set of resting-state flows is sufficient to describe how task-related features are generated. In light of this, we believe the most informative null (simulation) is one in which task states involve patterns not organized by the resting-state flows. This is directly tested by the comparison with alternative complex bases spanning the same subspace, which the reviewer helpfully suggests above.

      References

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      Bolt, T., Nomi, J. S., Bzdok, D., Salas, J. A., Chang, C., Thomas Yeo, B., Uddin, L. Q., & Keilholz, S. D. (2022). A parsimonious description of global functional brain organization in three spatiotemporal patterns. Nature neuroscience, 25(8), 1093-1103.

      Calhoun, V. D., Adali, T., Pearlson, G. D., & Pekar, J. J. (2001). A method for making group inferences from functional MRI data using independent component analysis. Human brain mapping, 14(3), 140-151.

      Erhardt, E. B., Rachakonda, S., Bedrick, E. J., Allen, E. A., Adali, T., & Calhoun, V. D. (2011). Comparison of multi‐subject ICA methods for analysis of fMRI data. Human brain mapping, 32(12), 2075-2095.

      Kutz, J. N., Brunton, S. L., Brunton, B. W., & Proctor, J. L. (2016). Dynamic mode decomposition: data-driven modeling of complex systems. SIAM.

      Nozari, E., Bertolero, M. A., Stiso, J., Caciagli, L., Cornblath, E. J., He, X., Mahadevan, A. S., Pappas, G. J., & Bassett, D. S. (2024). Macroscopic resting-state brain dynamics are best described by linear models. Nature biomedical engineering, 8(1), 68-84.

      Raut, R. V., Rosenthal, Z. P., Wang, X., Miao, H., Zhang, Z., Lee, J.-M., Raichle, M. E., Bauer, A. Q., Brunton, S. L., & Brunton, B. W. (2025). Arousal as a universal embedding for spatiotemporal brain dynamics. Nature, 647(8089), 454-461.

      Raut, R. V., Snyder, A. Z., Mitra, A., Yellin, D., Fujii, N., Malach, R., & Raichle, M. E. (2021). Global waves synchronize the brain’s functional systems with fluctuating arousal. Science advances, 7(30), eabf2709.

      Roberts, J. A., Gollo, L. L., Abeysuriya, R. G., Roberts, G., Mitchell, P. B., Woolrich, M. W., & Breakspear, M. (2019). Metastable brain waves. Nature communications, 10(1), 1056.

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      Tognoli, E., & Kelso, J. S. (2014). The metastable brain. Neuron, 81(1), 35-48.

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    1. Author response:

      The following is the authors’ response to the original reviews.

      Reviewer #1 (Public review):

      Summary:

      This computational study investigates the physical mechanisms underlying enhancer-promoter (E-P) interactions across genomic distances in Drosophila chromosomes, motivated by a previously published study that revealed unexpectedly frequent long-range contacts challenging classical polymer models. The authors performed coarse-grained polymer simulations testing three chromatin organization models: ideal polymers, loop extrusion, and compartmental segregation, comparing their predictions to experimental Hi-C contact maps, mean E-P distances, and two-locus mean-squared displacement dynamics. They found that compartmental segregation best captured both the structural and dynamic features observed experimentally, while neither ideal chains nor loop extrusion alone could reproduce all experimental observables. The combination of compartmental segregation with loop extrusion further improved agreement with experimental data, suggesting these mechanisms might be involved in Drosophila chromatin organization.

      Strengths:

      The paper has two primary strengths:

      (1) The simulations are based on biologically interpretable mechanisms (compartmentalization and loop extrusion), which may facilitate making specific experimentally testable predictions.

      (2) The work uses a systematic approach to increase model complexity by directly fitting to data, first establishing that simple models fail to capture the data until arriving at a more complex model that does capture the data.

      Weaknesses:

      I have two major concerns (detailed below) and multiple minor concerns.

      We thank the reviewer for the constructive assessment and for highlighting both the mechanistic value of the modeling framework and the systematic approach. We revised the manuscript substantially to address, to the best of our ability, the mentioned concerns (see below)

      Major concerns:

      (1) While the upside of the mechanistic simulations is that they are interpretable, the downside is that specific choices for the considered mechanism were made, and conclusions drawn from it are necessarily biased by the initial choices. In this paper, only two mechanisms were considered: loop extrusion and compartmentalization. Yet, it is not clear why these are the most likely underlying mechanisms that might determine the chromosome dynamics. Indeed, previous work (not cited in this paper) showed that Drosophila chromosome structure is not determined by loop extrusion: https://elifesciences.org/articles/94070.

      This should be acknowledged, and the main reasons for choosing these particular mechanisms should be laid out. The conclusions of the paper must then necessarily always be seen under the caveat that only these two mechanisms were considered.

      We now state more explicitly that our study focuses on two mechanistically interpretable classes of models, namely compartmental segregation and loop extrusion, because they are the two best-established and most tractable polymer-based mechanisms currently used to account for genome folding across species.

      We also now make the scope limitation explicit: additional mechanisms such as transient looping, transcription-mediated interactions, or other non-equilibrium effects are not modeled here, and our conclusions are therefore restricted to this physically grounded framework. This caveat is now stated clearly in the Discussion. We further acknowledge that the role of loop extrusion in Drosophila remains debated, and added the reference suggested by the reviewer.

      (2) Even within the framework of the approach, insufficient evidence is given to support the title of the paper "Criticality-driven enhancer-promoter dynamics in Drosophila chromosomes" for two reasons:

      (a) The fact that the best-fit parameters are near a coil-globule transition does not mean that the resulting dynamics are criticality-driven. To claim criticality, one would usually expect much more direct evidence, such as diverging correlation lengths. Furthermore, it would need to be shown that the key features of the dynamics (which should be defined, presumably the static and dynamic exponents) indeed depend on the parameters being at this transition. i.e., when tuning the simulations away from this parameter point, does the behaviour disappear? Only in this case can it be claimed that the behaviour is driven by this phenomenon.

      We agree that the proximity of the best-fit parameters to the coil–globule transition is not, by itself, sufficient to establish criticality in the strict statistical physics sense. In the revised manuscript, we therefore avoid presenting this as a formal proof of criticality and instead show that the experimentally relevant structural and dynamical features are optimized in a narrow regime close to the transition. We also discuss now in more detail how this transition can be associated with a near-critical behavior (see below).

      (b) The results section actually contains no mention of the coil-globule transition, and it is not clear in what way the parameters are close to this transition.

      We have now addressed this directly in the Results by adding a dedicated section, “Evidence for near-critical chromatin dynamics,” in which we explicitly relate the best-fit interaction strengths to the coil–globule crossover using independent observables, including conformational fluctuations and spectral signatures of polymer motion.

      Thus, three things are necessary:

      (i) How the parameters are close to the transition needs to be explained in detail.

      We now explain this in more detail in the revised Results section: the best-fit values of the interaction strength ε coincide with the coil-to-globule crossover seen in segment compaction (Fig. 3B), with minima in the fit metrics (Fig. 3C), and with a peak in conformational fluctuations together with spectral signatures characteristic of the transition (new Fig. 4A–C).

      (ii) The divergence of observed dynamics whenever the parameters are tuned away from the transition needs to be demonstrated.

      We show explicitly that agreement with the experimental observables deteriorates when ε is tuned away from the narrow range around the transition: both the structural and dynamical discrepancy metrics worsen outside this region (Fig. 3C), and the enhancement of homotypic encounter kinetics becomes less balanced across genomic distances away from the transition (new Fig. 4D).

      (iii) Even if 1 and 2 are fulfilled, a more careful title should be chosen, such as "Polymer simulations near the coil-globule transition are consistent with enhancer-promoter dynamics in Drosophila chromosomes."

      We thank the reviewer for this suggestion. We agree that the original manuscript did not provide sufficient evidence to support such a strong connection between the observed chromatin dynamics and the coil–globule transition. In response, we substantially expanded the analysis of the near-critical regime by adding a dedicated Results section, including measurements of conformational fluctuations, spectral signatures of polymer dynamics, and encounter kinetics as a function of interaction strength. These new analyses show that the agreement with experimental data is restricted to a narrow range of parameters near the coil–globule transition and deteriorates away from it. While we acknowledge that this does not constitute a formal proof of criticality in the strict statistical-physics sense, we believe that the revised manuscript now provides strong evidence that near-critical chromatin fluctuations facilitate long-range contacts. To reflect this more precisely, we have adopted the more cautious title: “Near-critical chromatin fluctuations facilitate long-range contacts in Drosophila chromosomes.”

      Many of the results in the figures and results section are rather repetitive and could be compressed. The main result of Figure 1 - that the data are not described by an ideal chain - was already fully shown and established in the original paper from which the data are taken. Figure 2 is a negative result with near-identical panels to Figure 3. Figure 4B is hard to interpret.

      We agree that some parts of the manuscript may appear repetitive, as the Results are organized as a progressive increase in model complexity. However, this stepwise structure was also viewed positively by the other reviewer, who appreciated the systematic comparison between models. In the revised manuscript, we therefore chose to preserve this progressive logic while improving readability by clarifying the section titles and restructuring the Results. This should make it easier for readers to follow the reasoning sequentially, while also allowing those who find some parts redundant to navigate more directly to the sections of greatest interest.

      The paper makes no concrete suggestions for new experiments to test the hypotheses formulated. Since the paper can only claim that the simulations are consistent with the data, it would significantly strengthen the paper if testable predictions could be made.

      In the revised version, we now include concrete, testable predictions in the Discussion. In particular, our model predicts that modest perturbations of compartmental interaction strength - for example, through changes in epigenetic state - should lead to measurable changes in chromatin dynamics and in the frequency of long-range interactions. In addition, our new analysis of first-encounter times shows that attractive compartmental interactions selectively accelerate homotypic encounters, especially near the coil–globule transition, providing a direct experimental signature that could be tested by perturbing compartmentalization and monitoring locus–locus encounter kinetics.

      Reviewer #1 (Recommendations for the authors):

      (1) The simulation code should be made available on GitHub.

      We have now deposited the code on GitHub with sufficient documentation and a sample of the best-fit trajectory for each simulated model.

      (2) Figure 4C looks very different from the experimental data; this should be commented on.

      In the revised manuscript, we refined the fitting procedure by fitting the P(s) curve rather than the Hi-C map directly and clarified this point explicitly in the Results. We now note that, although the simulated and experimental maps still differ in the strength of compartmentalization, the revised fit better captures the overall contact pattern. We also emphasize that in many previous studies simulated and experimental Hi-C maps are displayed using different color scales, which can make them appear more similar than they truly are; by contrast, we use the same color scale for both maps, providing a more stringent and transparent comparison.

      (3) "Since the contact threshold used to compute Hi-C maps from simulations is not precisely known and depends on experimental crosslinking conditions, we tested a reduced threshold of k = 4 s.u. (from k = 5 s.u.)."

      Why is this a reasonable thing to do? Is it just changing an assumption to fit the data better, since this threshold is not a fit parameter?

      In the revised manuscript, we use the fit from R(s) to estimate the scaling factor between simulated and experimental spatial distances and clarify that k is instead a forward-model parameter used to convert these distances into Hi-C-like contacts. Its exact value is not known a priori because it depends on experimental crosslinking and ligation conditions. Hence, we did not optimize k freely but tested the robustness of the results over a small and physically reasonable range of values (100-400 nm). As shown in Fig. S6A–C, varying k changes the sharpness of the simulated contact maps, but the best agreement is consistently obtained in a narrow range in the optimal ε.

      (4) Methods Equation 7: Why was the Spearman correlation coefficient used rather than Pearson, given that Spearman evaluates ranked data, rather than the correlation between raw data values?

      We agree that Pearson correlation is a better alternative when the goal is to compare absolute contact frequencies. In our case, we used Spearman correlation because we aimed to compare the relative organization and patterning of the observed-over-expected Hi-C maps in a way that is less sensitive to differences in overall amplitude between simulations and experiments.

      In the revised version, we show that both correlation metrics yield roughly similar results (Fig. S6B–C) and indicate the Pearson correlation when comparing the observed-over-expected Hi-C maps in the main text.

      Reviewer #2 (Public review):

      Summary:

      In this work, Ganesh and colleagues use experimental data from Hi-C and from live-cell imaging to evaluate different polymer models of 3D genome organization in Drosophila based on both structural and dynamic properties. The authors consider several leading hypotheses, which are examined sequentially in increasing level of complexity - from the minimal Rouse polymer, to a model combining sequence-specific compartmentalization and loop extrusion without extrusion blockers. They conclude that the combination of both compartmentalization and loop-extrusion gives the best agreement with the data. Their analysis also leads to concrete predictions about the processivity of cohesin loop extrusion in Drosophila, and a conclusion that the compartmental interaction strength is poised near criticality in the coil-globule phase space.

      Strengths:

      There is considerable interest in the field in understanding the mechanisms responsible for the 3D spatial organization genome and the dynamic movement of the genome, which has major implications for our understanding of long-range transcriptional regulation and other genome behaviors. The live-cell experimental work on which this study draws highlights the limitations of existing models to explain even the dynamic behaviors observed in the data, further exciting interest in further exploration. Therefore, this paper seeks to address an important gap in the field. The work is written in a well-organized, well-illustrated fashion. The text and figures are nicely integrated, easy to read, and explain challenging concepts with elegance and brevity in a manner that will be accessible to a broad audience.

      Weaknesses:

      The validity and utility of these conclusions are, in my view, substantially undermined by what appears to be unappreciated peculiarities of the live-cell data set that was used to constrain the model. The live-cell data comes from embryos were edited in a way that intentionally substantively changed both the 3D genome structure and dynamics specifically at the loci which are imaged, a case which is not at all explained by any of the models suggested nor acknowledged in the current work, nor compatible with the Hi-C data that simultaneously used to explain these models. As these ignored synthetic alterations have been previously shown to be determinative of transcriptional activity, the relevance of the author's work to transcriptional control (a prime motivation in the introduction) is unclear.

      The agreement in 3D organization, as represented in chromosome-scale contact frequency heatmaps, is substantially less impressive than the agreement seen in prior work with similar models. This discrepancy appears to be due in part to the unappreciated effects of the mentioned in the previous limitation, as well as inappropriate choices in metrics used to evaluate agreement. It is also not particularly surprising that combining more models, with more free parameters, results in an improvement in the quality of fit.

      Some major results, including both theoretical works and experimental ones, are ignored, despite their relevance to the stated objective of the work. The current manuscript and analysis could be improved substantially by a consideration of these works.

      We thank the reviewer for the careful and detailed assessment of the manuscript. We agree that the interpretation of the live-imaging dataset required clearer qualification, especially because the imaged loci are part of a synthetic system containing homie elements. In the revised manuscript, we explicitly acknowledge this limitation and provide a strategy (see further below) to mitigate its impact on the analysis.

      We also agree that increasing model complexity can naturally lead to improved agreement with the data. This point is now stated more explicitly in the revised manuscript. In particular, while the addition of loop extrusion improves the fit when combined with compartmental segregation, we emphasize that this does not constitute direct evidence for its biological relevance in Drosophila. Rather, our results are presented in a way that allows the reader to evaluate the contribution of each mechanism and draw their own conclusions regarding the role of loop extrusion in this system.

      I describe these issues in more detail below.

      Major issues:

      (1) The genetic element "homie" is present in a subset of the data: The experimental data used in this analysis come from different fly lines, half of which have been edited explicitly to alter genome structure and consequent transcriptional behavior, yet the authors are trying to fit with a common model - a problem which substantially undermines the utility of the analysis.

      Specifically, the authors evaluate the various models/simulations by comparing them to Hi-C from wild-type Drosophila embryos on the chromosome scale and 3D distances and dynamics from live-cell imaging in genetically edited embryos, to a series of models in turn. The exercise fatally overlooks a critical fact, (admittedly not easily noticed in the work from Bruckner et al), that the fly embryos used for nearly all their analyses contain not only fluorescent labels, but also contain two copies of a powerful genetic sequence, "homie", known for its ability to dramatically change the 3D organization and dynamics of the genome. Whether or not the fluorescent labels themselves used in the study further alter structure and dynamics is not entirely clear (and will require further work beyond the scope of either study), but at least these fluorescent labels aren't known to dramatically affect 3D structure and dynamics the way homie is. The critical problem is that adding or removing the "homie", as shown in a collection of prior works I describe below in more detail, dramatically affects structure, dynamics, and gene expression. Whether or not the genome contains two distal cis-linked copies of homie fundamentally changes genome structure and dynamics, so to use one dataset which has this edit (the live-cell data) and one dataset which lacks it (the Hi-C data) is, in some sense, to guarantee failure of any model to match all the data.

      If the authors had chosen instead to focus exclusively on the 'no homie' genetic lines in the Brukner data, they would have a much smaller dataset (just 2 distances), which would not cover all the length scales of interest, but it would at least be a dataset not known to be contradictory to the Hi-C. The two 'no homie' lines make much more plausible candidates for the sort of generalizable polymer dynamics these authors seek to explain, as will hopefully be made more clear by a brief review of what is known about homie. I next describe the published data that support these conclusions about how homie affects 3D genome spatial organization and dynamics:

      What is "homie" and how does it affect 3D genome distances, dynamics, and gene expression?

      The genetic element "homie" was named by James Jaynes' lab (Fujioka...Jaynes 2009) in reference to its remarkable "homing" ability - a fascinating and still poorly understood biological observation that some genetic sequences from Drosophila, when cloned on plasmids and reintegrated into the genome with p-elements, had a remarkable propensity to re-integrate near their endogenous sequence, (Hama et al., 1990; Kassis, 2002; Taillebourg and Dura, 1999; Bender and Hudson, 2000; Fujioka...Jaynes 2009). By contrast, most genetic elements tend to incorporate at random across the genome in such assays (with some bias for active chromatin).

      The Jaynes lab subsequently showed that flies carrying two copies of homie, one integrated in cis, ~140 kb distal from the endogenous element, formed preferential cis contacts with one another. Indeed, if a promoter and reporter gene were included at this distal integration site, the reporter gene would activate gene expression in the pattern normally seen by the gene, even-skipped. The endogenous copy of homie marks one border of ~16 kb mini-TAD which contains the even-skipped gene, (eve) and its developmental enhancers, so this functional interaction provides further evidence of physical proximity (as was also shown by 3C by Jaynes (Fujioka..., Schedl, Jaynes 2016), and later with elegant live imaging, by Jaynes and Gregor (Chen 2018)).

      Critically, if either copy of homie is deleted or substantially mutated, the 3D proximity is lost (Fujioka 2016, Chen 2018, Bruckner 2023), and the expression of the transgene is dramatically reduced (at 58 kb) or lost. Given the author's motivation of understanding "E-P" interactions, the fact that the increased 3D proximity provided by homie is as essential for transcription as the promoter itself at the ~150 kb distance, underscores that these are not negligible changes.

      These effects can be seen by plotting the data from Bruckner 2023, which includes data from labels with separations of 58 kb and ~150 kb "no homie" as well as homie. Unfortunately, the authors don't plot this data in the manuscript in the comparison of 3D distances, though the two-point MSD can be seen in Figure S13C, and laudably, the data is made public in a well-annotated repository on Zenodo, noted in the study. Note that the distance data in Figure S13 were filtered to exclude the transcriptionally off state, and are thus not the quantity the current authors are interested in. If they plot the published data for no homie, they will see the clear effect on the average 3D distance, R(s), and a somewhat stronger effect on the contact frequency P(s), which causes significant deviation from the trend-line followed by the homie-containing data.

      We thank the reviewer for this very insightful and well-documented discussion of the homie element and its impact on 3D genome organization and transcriptional activity. We agree that this is an important aspect of the experimental system that needs to be more explicitly acknowledged and addressed.

      In the revised manuscript, we therefore clarify both the synthetic nature of the imaged system and the potential impact of homie-mediated interactions. To mitigate this issue, we restricted our analysis to trajectory segments that exclude persistent encounter states corresponding to homie-dependent looping (the O<sub>off</sub> state from Brückner et al). By doing so, we effectively remove frames in which this locus-specific interaction dominates and focus instead on the baseline chromatin dynamics that occur in the absence of stable looping. In this sense, the filtered trajectories probe the intrinsic polymer dynamics of the system, independently of the engineered looping elements. Importantly, we verified this interpretation in our simulations by comparing conditions with and without stable loop formation: removing long-lived looped configurations recovers dynamics consistent with those of a polymer without persistent bridging interactions (see figure S7). This supports the idea that the filtered experimental trajectories provide a meaningful basis for comparison with our generic polymer models.

      (2) The agreement between the "best performing" simulations for all models and the Hi-C data is not on par with prior studies using similar approaches, apparently due to some erroneous choices in how the optimization is carried out. The 'best fit' simulation Hi-C looks strikingly different from the biological data in all comparisons, with clearly lower agreement than other authors have shown using highly similar methods (e.g., Shi and Thirumalai 2023; Di Pierro et al. 2017; Nuebler et al. 2018; Esposito et al. 2022; Conte et al. 2022), among many others. I believe this results from a few issues with how the current authors select and evaluate the data in their work:

      (a) Most works have used Pearson's correlation rather than Spearman's correlation when comparing simulation and Hi-C contact frequencies. Pearson's correlation is more appropriate when we expect the values to be linearly related, which they should be in this case, as they are constructed indeed to be measuring the same thing (contact frequency), just derived from two different methods. Spearman's correlation would have been justifiable for comparing how transcription output correlates with contact frequency. This may fix the bafflingly low correlations reported at lower adhesion values in Figure S2C.

      We agree that Pearson correlation is a reasonable alternative when comparing absolute contact frequencies. We had used the Spearman correlation because our aim was to compare the relative organization and patterning of observed-over-expected Hi-C maps in a way that is more robust to differences in dynamic range and normalization between simulations and experimental data. In the revised version, we compare the performance of the two metrics (Fig. S6) and show that they yield similar results, and now indicate the Pearson correlation whenever we compare Hi-C maps (observed-over-expected) in the text.

      (b) Choice of adhesion strengths - The Hi-C map comparison in Figure 3 strongly suggests that a much more striking visual agreement would have been achieved if much weaker (but still non-zero) homotypic monomer affinity had been selected. In the authors' simulation, the monomer state (A/B identity) strongly dominates polymer position, resulting in the visual appearance of an almost black-and-white checkerboard. The data, meanwhile, look like a weak checkerboard superimposed on the polymer.

      In the revised manuscript, we refined the fitting procedure to Hi-C data by taking the P(s) curve instead of the Hi-C map, which gives the same result as fitting with the Hi-C map and clarify this point in the results. We now note that, although the simulated and experimental maps still differ in the strength of compartmentalization, the revised fit better captures the overall contact pattern. We also emphasize that in many previous studies simulated and experimental Hi-C maps are displayed using different color scales, which can make them appear more similar than they truly are; by contrast, we use the same color scale for both maps, providing a more stringent and transparent comparison.

      (c) A further confounding problem is the aforementioned issue that the Hi-C data don't come from the edited cell lines, and that the interaction of the two Homie sites is vastly stronger than the compartment interactions of this region of the genome.

      This is precisely why, in the analysis, we restrict the live-cell trajectories to O<sub>off</sub> segments and clarify that our conclusions apply to the baseline polymer framework rather than fully to the engineered looping state.

      (3) Some important concepts from the field are ignored:

      The crumpled/fractal globule model is widely discussed in the literature (including the work containing the data used in this study) - its exclusion from this analysis thus appears as a substantial gap/oversight:

      A natural alternative to the much-discussed Rouse polymer model is the "crumpled polymer" (Grosberg et al. 1988; Grosberg 2016; Halverson et al. 2011; Halverson et al. 2011), also known as the "fractal globule" (Lieberman-Aiden et al. 2009; Mirny 2011; Dekker and Mirny 2016; Boettiger et al. 2016), much discussed for the way it captures the ⅓ scaling of R(s), found for much of the genome (or, equivalently, the -1 exponent of the probability of contact as a function of genome separation, P(s)). Given the 1/3rd scaling in the data, and the fact that the original authors highlighted the crumpled model in addition to the Rouse model, it seems that this comparison would be instructive and the lack of discussion an oversight. Moreover, while prior works (e.g., Buckner, Gregor, 2023) used some traditional simplifying assumptions to estimate the MSD and relaxation time scaling of this model, I believe a more rigorous analysis with explicit simulations (as in Figure 1 for the Rouse model) would be instructive for the crumpled polymer simulations. Note the crumpled globule is not necessarily the same as the globule in the coil-globule transition discussed here - it requires some assumptions about non-entanglement to stay trapped in the meta-stable state which has the 1/3rd R(s) scaling that is indicative of this model, and not the 1/2 exhibited by equilibrium globules (for s<< length of the polymer) and dilute polymers alike.

      While the fit in Figure 2 appears to get closer to the 1/3rd exponent (B= 0.32), this appears to be a largely coincidental allusion of agreement - the simulation data in truth shows a systematic deviation, returning to the 1/2 scaling for distances from 500 kb to whole chromosomes. This feature is not very evident as the authors restrict the analysis to only the few points available in the experimental data, though had they tested intervening distances, I expect they would show log-log P(s) is nonlinear (non-power-law) for distances less than the typical loop length up to a few fold larger than the loop length, and thereafter returns to the scaling provided by the 'base' polymer behavior. This appears to be Rouse-like in these authors' model, with R(s) going like 1/2, even though the data are closer to 1/3rd, as indeed most published simulated P(s) curves based on loop extrusion - e.g., (Fudenberg et al. 2016; Nuebler et al. 2018). In this vein, it would be instructive to the readers if the authors would include additional predictions from the simulation on the plot that lie at genomic separation distances not tested in the data, to better appreciate the predictions.

      We appreciate the reviewer's suggestion to consider the crumpled (fractal) globule model, which has played an important historical and conceptual role in discussions of chromosome folding. After careful consideration and preliminary tests, we chose not to include this model in the present study for several reasons.

      First, the objective of our work was not to provide an exhaustive comparison of all polymer descriptions, but rather to evaluate two mechanistically explicit frameworks, namely compartmental segregation and loop extrusion. In contrast, generating a fractal globule state in simulations typically requires imposing rapid, externally driven compaction protocols whose biological interpretation is less direct in the context of the mechanisms studied here.

      Second, as the reviewer notes, the scaling behavior associated with fractal globules is often discussed in terms of idealized power-law regimes. However, both experimental and simulated chromatin contact profiles generally display more complex behaviors across scales, making direct comparisons non-trivial. In addition, the original study from which the experimental data were derived already discussed this class of models and concluded that it could not account for the observed dynamical features.

      While we agree that including such a comparison could be of conceptual interest, we felt that it would substantially increase the scope and complexity of the manuscript without providing a commensurate gain in mechanistic understanding. For this reason, we chose to focus on compartmental segregation and loop extrusion, whose effects can be linked more directly to known biological processes. We now clarify this choice and its limitations more explicitly in the revised manuscript.

      Minor issues

      (1) I think it is too misleading to only describe the experimental data from Brukner as "E-P" interactions from Drosophila. It is important to note somewhere that this is not an endogenous interaction with a functional role in Drosophila - it is a synthetic interaction between enhancers in the vicinity of the eve gene and a synthetic promoter placed at a variable distance away. The uniformity is elegant - (it is the same pair of elements being studied at all distances), but also provides limited scope for generalization as suggested by the current text. Moreover, the enhancers were not directly labeled; rather, the 3D position of nascent RNA transcribed from eve was tracked with an RNA-binding protein and used as a proxy for the 3D position of the enhancers. There is not an individual enhancer at the eve locus that interacts with the transgene, but rather a collection of enhancers is distributed at different positions throughout the entire TAD, which contains eve, and must form separate loops to reach eve. Indeed, it was previously reported that differences in the local position of these enhancers, relative to eve, affect their ability to interact with the distal reporter gene and the endogenous eve gene (Chen 2018). There is also reported competition between these enhancers and the distal gene, which further complicates the analysis (especially since the state of eve and of its enhancers varies among the different cells as a function of stripe position) - see Chen 2018. All of this is ignored in the current work, despite the assertion of the application to understanding E-P interaction. A detailed discussion of these issues is not necessary, but I fear that ignoring them entirely is to invite further confusion and error.

      We agree that describing the Brückner dataset simply as enhancer–promoter interactions was an oversimplification. In the revised manuscript, we now refer to it consistently as a synthetic enhancer–promoter system and avoid presenting it as an endogenous wild-type enhancer–promoter interaction. We also explicitly note that the live-imaging measurements involve engineered loci containing additional regulatory elements, including homie, and therefore require appropriate caution in their interpretation. More generally, we agree that the system is more complex than a simple one-to-one enhancer–promoter interaction, as the tracked signal is linked to transcription at the eve locus and may reflect the contribution of multiple regulatory elements. Our objective was not to model all these locus-specific features, but rather to test whether generic polymer mechanisms can account for the baseline structural and dynamical properties captured by the measurements. We have revised the text accordingly to make the scope and limitations of our conclusions more explicit.

      (2) I believe this sentence is overstated, given available data: "TAD borders are characterized by transitions between epigenetic states rather than by preferentially-bound CTCF [4, 23, 24]." Indeed, this claim has been repeatedly made in the literature as cited here. However, other data clearly demonstrate a strong enrichment of CTCF at TAD borders (and at epigenetic borders, which in Drosophila have a high correspondence with TAD borders, as the authors have already appropriately noted). See, for example, Figure 4 of Sexton Cell 2012, and compare to Figure 2 of Dixon 2012. Of minor note, CTCF peaks co-occupied by the Zinc Finger TF CP190 are more likely to be TAD borders than CTCF alone. How big a species-specific difference this is remains unclear, as it appears some mammalian CTCF-marked TAD boundaries may be co-occupied by additional ZNFs. While plenty of Drosophila TAD boundaries indeed lack CTCF, many are marked by CTCF, this is enriched relative to what would be expected by chance (or relative to the alignment of other TFs, like Twist or Eve with TAD boundaries), and it has been shown that CTCF loss is sufficient to remove a subset of these, see for example Figure 5 of (Kaushal et al. 2021) (though it is possible, most will require mutation of the all the border-associated factors that collectively bind many of the borders, dCTCF, CP190, mod(mdg4) and others).

      We agree, so this now reads: “In flies, insulating regions are often enriched at TAD borders and can have locus-specific architectural roles. Many TAD borders also coincide with transitions in chromatin state, although a subset is associated with CTCF and other insulator protein. Together, these observations support the view that chromatin-state-dependent interactions make an important contribution to TAD formation in Drosophila.”

      (3) This assertion is overstated given available data: "Although TAD boundaries in Drosophila are often associated with insulator proteins [20], there is no direct evidence that these elements block LEFs in vivo. Therefore, we did not impose boundary constraints in our simulations; LEFs were allowed to move freely unless stalled by collisions with other LEFs, with the possibility of crossover.". Deletion of insulator in Drosophila that lie within a common epigenetic state leads to fusion of TADs (e.g., Mateo et al., 2019 - deletion of the CTCF-marked Fub insulator, in posterior tissues where both flanks of Fub are active; Kaushal, 2021, has examples as well). Loss of CTCF causes a small number of TADs to fuse as measured by Hi-C. This is far from 'direct evidence that insulators block LEFs' - as the authors have already noted, even the idea that cohesin extrudes loops in Drosophila in the first place is indeed controversial. However, LEF activity and stalling at insulators would provide a very natural explanation of why chromatin in a shared epigenetic state should form distinct TADs, and why these TADs should fuse upon insulator deletion. Justifying the lack of stalling sites based on empirical data is thus not very convincing to this reviewer. I believe it would be more apt to simply describe this as a simplifying assumption, rather than the above phrase, which may be misleading.

      Agreed, this now reads “Although TAD boundaries in Drosophila are often associated with insulator proteins, whether these elements act as barriers to loop-extruding factors in vivo remains unclear. In the absence of a well-established blocking rule for Drosophila, we did not impose boundary constraints in our simulations and instead treated freely moving LEFs, with possibility of crossover, as a simplifying assumption.”

      Reviewer #2 (Recommendations for the authors):

      Suggestions:

      (1) The conflict between the data sources should be resolved.

      (a) The live-cell 3D distance data could be converted into contact frequencies and used in place of the Hi-C in unedited cells.

      (b) The "no homie" data points, not currently used, could be used for comparison to Hi-C.

      We agree that the discrepancy between the wild-type Hi-C data and the live-cell imaging data from engineered lines needed to be addressed more explicitly. Rather than replacing one dataset with another, we chose an alternative strategy aimed at making the comparison more internally consistent. Specifically, we analyzed the live-cell data by taking only the O<sub>off</sub> state, which approximates “no homie” behavior by filtering out configurations associated with stable homie-dependent contacts. This allows us to focus our comparison on baseline chromatin dynamics in the absence of persistent locus-specific looping.

      Further, we performed simulations with and without homie-mediated looping and showed that this filtering substantially reduces the effect of stable homie-mediated contacts and recovers structural and dynamical properties that are much closer to those of the corresponding model without homie-mediated looping (new Fig. S7).

      We believe this provides a practical way to mitigate the conflict between the two data sources while retaining the broad range of genomic distances needed to constrain the models.

      (2) Any model that fits and claims to "explain" the live-cell imaging data using homie should also offer a hypothesis of how homie results in site-specific local changes to 3D genome structure and dynamics. The current models are elegantly general, suggesting the site-specific differences in epigenetic state that determine the compartmentalization/phase separation couple with global, sequence-agnostic effects of loop extrusion. However, such explanations completely fail to predict the experimental reality that adding or removing this special sequence changes structure, dynamics, and gene expression.

      We agree with the reviewer that our models do not provide a mechanistic explanation for the specific, locus-dependent effects of the homie element on chromatin structure, dynamics, and transcription. This was not the objective of the present study. Our goal was instead to test whether generic polymer mechanisms—compartmental segregation and loop extrusion—can account for the baseline structural and dynamical properties of the chromatin region. For this reason, in the revised manuscript we do not present the model as explaining the full behavior of the engineered homie-containing system. Instead, we explicitly restrict the comparison to trajectory segments prior to stable homie-dependent encounters, thereby focusing on chromatin dynamics in the absence of persistent locus-specific looping. We also clarify throughout the manuscript that the live-imaging measurements were obtained in a synthetic enhancer–promoter system and should be interpreted within that scope.

      (3) I recommend comparing the performance of Pearson's correlation vs. Spearman's correlation for evaluating agreement of the Hi-C data, and using weaker homotypic binding interactions so that these interactions do not overwhelm the distance-dependent decay seen in the data (and in the earlier simulations).

      We performed this comparison in the revised manuscript (Fig. S2B–C), which shows that both metrics when computed on the observed-over-expected maps yield roughly similar results. While weaker homotypic interactions show a distance-dependent decay in Hi-C maps, the best-fit to the experimental data still occurs at the value of ε=0.275 (regardless of whether the P(s) or Pearson correlation is used for the fit). Also, we emphasize that unlike in many previous studies, where simulated and experimental Hi-C maps are displayed using different color scales, we use the same ones, providing a more stringent and transparent comparison.

      (4) I recommend not describing the Brucker data simply as E-P interactions - this vast oversimplification will cause unnecessary confusion in addition to being technically inaccurate. It seems likely Brucker and Gregor have already confused the field enough (and perhaps also confused the current authors) by sometimes simplifying the description of this interaction between an endogenous RNA (which is linked to several surrounding enhancers, that appear at unmeasured/untracked distances away from the gene) and a distal synthetic DNA element as an investigation of E-P interactions. It is convincing that the distal transgenic promoter is responding to the several enhancers of the eve locus, but this is not an interaction that happens in wild-type animals nor is it a simple 1-1 to interaction, nor is it mediated by the enhancer or promoter (it is instead dependent on two additional elements, the two copies of homie, one of which is >15 kb distal from some of the enhancers in question, a relatively long distance for the fly genome).

      We agree with the reviewer that describing the Brückner dataset simply as “enhancer–promoter interactions” was too reductive. In the revised manuscript, we now refer to it consistently as a synthetic enhancer–promoter system, and we explicitly state that the live-imaging measurements were obtained in genetically modified embryos containing additional regulatory elements, including homie. We also restrict the analysis to trajectory segments prior to stable homie-dependent encounters, so that the comparison focuses on baseline chromatin dynamics rather than on engineered, persistent looping states.

      That said, we agree that this system is more complex than a simple endogenous one-to-one enhancer–promoter interaction. We have therefore revised the text to make the scope of our conclusions more explicit and to avoid overgeneralizing these results to endogenous enhancer–promoter interactions in wild-type animals.

      (5) It would be instructive to show the distribution of R(s) from the model and compare that to the data. A key advantage of the experimental data used here, of Hi-C, and of simulations over Hi-C, is the access to the full distribution of distances. The experimental data R(s) gets a bit flatter than 1/3rd past 500 Mb, possibly reflecting the homie-loop, which, due to the long lifetime of the proximal state, has dramatically decreased the average R(s) to something much less than expected for any other pair of DNA sequences ~3 Mb apart. Note that the distribution of R(s) in all the experimental data is bimodal (the original 2018 work at 140 kb separation plots this in the main figures (Chen et al. 2018), but an analysis of the raw data shows a similar signature for larger distances). This is not believed to be a feature of compartmentalization / phase-separation, as the prior FISH on unedited do not exhibit such bimodal behavior in Drosophila (e.g., Mateo et al. 2019; Cardozo Gizzi et al. 2019). I believe this will reveal further qualitative differences between the experimental live cell data and some of the models proposed.

      We thank the reviewer for this suggestion. We compared the scaled distribution of R(s) from the experimental O<sub>off</sub> state with that of the (A) Rouse model, (B) best-fit of R(s) to the loop extrusion model, (C) best-fit to R(s) from the compartment-based block copolymer model, and the (D) best-fit to R(s) in the model combining the block copolymer and loop extrusion (see Author response image 1). For each model and genomic distance, we compute the Wasserstein distance W between the two distributions. Although the fits between the simulated and experimental distributions is not perfect, W shows a significant overall reduction — a similar trend to that of the mean R(s) — for the compartment-based models. We chose not to add this figure in the manuscript, opting instead to keep the mean R(s).

      Author response image 1.

    1. Author response:

      We sincerely thank the reviewers for their feedback. In the revised manuscript, we will expand our discussion on the significance of microglia redistribution, particularly as it pertains to retinal inflammation and degeneration. Microglia play a key role in retina development, maintenance and protection and their distribution across the layers of the retina is important [1,2,3]. Most notably, changes in microglia location can alter their interactions with the neuronal, glial and vascular cells associated with different retinal layers, potentially affecting functional processes such as synaptic maintenance [4,5].

      This link makes microglia redistribution relevant to basic research into how the retina maintains homeostasis and responds to inflammation. We acknowledge that results obtained from parameterization of the model to rat and rhesus macaque pharmacokinetics rely on a few assumptions recognized by both ourselves and the reviewers. Most notably, these assumptions include that microglia migration parameters and cellular sensitivity to LPS are transferable across species. To our knowledge, comparable time-resolved measurements of layer-specific microglia densities following systemic LPS challenge are unavailable for rats and macaques, making this a necessary assumption that we will elaborate further on in the revision. We hope that our results might motivate such experiments, enabling further confirmation of our modeling approach and predictions.

      We also agree that the contribution of LPS pharmacokinetics must be interpreted in relation to the model’s structure and accompanying parameter uncertainty. In the revision, we will investigate the following.

      - Compare candidate models fitted to the figure 3 data to test whether direct LPS effects confined to the outer plexiform layer, with density-dependent migration in the other layers, can reproduce the observed trajectories.

      - Assess how rat and rhesus macaque predictions change when mouse microglial migration rates are scaled allometrically by body mass.

      - Test a model in which migration from the ganglion cell and nerve fiber layers (GCL/NFL) to the inner plexiform layer (IPL) depends on circulating LPS.

      - Examine how peak blood LPS concentration (Cmax) and cumulative exposure over a finite time window affect the predicted maximum and minimum microglial densities in the outer and inner plexiform layers.

      - Use the model to generate synthetic datasets and test which types and amounts of data improve our ability to estimate the microglial migration rates.

      We remain mindful that the available data render some migration parameters difficult to identify. In light of this, we will offer an improved discussion on the trade-offs between reproducing the observed trajectories, model complexity and parameter identifiability. Finally, we will clarify the uncertainty quantification methods, more clearly report sample sizes and the meaning of plotted summary statistics, and discuss the ideal data that could help constrain the model.

      (1) Silverman, Sean M., and Wai T. Wong. "Microglia in the retina: roles in development, maturity, and disease." Annual review of vision science 4.1 (2018): 45-77.

      (2) Singaravelu, Janani, et al. "Microglia in the primate macula: specializations in microglial distribution and morphology with retinal position and with aging." Brain Structure and Function 222.6 (2017): 2759-2771.

      (3) Chen, Ling, Peizeng Yang, and Aize Kijlstra. "Distribution, markers, and functions of retinal microglia." Ocular immunology and inflammation 10.1 (2002): 27-39.

      (4) Mills, Samuel A., et al. "Fractalkine-induced microglial vasoregulation occurs within the retina and is altered early in diabetic retinopathy." Proceedings of the National Academy of Sciences 118.51 (2021): e2112561118.

      (5) Wang, Xu, et al. "Requirement for Microglia for the Maintenance of Synaptic Function and Integrity in the Mature Retina." Journal of Neuroscience 36.9 (2016): 2827–2842.

    1. Author response:

      We thank the Editors and the Reviewers for their evaluation of our work and constructive feedback. We appreciate the recognition of the importance of our study, the strength of our dataset, and its contribution to understanding the electrophysiological organisation of the mediodorsal thalamus (MD). The main concerns raised by the Reviewers include the influence of behavioural and experimental events on examined physiological metrics, the uncertainty of anatomical localisation of MD neurons, and the statistical framework employed. We think these concerns can be addressed through both a clarification of our approach and through additional analyses, and we would like to provisionally outline how we plan to address them in a revised manuscript.

      First, we will more thoroughly untangle the influence of various behavioural events on the electrophysiological differences across MD subdivisions. We will describe more clearly how we calculated the physiological metrics used throughout the manuscript. Furthermore, we will extend our current analyses to examine in more detail how physiological characteristics throughout MD subdivisions are influenced by task-related events and animal engagement.

      Second, we will more extensively describe our anatomical localisation approach and past and current considerations for neuron assignment. We will extend our considerations for both the lateral, medial and ventral borders of the MD in general as well as its parcellation into subdivisions. We will provide additional data to support our claim of accurate localisation of neurons, as well as data to suggest minimal effects of contamination of non-MD thalamus neurons in MDl and MDm.

      Lastly, we will strengthen the statistical framework of our study. We will implement mixed-effects models to account for the hierarchical structure of our dataset and provide a more rigorous statistical foundation of the findings.

      Overall, we believe the recommendations and planned revisions will address the concerns raised by the Reviewers and strengthen the interpretation of our findings. We thank the Reviewers for their constructive comments and look forward to incorporating their suggestions into the revised version of our manuscript.

    1. Author Response:

      We would first like to thank the reviewers for recognizing the general interest and value of our study. The core shared concerns were around validation of the translocations and the target-containing vs distant translocation frequency. We agree that is an area of particular interest, particularly given the higher target-containing translocation rate observed by other groups using methods specialized for detecting such events. To help better compare the target-containing translocations and validate at least some of the distant translocation events, we intend to perform direct DNA sequencing using the nanopore platform following hybridization capture with probes around both the target sites as well as some of the fragile off-target sites on bulk samples. This should allow direct measurement of translocations involving each of these site classes to be performed with reasonable depth, ensuring adequate power to detect these rare events while keeping detection amplification-free, ensuring that it will not introduce PCR bias. Mechanistically we will also determine whether there are putative off-target recognition sites for the guides in observed translocation regions to determine whether off-target cutting might be involved in the observed distant translocation sites.

      The other main experiment set which will be performed will be single cell copy number analysis in cells with longer term functional tracking. This will address whether the observed CNVs can induce a competitive advantage under physiologically relevant conditions, whether they’re neutral (still present but not over-represented vs any other clone), or whether they ultimately disappear from the population. Results from this additional experimental set will help to answer whether the genomic aberrations which result from editing are generally a cause for concern, or whether most are benign.

      Outside of these experiments, we will be adding additional details and clarifications around statistics and their relative power. Additional discussion/text modifications will be added addressing other specific comments.

    1. Author response:

      Reviewer #1 (Public Review):

      The retina adapts to statistics of the scenes it views, and in particular can adapt to million-fold changes in light intensity. The adaptation alters how the population of retinal ganglion cells encodes the scenes, and it is unclear how downstream circuits could handle different types of changes in scene encoding. This careful study investigates how a population of six different retinal ganglion cells changes their encoding response properties as a function of mean luminance level. It does this by mapping receptive fields and response nonlinearities over a million-fold change in light intensity, from the scotopic to photopic regime.

      This paper has several strengths. (1) It is clearly written and lays out clearly the alternative hypotheses it examines. (2) Its experiments are carefully done and rigorously analyzed. (3) It finds interesting results, pointing especially to two cell types that seem to stand out for their different responses to increasing light levels in these experiments. It also finds less spatial and temporal integration at low light levels than theory predicts (or than others have found).

      This paper has relatively minor weaknesses. (1) It does not particularly resolve why its results are different from prior, similar experiments, though it carefully discusses and highlights those differences. (2) The functional implications of these results, and especially the two cell types that stand out from the crowd, are not discussed with much depth. This likely reflects an issue beyond this paper: that the functions of different RGC types for visual processing in the brain remain poorly understood, which in turn makes it difficult to understand functional implications of these results.

      We thank the reviewer for their clear summary.

      Reviewer #2 (Public Review):

      This paper describes careful work on the effects of light adaptation on the spatio-temporal receptive fields of retinal ganglion cells assessed using an ex vivo preparation on a multielectrode array. The results are analyzed systematically and clearly but do not provide a clear insight into this important aspect of retinal function, in part because of doubts about how they might extrapolate to the situation in vivo.

      We thank the reviewer for their clear summary.

      Strengths

      - A potentially interesting question: Do changes in average luminance alter spatio-temporal receptive fields of different types of retinal ganglion cell (RGC) in different ways? Or are different types of RGC affected in similar ways and to similar extents? Previous work going back decades has investigated the effects of luminance adaptation in a piece-meal way but this study makes a more systematic comparison across six types of RGC.

      - Experiments and analyses have been carried to a very good level.

      - Thorough description of the results with clear figures.

      - A scholarly presentation that includes important literature.

      We thank the reviewer for their assessment.

      Weaknesses

      - Some of the effects observed in the six types of RGC, such as shortening of integration times at higher luminance, have been recognized for some time (as is clearly discussed).

      We agree, most of the general effects we observe have been observed in prior literature. However, the literature is also conflicted on most of the effects we observe. For example, whether or not the surround disappears at low light levels has been argued in prior literature. Similarly, the extent to which temporal receptive fields switch from differentiating to integrating (biphasic to monophasic) across light levels also has conflicting evidence in prior literature. Thus, we think our experiments add some clarity to this by presenting a unified set of stimuli to six simultaneously measured cell types.

      - The most novel finding is probably that one of the six types of RGC, the ON brisk-sustained, exhibited a proportionately larger change in integration time than other types, but this has not been placed in a functional context. The impact of the paper in terms of understanding retinal processing is unclear.

      We agree, the observation would be stronger if placed in a functional or behavioral context and we would love to do this! We are currently developing methods for inactivating particular RGC types and measuring the impact on behavior, but as the reviewer can appreciate, this is challenging. We hope in future studies to make intracellular measurements in these different RGC types to understand how some of these changes are reflected in (or produced by) their synaptic inputs.

      - A major drawback of all work on an MEA, usually ignored by users of this technique, is that diffusible neuromodulators are removed by perfusion. Neuromodulators can profoundly adjust processing through the retina and their levels can change in response to changes in luminance. The retinal network on an MEA is therefore likely to be far from its normal state. It is hard to know how far the ability of a retina on MEA to adapt reflects adaptation in vivo.

      100% agree! This is a very important point, and we have added some discussion on this topic as a critical caveat (lines 551-557). We have been performing experiments in mice with agonists and antagonists of D1 and/or D2 receptors to see if we can manipulate particular aspects of adaptation across different RGC types. So far, we have struggled to see much of an effect on spatial or temporal receptive field properties across light levels. The effects we do see are mostly limited to spike latencies and the gain of the contrast response functions, but these are quite subtle effects in our experiments thus far. That said, we think this is very likely an issue of not yet landing on the right drug concentrations, stimulus conditions, and possibly not waiting long enough for the effects of the neuromodulators to take full effect. Understanding how neuromodulators impact retinal adaptation is certainly important and a downside of our ex vivo experiments is that they may remove some of that from the equation. Nevertheless, we think this is a caveat that can and should be addressed in the discussion, not a fatal flaw of the experimental design.

      - An important control, reversing the direction of the luminance change, has not been carried out. If stepping back from a higher light level to a lower level does not (at least partially) reverse the changes caused by an increase in luminance, it may be that the lack of a pigment epithelium is affecting the results more severely than estimated by calculation.

      We also agree with this. We raised the light level because we are not doing our measurements with the pigment epithelium (PE) attached. If we start at high light levels and work backwards, the retina minimally sensitizes to the lower light levels, especially when switching from cone to rod-mediated conditions. We are measuring RGC responses without the PE because we cannot isolate the retina and PE from the sclera in rat (or mouse). Measuring RGC responses with the sclera attached presents problems with flattening the retina against the electrode array and presents a major diffusion barrier for oxygen to reach the retina. This is a limitation of the approach, however, as stated in the Discussion, we think that our measurements at 0.1-10 R*/rod/s and 10,000 R*/rod/s (low scotopic and low photopic respectively) are minimally subjected to pigment bleaching and thus are likely to accurately reflect in vivo steady-state conditions. The core result, that adaptation is largely ‘proportional’ still holds even if results at the light levels which are subject to photopigment bleaching are removed from the study.

      Reviewer #3 (Public Review):

      There have been variable reports on the degree to which light adaptation can modify a retinal ganglion cell's receptive field properties. The classic description suggested that the receptive field would become more low-pass in both space and time in dim light, better to integrate when signals are weak. More recent studies, particularly Tikidji-Hamburyan et al. (2015), suggested more radical changes in receptive fields across light levels, raising questions about how downstream circuits could keep track of highly variable output of the same ganglion cell, depending on the mean luminance.

      The current study revisits this problem with a straightforward set of experiments: measuring spikes in rat retinal ganglion cells, using a multi-electrode array, and presenting either spatiotemporal white noise or drifting gratings while varying the mean intensity over a one-million fold range. The technical achievement of this work is the careful and quantitative characterization of receptive field properties of specific cell types and the careful tracking of individual cells across light levels using each cell's electrophysiological image.

      The current study doesn't exactly agree with either of the extreme views from the literature. That is, the six ganglion cell types studied here mostly adapted in a similar way - becoming tuned to higher temporal and spatial frequencies in bright light. However, the receptive field did not become extremely low-pass at the dimmest light level, and there were exceptions to how individual cell types adapted, with some types showing a unique pattern, e.g., the ON brisk-sustained cell shows a particularly large shift in the peak temporal frequency in bright light. It's not exactly clear what to make of these unique patterns, which were rare, and it suggests that downstream circuits must somehow be attuned to these patterns or at least there is some benefit to these patterns that we do not currently understand.

      The study offers many technical strengths and is written clearly. If there is a weakness, it is that the new analysis does not clarify some of the discrepancies from previous studies, which had used various species, cell types and light levels that do not completely overlap with the current study. Still, if future studies followed the standard set in the current one, the field would certainly benefit.

      We thank the reviewer for their clear summary.

    1. Author response:

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      This study investigates how behavioral, morphological, and mechanosensory traits contribute to the ability of Drosophila species to use firm, intact fruits as oviposition substrates. By comparing oviposition behavior across ten species, the authors confirmed D. suzukii and identified D. immigrans as two species that can overcome the mechanical barrier imposed by firm fruit surfaces despite belonging to distinct species groups and possessing markedly different ovipositor morphologies. The study further uses the genetic toolkit of D. melanogaster to identify iav as an important regulator of stiffness-dependent oviposition inhibition and examines functional differences among iav orthologs from D. melanogaster, D. suzukii, and D. immigrans. Finally, laboratory offspring-development assays and a field survey are used to relate these behavioral and mechanistic differences to fruit use in an ecological context.

      Strengths:

      A major strength of this study is its broad comparative framework. The authors examine oviposition behavior across ten Drosophila species and identify two distinct morphological strategies associated with the ability to use firm, intact fruits: the robust, serrated ovipositor of D. suzukii, which has been previously well-documented, and the elongated, needle-like ovipositor of D. immigrans, which was less studied. This provides an interesting example of distinct evolutionary solutions for overcoming a similar mechanical barrier.

      The functional genetic analysis in D. melanogaster is a strength. The identification of iav as a regulator of stiffness-dependent oviposition inhibition, together with loss-of-function, rescue, and neuronal-silencing experiments, provides a useful mechanistic link between mechanosensation and oviposition behavior. In particular, the cross-species rescue experiments using D. suzukii and D. immigrans iav orthologs in a common D. melanogaster mutant background provide an informative approach for testing functional differences among the orthologs while controlling for much of the broader species-specific genetic background.

      The study also makes a valuable effort to connect controlled laboratory observations to ecological patterns. The inclusion of offspring-development assays and field-collected substrates extends the study beyond laboratory oviposition assays and provides an interesting ecological context for the observed differences in fruit use.

      Weaknesses:

      It is inaccurate to characterize D. suzukii as a niche specialist. It is highly polyphagous, with hundreds of recorded hosts, and Figures 1, 2, and 6 indicate the most expanded, not narrowed, niche among the species examined. The only supporting result, in Figure S1, is aversion to rotten strawberry puree, which may have other explanations, such as bacterial effects. Without further evidence, the claim is unsupported.

      More broadly, "niche" should be defined more carefully. The experiments and results support differences in oviposition or breeding niche breadth but may not necessarily capture the broader ecological niche. Adult feeding-site preference, for example, represents another component of resource use and may not necessarily coincide with oviposition-site preference.

      We thank the reviewer and agree that niche specialist requires a more precise definition. Our original intention was to distinguish specialization in host-plant species from differences in the stage of fruit development used for oviposition. Fruit ripening represents an ecological resource axis of oviposition site selection rather than a narrow ecological niche. Furthermore, aversion to rotten fruit may reflect microbial effects rather than standalone evidence of specialization. In the revised manuscript, we will: (1) explicitly define our scope as oviposition and breeding niche breadth; (2) reframe D. suzukii as exhibiting an oviposition preference shift along the ripening axis rather than general specialization; (3) calibrate broad niche terminology throughout the text.

      The proposed distinction between relatively flexible chemical sensory tuning and a strict, non-substitutable mechanical barrier may also be more nuanced than currently presented.

      Interestingly, the iav results themselves show that loss of a single mechanosensory gene not only substantially reduces oviposition inhibition on stiff substrates but also enables puncture oviposition in D. melanogaster without a corresponding change in ovipositor morphology. Although specialized morphology likely improves penetration, this result shows that a simple genetic change can strongly alter the sensory or behavioral component of the mechanical barrier. This result somewhat complicates a strict distinction between flexible chemical tuning and mechanical constraint.

      We thank the reviewer for this comment and agree that the distinction between chemical and mechanical constraints warrants a more nuanced presentation. As the reviewer points out, loss of inactive (iav) in D. melanogaster not only abolishes egg-laying aversion on stiff agarose, but permits puncture oviposition on intact fruit without morphological changes (Figure 4C–D). This proves that the physical barrier is actively gated by the mechanosensory nervous system. However, morphology remains critical for efficiency: iav mutants exhibit a modest puncture frequency (18–35%) compared to ~100% in D. suzukii (Figure 4C vs. 3B). Thus, sensory gating and morphological machinery operate in tandem. In the revised manuscript, we will clarify this distinction, preserving the ecological concept of non-substitutable mechanical constraints and further write discussion about this.

      The relationship between puncture oviposition and offspring success should be interpreted cautiously. Puncture oviposition likely facilitates access to fresh fruit, but species-specific larval traits may also affect development. Puncture-induced decay could facilitate later use by other saprophagous species while giving puncture-capable species an early advantage. Thus, the association does not establish puncture behavior as the primary determinant of larval success.

      We thank the reviewer for this point. While puncturing intact fruit skin facilitates physical entry and accelerates localized tissue softening, successful development to adulthood also depends on species-specific larval traits and temporal changes in fruit condition. Furthermore, as noted, puncture-induced decay can eventually open the substrate to secondary saprophagous species, indicating that puncture behavior primarily provides a temporal priority advantage on fresh fruit rather than serving as the sole driver of larval survival. In the revised manuscript, we will avoid framing puncture oviposition as the determinant of offspring success. We will revise the results and discussion part to present it as a mechanism that facilitates early access to intact fruit resources, and acknowledge how species-specific larval performance, successional decay dynamics, and interactions with subsequent colonizers jointly shape developmental outcomes.

      The field survey supports the use of firm-surfaced fruits by D. suzukii and D. immigrans, but some ecological conclusions are stronger than the data support. Because local species composition and abundance are not reported, it is unclear whether their high recovery reflects preferential use of firm fruits or local abundance. The field observations are valuable, but the conclusion that mechanical capability directly produces niche partitioning in the wild requires more cautious interpretation.

      We thank the reviewer for raising this point and agree that local species abundance is an important factor when interpreting field collection patterns. A high recovery of D. suzukii and D. immigrans from firm-surfaced fruits could reflect their overall local abundance rather than preferential use of these substrates. In addition, adult emergence records alone cannot establish that mechanical ability directly produces niche partitioning in the wild. To address this, we will present additional data on overall fly abundance and species composition to the revised field survey results. Comparing each species' total abundance with its recovery across fruits of different surface firmness will help assess whether the observed patterns reflect differences in local population size or align with distinct substrate use. We will also moderate our ecological conclusions to state that the field observations are consistent with our laboratory findings.

      Reviewer #2 (Public review):

      Summary:

      This paper investigates how physical perception and morphology are integrated to determine what kinds of substrates different species of insects, here flies, prefer for laying their eggs. These questions have far-ranging implications, in particular because the authors include Drosophila suzukii, a lineage of Drosophila that has made the transition from rotting to fresh fruit and therefore functions as a significant agricultural pest. Through careful experimentation, the authors show that individual components of oviposition behavior, including chemosensory and physical perception of substrate stiffness, vary across ten species, creating unique responses in each. By integrating functional and fitness experiments, the authors provide evidence linking these differences to morphology, genetics, and the neural basis of behavior.

      Strengths:

      A significant strength of the paper is the elegant simplicity of the experiments. Even though many of these species have been studied for decades in the laboratory, there is still much to learn from straightforward observations of their behavior under different conditions. The authors show that there are species-specific responses to the physical perception of stiffness (something often overlooked in studies of oviposition preference), that these responses are associated with fruit ripeness, but that they can be successfully separated from chemosensory signals in the laboratory. They further show that the morphology of the egg-laying machinery, in particular the ovipositor, has implications for the success of these preferences, as it allows some species to successfully pierce the skin of ripe fruits, with the result that larvae are able to feed and develop into adult flies. Finally, they show that differences in behavior in response to stiffness are in part associated with apparent differences in the function of key genes (e.g., iav). When iav sequences from D. immigrans or D. suzukii are expressed in D. melanogaster, they do not fully rescue the stiffness-dependent oviposition phenotype.

      Weaknesses:

      The weaknesses of the paper are largely in the interpretation of these results. Cross-species studies such as these, especially in Drosophila, face challenges in interpreting the evolutionary and ecological basis of observed behaviors. This is in part because we often consider these species in isolation from their natural environments and phylogenetic context. The authors attempt to tackle this problem by examining adult emergence from substrates collected in the wild, and their results are broadly consistent with what is suggested by the laboratory assays.

      However, some of the most interesting and complex aspects of their results remain insufficiently explored. For example, across their assays of physical and chemical preferences for oviposition, they find that:

      (1) D. suzukii has a clear preference for ripe fruit and reduced avoidance of stiff substrates, representing a substantial shift in niche use.

      (2) D. immigrans is capable of using ripe fruit as a substrate but shows nearly no preference between ripe and rotten fruit or between stiff and soft substrates.

      (3) D. biarmipes shows a preference for ripe-fruit chemical cues and will lay eggs on ripe fruits, despite a strong aversion to stiff agarose substrates.

      (4) D. mercatorum will likewise lay eggs on ripe fruits and stiff substrates, predominantly on the surface, but has a clear preference for other options.

      (5) D. quadrilineata, like D. immigrans, has the ovipositor morphology required to successfully lay eggs in ripe and stiff substrates but shows a strong preference for rotten fruit and soft substrates.

      A major result communicated through these experiments is therefore that multiple inputs must be integrated to determine oviposition behavior, and that each species appears to weigh these inputs differently. The diversity of these responses is itself one of the most interesting findings of the study, but the authors' focus on a binary interpretation of niche specialization obscures this variation rather than embracing it.

      We thank the reviewer for these thoughtful comments and detailed suggestions. We agree that the behavioral strategies exhibited by these five species are much more varied than a simple binary framework of niche specialization versus expansion can capture. As the reviewer noted, the distinct patterns across D. suzukii, D. immigrans, D. biarmipes, D. mercatorum, and D. quadrilineata highlight an important distinction between the capacity to use a resource and the behavioral preference for it. Having the morphological ability to pierce firm skin does not necessarily translate into a preference for ripe fruit, just as attraction to favorable chemical cues does not always overcome mechanical barriers. Instead, each species integrates and weighs these sensory and physical inputs differently during egg-laying decisions. In the revised manuscript, we will avoid categorizing species simply as specialists or generalists based on single assays. We will reorganize the Discussion around the integration of chemical cues, mechanosensory responses, and ovipositor morphology, emphasizing how their different weightings lead to diverse strategies for accessing and using breeding substrates.

      The field ecology data provide useful evidence of natural host associations, but the reported sampling information limits their interpretation. Without information on sampling effort, host availability, and fruit ripeness and damage at collection, it is difficult to establish differences in niche breadth or exclusion from particular hosts. Adult emergence also does not reveal whether females laid eggs through intact skin or used previously damaged or decaying fruit. These results are therefore consistent with the laboratory observations, but do not establish that mechanical access determines ecological partitioning or reduces competition in the wild.

      We thank the reviewer for noting that our field survey provides useful evidence of natural host associations, and we agree with the limitations raised regarding our sampling information. In the revised manuscript, we will moderate our conclusions to reflect these limits. We will state that our field data demonstrate natural host associations and successful development in the sampled substrates, rather than direct evidence of puncture oviposition or mechanically driven niche partitioning. We will also note in the Discussion that testing whether mechanical traits partition niches or reduce competition in the wild will require future studies.

      More generally, it is difficult in studies comparing species that have been maintained for generations under laboratory conditions to interpret variation in behaviors observed in the laboratory. We expect differences across species because they have distinct genomes, ecologies, and evolutionary histories. Moreover, some species may have spent many more generations under laboratory conditions than others, and standard laboratory conditions were largely designed around some species (particularly D. melanogaster) rather than others. This makes it difficult to establish the extent to which differences in oviposition reflect biologically meaningful differences in preference that might allow them to function within a specific niche. For example, it may not be helpful to compare absolute oviposition rates under the same experimental conditions given that species differ in the number of ovarioles in their ovaries, rates of oogenesis, metabolism, and other aspects of reproductive biology. Within-species choice assays partly account for differences in egg production, although relative preferences may still depend on multiple aspects of reproductive biology and the options provided. Even so, it is valuable to see how these species behave under the same experimental conditions, if only to establish a comparative baseline.

      We thank the reviewer for raising this point and agree that laboratory rearing history and species-specific reproductive physiology are important considerations in comparative behavioral studies. Drosophilid species differ in ovariole number, oogenesis rate, metabolism, and adaptation to lab culture, and standard laboratory conditions do not represent optimal environments for every species. We recognize that these baseline differences can affect absolute egg-laying rates and potentially influence behavioral responses. For this reason, we avoid using absolute egg counts to define reproductive capacity across species. Even so, testing all species under standardized conditions provides a useful comparative baseline for how they respond to identical chemical and mechanical cues, and within-species choice assays help assess relative egg allocation while partly accounting for differences in overall egg production. At the same time, we understand that relative preferences remain context-dependent and can be influenced by the specific options offered, physiological state, and mating experience. In the revised manuscript, we will explicitly discuss these methodological limitations and avoid equating laboratory egg-laying rates directly with reproductive performance or ecological preference in nature.

      One direction in which this work could point in the future is toward investigating the ecology of these flies under the conditions in which their traits were likely to have evolved. These traits presumably arose in ecosystems where competition and interactions with other species were important components of fitness, yet under laboratory conditions these factors are largely removed and therefore invisible. Some of the summary statements in the manuscript also reflect a tendency to interpret species in terms of niche specialization versus niche expansion ("generalism"), when in reality these species are responding to multiple stimuli, and their observed behavior reflects only one component of their potential niche use. Placing the diversity of behavioral responses documented here into a broader ecological and evolutionary context would therefore strengthen the interpretation of an already valuable comparative dataset.

      We thank the reviewer for this thoughtful perspective. In nature, the suitability of a breeding substrate depends not only on its physical and chemical properties, but also on its accessibility, nutrient content, microbial communities, and prior occupancy by conspecifics or other species. We also recognize that laboratory behavior reflects one component of how flies integrate multiple stimuli, and that mechanical access alone does not determine ecological differentiation. While the ability to puncture intact fruit skin provides an early opportunity to use fresh resources before saprophagous species colonize, whether this translates into reproductive success also depends on larval performance, resource competition, and the timing of fruit decay. Subsequent softening and decay after puncturing can open the substrate to later colonizers, further shaping final reproductive outcomes. In the revised manuscript, we will moderate summary statements that frame species strictly in terms of niche specialization versus expansion. Instead, we will expand the Discussion to place our findings within this broader ecological and evolutionary context, treating mechanical access as one component of breeding resource use and noting the importance of future studies examining oviposition behavior, competition, and offspring fitness under more natural conditions.

      Reviewer #3 (Public review):

      Summary:

      This study examines how mechanosensory and morphological adaptations allow Drosophila species to overcome the mechanical barrier of intact ripe fruit and expand their ecological niches. The authors combine comparative behavior, morphology, genetics, and field surveys, and identify the mechanosensory channel IAV as a contributor to species differences in stiffness-dependent oviposition. The findings have broad implications for evolutionary ecology and agriculture. The data are compelling, and the evidence supporting the major conclusions is strong.

      Strengths:

      The morphological and behavioral comparisons across ten species and different food substrates are exceptionally comprehensive and provide a rich phylogenetic context. The experimental design is careful and rigorous; for example, the authors first measured the biologically relevant range of fruit stiffness and then used corresponding agarose concentrations to test stiffness-dependent oviposition. The screening of candidate mechanosensory receptors is comprehensive, and the iav loss-of-function and cross-species rescue experiments provide particularly strong evidence for functional divergence in mechanosensation. In addition to all these strengths, I was also impressed by the tour-de-force field survey. Demonstrating ecological relevance can be challenging and is frequently missing from mechanistic studies of behavioral evolution. Here, the field data directly connect laboratory phenotypes with natural resource use and substantially strengthen the ecological significance of the study.

      Weaknesses:

      I do not identify any major limitations, but the manuscript would benefit from a few methodological clarifications. The exact nature of the iav transgenic constructs should be clarified, as this affects the interpretation of the molecular mechanisms (e.g., coding versus non-coding). In addition, the field study would benefit from more complete documentation of the sampling sites and sample sizes.

      We appreciate the reviewer’s suggestions, which will help improve the methodological clarity and reproducibility of our study. Regarding the iav transgenic constructs, we clarify that the constructs used in this study contain the coding sequence (CDS) of iav, rather than its non-coding regions. We will provide a clearer description of the construct design and the relevant molecular details in the revised manuscript to facilitate interpretation of the underlying molecular mechanisms.

      We also agree that more complete documentation of the field survey would improve the transparency and reproducibility of the study. We will therefore provide more detailed information on the sampling locations and sample sizes, including the relevant details in the Methods section and supplementary materials.

    1. Author response:

      The following is the authors’ response to the original reviews

      Reviewer 1 (Public Review):

      Major Concerns (highest priority):

      (1) There is a lack of detail about the methodology in the results section/figure legends, which makes it difficult to interpret the data. Sometimes, adequate information is also not included in the methods themselves. For example, Figure 1A: how many doses did each mouse receive? How long after dosing were animals sacrificed? Figures 1E and 2A: is this RNA-seq analysis?

      We thank the reviewer for this helpful suggestion. We have revised the figure legends throughout the manuscript to include the requested methodological details, including the dosing regimen, number of doses administered, interval between the final dose and tissue collection, and clarification that the gene expression analyses shown in Figures 1E and 2A were derived from RNA-sequencing. We focused our revisions on the figure legends to improve clarity and facilitate interpretation of the data.

      Figure legend additions:

      - Figure 1A: Page 35, line 828-829 added: Mice were treated by daily oral gavage for 4 days and sacrificed 4 hours after the final dose.

      - Figure 1E: Page 35, line 833-835 added: Gene expression differences were derived from RNA-sequencing analysis of vehicle-treated xenografts.

      - Figure 2A: Page 37, line 883- 886 added: Gene expression differences were derived from RNA-sequencing analysis of vehicle-treated xenografts. For the vehicle- and osimertinibtreated groups, mice received daily oral gavage for 7 days and were sacrificed 4 hours after the final dose.

      - Figure 3: Page 39, line 931-932 added: Mice were treated by daily oral gavage for 7 days and sacrificed 4 hours after the final dose.

      - Figure 4: Page 41, line 978-979 added: Mice were treated by daily oral gavage for 7 days and sacrificed 4 hours after the final dose.

      - Figure 5A: Page 43, line 1021 – 1022 added: by daily oral gavage for 4 days and sacrificed 4 hours after the final dose.

      - Figure 5B: Page 43, line 1028- 1029 added: Mice were treated by daily oral gavage for 38 days and sacrificed 4 hours after the final dose.

      Using a second EGFR inhibitor for some of the key experiments would increase the rigor of the studies shown.

      Thank you for this suggestion. We agree that a second EGFR inhibitor may increase the scientific rigor of the findings. However, at the time the experiments were completed, osimertinib was the clear standard-of-care first-line therapy for EGFR-mutant lung cancer, and the clinical relevance of using other inhibitors in these experiments is unclear.

      (2) Nice to have experiments:

      Using CRISPR KO of CDK4 in the CDK4-amplified HCC827 and testing response to Osi and presence of replication stress would also increase the rigor of the studies.

      Thank you for this suggestion. We agree that this would increase the rigor of the studies, but these experiments are currently beyond the scope of this manuscript.

      The authors show that in their patient data, some cell cycle regulators which are amplified in NSCLC at similar rates to CDK4/6, such as CCNE1, had no increase in FGA. Overexpressing CCNE1 and testing Osi response in their cell models would be a nice test of their proposed mechanism that it is the genomic instability and FGA that are driving resistance. This wouldn't need to be done in vivo, but could be done using cell culture-based methods.

      Thank you for this suggestion. For this manuscript, we have chosen to focus on the role of CDK4 and CDK6 in osimertinib resistance, as they have shown the clearest correlation with decreased responsiveness to EGFR TKI treatment in other studies. We agree that assessing the role of CCNE1 in osimertinib resistance is important and will address this in future studies.

      Similarly, testing the overexpression of some of the proposed target genes, such as STEAP1 and AGR2, on the therapeutic response to Osi in cell culture would also be a nice test of the mechanism proposed.

      Thank you for this suggestion. We agree that these experiments are important, but they are currently beyond the scope of this study.

      Reviewer #1 (Recommendations for the authors):

      Minor Concerns (text/figure display):

      (1) Use of "biochemical analysis" is used to mean immunoblot in the text and legends. I'm not familiar with this terminology; I recommend using Western blot or Immunoblot.

      Thank you for pointing this out. We have changed “biochemical analysis” to “Immunoblot.” Page 35, line 836, and page 37, line 896.

      (2) Figure 1A: No inclusion of total EGFR.

      Phospho-EGFR levels were normalized to actin expression.

      (3) Figure 2C: Bottom panel looks like it is a merge image for CD4/6, not only Edu/DAPI.

      Thank you for pointing this out. This is a merged image of EdU, DAPI, and γ-H2AX. We have corrected the figure and clarified the figure legend, page 37, lines 889-891.

      (4) Figure 2F: How is the normalization completed? There are varying levels of yH2AX in the western blot, but all three samples are quantified as "1".

      γ-H2AX was normalized to actin levels. The mean of the g-H2AX expression levels in the E.V. samples was set to “1” so that fold change comparisons in g-H2AX expression levels between E.V. samples and CDK4 and CDK6 overexpressing samples could be made.

      (5) Figure S9: Were there vehicle mice for panels A&B?

      The growth rate of vehicle-treated mice was shown in Figure S4A. They were not included in Figure S9A and S9B to more clearly visualize the main points of the figures.

      Reviewer 2 (Public review):

      Major Comments:

      (1) Reliance on overexpression models over loss-of-function

      The mechanistic studies mainly rely on overexpression of CDK4 and CDK6 to simulate the amplified state. Although the authors argued that the level of overexpression mimics that observed in resistant tumors, a complementary study in which CDK4/CDK6 were suppressed in a model where CDK4/CDK6 is amplified (such as HCC827 or TH116), and replication stress and osimertinib sensitivity tested would greatly strengthen their observations. Indeed, there is mention of CDK4 constructs to perform knockdown studies in the methods, but those studies are not included in this submission.

      Thank you for this suggestion. We agree that loss-of-function studies are an important complement to overexpression studies. However, we have chosen to focus on pharmacologic inhibitors of CDK4/6, which are more clinically relevant than knockdown studies. We demonstrate that the CDK4/6 inhibitor palbociclib can prevent replication stress and restore osimertinib sensitivity in CDK6-amplified TH116 patient-derived xenografts (Figure 5 and Supplementary Figure 10). Mention of CDK4 knockdown constructs has been deleted from the methods, Page 20, line 437.

      (2) Mechanistic link between genomic instability and specific gene amplifications

      The authors highlight that CDK4/6 activation leads to recurrent copy number gains and transcriptional upregulation of specific pro-tumor genes including AGR2, ASNS, and STEAP1. While the paper establishes that CDK4/6 overexpression causes general genomic instability (increased FGA), it does not mechanistically explain why these specific genes are consistently amplified. The authors should investigate or discuss whether these specific loci are inherently fragile under replication stress, if they are direct downstream targets of the E2F transcriptional program, or if this is a result of random genomic instability followed by strong positive selection under osimertinib pressure.

      Thank you for this suggestion. We hypothesize that the amplification and expression of these genes is not due to inherent fragility of these loci under replication stress, nor are these genes known to be direct downstream targets of the E2F transcriptional program. Rather, this enrichment is more likely the result of random genomic instability followed by strong positive selection under osimertinib pressure.

      To clarify this, we have added the following to the Discussion section (Page 16-17, lines 356 366):

      "This suggests that while CDK4/6 hyperactivation induces broad structural genomic instability, it also leads to recurrent amplification and transcriptional upregulation of specific pro-tumor loci including AGR2, ASNS, and STEAP1. This enrichment likely reflects a multi-step evolutionary process rather than purely localized genomic fragility or direct E2F-driven upregulation. In this model, CDK4/6-mediated replication stress establishes a background of random structural variations, but subsequent positive selection under EGFR inhibitor pressure drives the clonal expansion of cells harboring copy number gains at these specific loci. Because AGR2, ASNS, and STEAP1 are associated with aggressive phenotypes like EMT and WNT/b-catenin activation, the enrichment of cancer cells harboring these alterations may allow them to overcome the suppressive effects of EGFR inhibitor treatment.”

      (3) Discrepancies in tumor mutational burden (TMB) reporting

      There is a slight contradiction regarding the TMB data that needs to be clarified for readers. The manuscript states that in the clinical datasets, "EGFR-mutant LUAD harboring cell cycle gene alterations exhibited significantly elevated FGA and TMB relative to cell cycle-negative tumors" (Line 265-266). However, in the next section, the authors say, "Notably, no corresponding increase in TMB was observed with CDK4 or CDK6 CNA, similar to our findings in preclinical models" (Line 271-273). The authors should clarify or discuss why broad cell cycle alterations correlate with high TMB, while CDK4/6-specific alterations drive structural instability (FGA) without increasing TMB.

      We appreciate the reviewer’s insightful comment. We agree that this distinction warrants clarification. The association between broad cell cycle gene alterations and increased TMB likely reflects that these alterations included genes whose loss of function may impair DNA repair, such as RB1 and CDKN2A/B. In contrast, our study specifically evaluated CDK4/6 amplification and found that it primarily promoted replication stress and chromosomal instability, as reflected by increased FGA. This mechanism did not correspond to an increase in the point mutations that contribute to TMB. Thus, our findings suggest that CDK4/6 amplification preferentially drives structural genomic alterations rather than mutational burden.

      To clarify this distinction, we have added the following to the Discussion, page 15, lines 332-337:

      “Notably, alterations across a broader number of cell cycle genes were associated with increased TMB in addition to increased FGA. This likely reflects the fact that broad cell cycle pathway alterations included genes whose loss of function is known to affect DNA repair, including CDKN2A/B and RB1. In contrast, CDK4/6 amplification primarily promoted replication stress and chromosomal instability, but is not known to impact DNA repair, resulting in increased copy-number alterations (FGA) without a corresponding increase in TMB.”

      Reviewer #2 (Recommendations for the authors):

      (1) The manuscript would be enhanced with a complementary study in which CDK4/CDK6 were suppressed in a model where CDK4/CDK6 is amplified (such as HCC827 or TH116) and replication stress and osimertinib sensitivity tested.

      Thank you for this suggestion. We agree that loss-of-function studies are an important complement to overexpression studies. However, we have chosen to focus on pharmacologic inhibitors of CDK4/6, which are more clinically relevant than knockdown studies. We demonstrate that the CDK4/6 inhibitor palbociclib can prevent replication stress and restore osimertinib sensitivity in CDK6-amplified TH116 patient-derived xenografts (Figure 5 and Supplementary Figure 10).

      (2) Supplementary Table 2: There are two typographical errors regarding the cell line nomenclature. In row 3 (under "In vitro 3-D models") and row 15 (under "In vivo models"), the table lists the model as "H1976 CDK6". This should be corrected to "H1975 CDK6" to remain consistent with the rest of the manuscript.

      Thank you for pointing this out. We have corrected these typographical errors in Supplementary Table 2.

      (3) Line 300: Misspelling of amplification: "...11 tumors from patients without CDK4 or CDK6 amplificaiton based on clinical sequencing data...".

      Thank you for pointing this out. We have corrected the spelling to “amplification”, page 14, line 301.

      (4) Line 358: Misspelling of treatment: "Combined osimertinib and CDK4/6 inhibitor reatment suppressed proliferation...".

      Thank you for pointing this out. We have corrected the spelling to “treatment”. Page 17, line 376.

  2. Nov 2026
    1. Author response:

      General Statements

      In addition to the point-by-point responses to the reviewer's comments, we have implemented the following changes to the manuscript to address errors in the previous version. We apologize for this inconvenience and wish to clarify that these changes do not affect the conclusion of the manuscript.

      (1) L.155 in text: “weaker” -> “stronger”

      (2) L.332-333 in text: “Of the 6 parameters, 5, excluding Linker, supported CC1 between structural and behavioral parameters (Fig. 5A). All 5 of these parameters…” -> “Of the 6 parameters, 4, excluding IDRC and Linker, supported CC1 between structural and behavioral parameters (Fig. 5A). All 4 of these parameters…”

      (3) L.532 in text: “14 fields” -> “15 fields”

      (4) L.110 in supplement: The minimum step number for single-particle tracking was 14 but not 20.

      (5) Supplement Movie S1 has been revised because the old version contains movies in the pilot experiments which were not used in the final analyses.

      Point-by-point description of the revisions

      Reviewer #1 (Evidence, reproducibility and clarity):

      Summary:

      "Single-molecule behavior and cell-growth regulation in human RTKs" studies 52 of the 58 human receptor tyrosine kinases (RTKs) on the surface of live HEK293A cells using a Total Internal Reflection Fluoresence Microscope (TIRFM) system previously described in Watanabe et al.

      Single molecule tracking is conducted automated commercial Auto Analysis System (AAS; Zido) software followed by analysis in Python via scikit-learn. The analysis includes use of a Variational Bayesian-Hidden Markov Model (VB-HMM) described previously (Hiroshima, 2018). The VB-HMM analysis was used to characterize movement of RTKs with the authors concluding that the movement could be explained by the receptors transitioning between three states: immobile, slow, and fast. Single molecular transport parameters are then extracted from the analysis and averaged results are reported. How these parameters change after stimulation are then evaluated and compared.

      To relate the diffusion "behaviors" with biological function, the authors retrieve cell growth data from loss-of-function data in the DepMap project (Arafeh, 2025). By correlating selected parameters with the functional data, the authors find that behaviors in the resting and response states partially "explained their function".

      The authors then relate specific parameters through correlation to growth-inhibitory or growthsupporting signaling, amino acid sequence characteristics ("structural"), and evolutionary parameters. Additionally, the authors build a regression model to evaluate how their behavior parameters may predict RTK functional characteristics.

      Major Comments:

      (1) The primary findings from this article are the extraction of parameters of a 3-state hidden Markov model from the analyzed single molecule trajectories of 52 RTKs. It is difficult to evaluate these primary findings since the raw data, the analysis software, the intermediate results, the hidden Markov model, and the Python analysis scripts are not readily available to the public or this reviewer. Thus the evaluation of the underlying software, applicability of the software to the problem, or reproducibility of the results from the data are not possible to evaluate. I encourage the authors to provide as much data and software available as possible even if under restricted licenses.

      a. The availability of raw single molecule movies from this study are not generally available and thus it is difficult possible to evaluate the efficacy of the Zido AAS software or compare to the tracks generated to other single molecule tracking software. While it is appreciated that a mosaic of the movies is made available as Supplemental Movies 1A through 1D, these are not in a form analyzable by other tracking software. Ideally, all the raw experimental data would be made available, but it might suffice if a single raw movie and its analysis were made available for direct evaluation.

      We recognize the importance of making the raw data publicly available, but the volume of data is too great to include with this manuscript.

      For the revised version, we considered the reviewers’ comments and uploaded raw video examples of the EGFR family (in the format of raw tif files) to GitHub (https://github.com/yanagawamasataka5zoss/smDA-Igor). Since it is impossible to upload the entire dataset, and since there are items we wish to analyze further in the future works, we will provide the data on a case-by-case basis upon request. This is noted in the manuscript under "Acquisition of single-molecule moves." in the “Materials and Methods” section (text l.538-540). 

      Procedures for the tracking is shown in the revised supplement text (text l.544 and Supplement text “Single-particle tracking”) within the range disclosed by ZIDO with the parameter values we used in this study. Since AAS is commercial, please direct all inquiries about further details to Zido, the developer and distributor.

      To validate the AAS results, we performed parallel analyses with Fiji TrackMate (Tinevez et al., Methods 2017) for the particle trajectories in the sample movies of EGFR families uploaded to the aforementioned GitHub. TrackMate-specific detection parameters were set to Grid = 5 × 5 pix, Diameter = 9 pix, Quality = 20. The gap in the TrackMate trajectories was filled by linear interpolation as employed in AAS. Subsequently, we applied VB-HMM analysis to the results of TrackMate using AAS and found that the three-state model was the most suitable for all four movies. The results are shown in the below figure.

      The coincidence of the single-particle trajectories and the mobility parameters between the results of AAS and TrackMate was compared using smDA (Igor Pro; https://github.com/yanagawamasataka5z-oss/smDA-Igor). 

      If we define matched particle positions between the results of two algorithms as those detected within 200-nm distance in the same movie frame (Author response image 1a), the mean matched ratios from AAS to TrackMate and from TrackMate to AAS were ~80% and ~70%, respectively (Author response image 1b). This difference in the matched ratios indicates that TrackMate detected a greater number of particle steps than AAS. The distributions of distances between matched particle positions (Matched) and between all nearest particle positions (in the same movie frame) in the trajectories containing at least one matched position (Total) are shown in Author response image 1c. As demonstrated in these histograms, the differences in particle positions exhibited a peak at 20-40 nm or less. The differences were more pronounced in the fast mobile state.

      Author response image 1.

      The values of the mobility parameters (D, P, L, tau) are listed in Author response tables 1-4. In general, the discrepancy between the parameter values of AAS and TrackMate was ~10% or less, with the exception of D1 (diffusion coefficient for immobile state). The substantial discrepancy in D1 is likely attributable to the small step sizes, which are commensurate with the spatial precision.

      Author response table 1.

      Author response table 2.

      Author response table 3.

      Author response table 4.

      The tracking results for these four movies have been deposited on GitHub. We note that AAS performs a full 2D Gaussian fit with a tilted-plane background at every spot. This process provides quantitative I<sub>max</sub>, I<sub>back</sub>, and per-spot PSF widths (σ<sub>x</sub>, σ<sub>y</sub>) that are required for the parameter set I and F used in this study. TrackMate's Laplacian of Gaussian-based detection does not produce equivalent quantities.

      Since the method of single-particle tracking is not the subject of this study, we do not think it is indispensable to show these data in the manuscript.

      b. The trajectory information of single particles from the Zido AAS are not available. While the raw movies may be voluminous in nature, the extracted trajectories would also be valuable. As multiple hidden Markov models are available to evaluate diffusive behaviors, it would be useful to have the trajectory information available for a comparison between distinct models to be conducted by reviewers.

      We uploaded CSV files to GitHub (https://github.com/yanagawamasataka5z-oss/smDA-Igor) showing the trajectories and changes in signal intensity of single particles derived from the sample movies. These files involve the state assignments in HMM with 1 (Model 1) to 5 (Model 5) mobility states.

      c. The Variational Bayesian-Hidden Markov Model (Hiroshima et al. 2018) that is used at the core of this paper is not readily available.

      We used a variational Bayesian inference methods for HMM composed in AAS. Since it is commercial we cannot distribute AAS.  As long as we recognized, the method based on standard algorithm of VB-EM HMM for SPT (Hiroshima et al. 2018; Yanagawa et al. 2018; Persson et al. 2013).

      We have added “VB-HMM analysis” section in the Supplement text. Here, we do not repeat explanation of the method shown in textbooks but described the special details of the algorithm which have a variation between implementations with the parameter values and model selection. One can reproduce our result from these lines of information based on the standard VB-HMM algorithm in textbooks. 

      Results of HMM analysis for the sample trajectories are shown in the csv files uploaded in GitHub (https://github.com/yanagawamasataka5z-oss/smDA-Igor). Results from the trajectories detected using TrackMate are also uploaded.

      (2) While it is appreciated that the authors combine their extracted VB-HMM parameters of RTKs to other bioinformatic data sets, the relationship to functional and structural-sequence information is only correlative. There is no attempt in this article to validate the correlative findings.

      There are very few instances of high correlation coefficients between individual parameters in different categories (behavior, structure, and function). Because there are so many parameters, these high correlations may be the result of statistical fluctuation (multiple testing). Therefore, we avoided drawing conclusions based on a simple correlation (text l.184-186; l.245-248; l.300-302; l.315-318, l.326-328). Consequently, we did not conduct any validation. One evolutionary parameter (EG1) may correlate significantly with the RTK function (text l. 270-273). However, we do not emphasize the importance of this result. Since EG1 indicates the EGFR family, a typical RTK family for regulating cell proliferation, this result may be obvious.

      Regarding the validation of pR in multiple regression models for the function, first, please note that the distributions of pR values in the models for various cell lines are often clearly biased toward positive or negative (see Figs. 3B, D and 4B, F). This suggests that these pR values were not randomly determined, but rather, there was a high degree of commonality in the pR values among the models (i.e., among the parameters' roles). However, since variation among the models cannot be ignored, we based our discussion on the major parameters (average |pR| > 0.2 or 0.1) in the statistically significant (p < 0.1) models and the parameters highly correlated with them (but removed to avoid multicollinearity) (Figs. 3 and 4; Supplement text “Parameter selection for multivariate analyses”). Given the large number of models (cell species), the sign bias of the pR values is clearly statistically significant. Furthermore, this bias is not only common in models with high explanatory power (p < 0.1) but also in the pR distributions for all models, as seen in Table 2 and Supplement Table S8A, B. To clarify these points, we colored the cells in the above tables to indicate pRs with large absolute values.

      Additionally, we validated the pR significance levels based on t-test (Tables 2, 4, and Supplement Table S8). Many of the pR values satisfy the p < 0.05 criterion for the parameters that were considered important in the models. Regarding the models for PC1 of the CRISPR factor (Fig. 6), we have indicated the 95% confidence intervals for Rs in the revised figure.

      (3) Many statistical comparisons are made in this article across cell lines, RTKs, and parameters, but it is not clear if multiple comparison corrections are applied to compensate for the false discovery rate. The authors should provide a detailed Statistical Analysis section in the methods section.

      As noted above, we did not use simple correlation coefficient (R) in our discussion due to the risk of multiple comparisons. A multiple regression model involves a single target variable vector and multiple explanatory variable vectors. Although the problem of multiple comparisons does not arise in the multiple regression modeling, multicollinearity among the explanatory variables may occur. To avoid this issue, we reduced the number of explanatory parameters by identifying combinations of highly correlated variables (Figs. 3A, C and 4A and Supplement text “Parameter selection for multivariate analyses”). 

      For multiple regression model and CCA, we added detailed explanations in Supplement text l.261-265 and text l.558-567.

      Minor comments:

      (1) The authors insufficiently cite the Broad Institute's Dependency Map project from which their functional analysis is derived. The following is quoted from https://depmap.org/portal/data_page/?tab=overview#how-to-cite .

      For DepMap Release data, including CRISPR Screens, PRISM Drug Screens, Copy Number, Mutation, Expression, and Fusions:

      DepMap, Broad (2025). DepMap Public 25Q3. Dataset. depmap.org

      Please note, you may need to update the release quarter depending on which version of the data you are using.

      We ask that you also cite the DepMap program:

      Arafeh, R., Shibue, T., Dempster, J.M. et al. The present and future of the Cancer Dependency Map. Nat Rev Cancer 25, 59-73 (2025). https://doi.org/10.1038/s41568-024-00763-x

      We have corrected the citation for DepMap (text l.581) and cited Arafeh et al. (text l.575-576). Thank you for pointing this out.

      Reviewer #1 (Significance):

      General assessment: The main significance of this paper comes from a broad and data-rich study of 52 of 58 human receptor tyrosine kinases. If this data, the intermediate analysis results such as the trajectories, or executable software used to conduct the analysis were made available, the value to the field would be high. However, the article lacks any statements regarding open availability of the data or the software. While correlating their "behavioral" parameters to other bioinformatic datasets creates context and suggests further studies, the lack of any validation of the correlative findings limits the significance of the results.

      Advance: While the authors share large final outputs of their parameter datasets, the unavailability of the raw data or intermediate results makes it difficult to compare their analysis and models to other readily available analysis pipelines or models. In particularly, it would be useful to the field if their analysis could be directly compared to the software packages in the following citations:

      (1) Monnier, N., Barry, Z., Park, H. et al. Inferring transient particle transport dynamics in live cells. Nat Methods 12, 838-840 (2015). https://doi.org/10.1038/nmeth.3483

      (2) Vega et al., Biophys. J. 2018. Multistep Track Segmentation and Motion Classification for Transient Mobility Analysis. https://pubmed.ncbi.nlm.nih.gov/29539390/.

      Audience: The potential audience is the field of receptor tyrosine kinases and more generally cell surface receptors. The lack of validation of their correlative results or comparison of their analysis pipeline to other analysis pipelines limits the value of the findings to the field. There is also a potential audience for other authors of computational trajectory analysis software if the raw data or intermediate analysis results were available. The effective audience is thus limited to biophysicists or quantitative biologists capable of replicating the VB-HMM model for validation of the correlative results in falsifiable experiments.

      Reviewer's Field of Expertise: I have a field of expertise in advanced microscopy, image analysis, single particle tracking, receptor tyrosine kinases, membrane biophysics, hidden Markov models, Bayesian analysis, and software engineering.

      Reviewer #2 (Evidence, reproducibility and clarity):

      In their manuscript entitled " Single-molecule behavior and cell-growth regulation in human RTKs" Abe et al. demonstrate automated single-particle tracking of 52 receptor tyrosine kinases (RTKs) in both resting state and upon stimulation with the respective ligands. The approach is based on transient transfection of cells with each RTK tagged with a Halo-tag, allowing for subsequent dye labeling and live cell video recording using TIRF microscopy. Subsequently, a seemingly commercial analysis software is used to then obtain particle trajectories from single molecule localizations and analyze their properties using a hidden Markov model. The authors have previously demonstrated pioneering work in the field of single-particle tracking with respect to automation (Yasui et al, 2018) and analysis (Yanagawa et al, 2021), and in this work they scale their approach up to characterize a broad set of RTKs. The resulting observations are a powerful demonstration of the benefits of SPT in general and significantly advance our understanding of the dynamics of RTKs as a class, beyond the most prominently studied candidate EGFR, as well as promising evolutionary insights.

      Comments and questions:

      (1) The authors picked 52 out 58 human RTKs. Why not all?

      We were unable to obtain cDNA for five species, and one species did not express in cells. This point was mentioned in the “Materials and Methods” section, but we move it to the “Results” section (text l.100-101).

      (2) In contrast to the above mentioned previous publications, here a seemingly commercial software package was used (AAS by Zido). The methods part is very short on the specific parameters that were used to i) localize particles (e.g. net gradient threshold) or ii) connect localizations into trajectories (step size, allowed dark frames, min. trajectory length). Similarly a clearer explanation of the HMM calculus would significantly help to better follow the analysis approach and parameter choice. Perhaps this reviewer has missed it, but why did the authors e.g. choose 3 states for HMM?

      We have added a detailed explanation on the single-particle tracking method (Supplement text “Singleparticle tracking” section). The tracking parameters that the reviewer asked about were shown in this section  

      Supplement Figure S1 and Supplement Table S1 show model selection for the HMM. After comparing models with single to five state(s), we consistently chose the three-state model, which generally produced the highest lower bound (text l.115-l.122).

      (3) The replicate experiment in Fig. S2 is appreciated, but what condition was repeated here? Also experimental details are missing: was it two repeats of: i) seeding cells in a dish, transfection, labeling, imaging? An image from cells from those repeats would be important to show, also to which degree the density of particles F varies, i.e. to which degree this is an unprecise experimental parameter itself as compared to biologically meaningful. This is especially as Fig. S2 does not contain any density comparison at all, whereas in the main figures it is indeed an experimental observable used.

      The two experiments used essentially the same population of transfectants (text l.145-146). The population was divided and transferred into two separate wells and cultured overnight. Staining was performed in each well. 

      The ratios of the F-values from the two measurements are shown in Supplement Figure S2D (upper middle) and Supplement Table S3. Supplement Figure S2D indicates the ratios of the parameter values in the two measurements for 52 RTKs. The differences were less than twice.

      The movies contain only one to three cells per field of view and exhibit significant variability in expression between cells. For this reason, they are not suitable for evaluating reproducibility and have been omitted.

      (4) The density raises another issue. Some of the movies show extremely dense signal. Here the authors should explain how they deal with particles whose trajectories cross. This could lead to artificial dynamics and a supplementary figure showing that their analysis is robust toward varying densities (again suggesting to include a simulation) could be helpful

      If trajectories intersect, our algorithm assigns the intersection point to the trajectory that was closer in the previous frame, and interrupts tracking of the more distant trajectory. Particles with fewer than 15 tracking frames are excluded from the analysis. (Supplement text “Single-particle tracking”)

      Handling the intersection of trajectories is a challenging problem in single-particle tracking. Accurately assessing the impact of this issue is also difficult. Even with a sophisticated simulator, the results may not reflect reality because diffusion coefficients and clustering states change with time for a single particle, and particle distributions are non-random. Moreover, these factors are entangled in actual cells.

      As an alternative and practical approach, we evaluated the correlation between the parameter values for particle mobility, D, L, P and tau, and the particle density (Supplement Table S9). The results are summarized in Supplement text “Dependence on the particle density” and Supplement Figure S4. It cannot be concluded that the density dependence of the measured values, and therefore, the trajectory intersections, significantly impacts the overall results of this study.

      (5) Fig. 2C is a bit hard to understand since here localizations are colored based on their state but not from which trajectory they come. Do e.g. individual trajectories show various dynamic behaviors or are the trajectories not long enough to observe this?

      Figure 2 has been revised to present examples of trajectories color-coded according to the mobility state.

      (6) The evolutionary aspects could use further and simpler explanations to make this passage easier to grasp

      We introduced evolutionary parameters because we expected them to reflect higher-order structural information that is difficult to parametrize directly (text l.265-267). From this perspective, the results of analyses suggested that higher-order structures regulate function through (or at least in correlation with) the response behaviors. This is based on the fact that evolutionary parameters explained function better than the structural parameters and explained the response dynamics better than the resting state dynamics. Additionally, the evolutionary models for function highly agreed with the response models. (text l.279l.281)

      The introduction of evolutionary parameters naturally raises questions from a different perspective regarding how evolution relates to structure, behavior, and function. We believe the reviewer’s question pertains to this very point. Since we have only used simple evolutionary grouping, we cannot address this issue by delving deeply into the details of evolutionary processes. We provided some discussion on this issue in “RTK behavior influenced by evolution and structure” section in Discussion (text l.449-l.456). Our findings suggest that multiple mechanisms produce response behavior that transcends evolutionary specificities. 

      Reviewer #2 (Significance):

      The manuscript by Abe et al. represents a significant advancement in the field of single-particle tracking (SPT) by scaling up recording 52 human receptor tyrosine kinases (RTKs), offering comprehensive insights into their dynamics beyond the traditionally studied EGFR. While the study demonstrates cutting edge single-particle tracking and provides promising evolutionary insights, it currently lacks certain methodological details that are essential for reproducibility, such as specific parameters used in particle localization and trajectory analysis. The exclusion of 6 out of 58 human RTKs without discussion also requires further explanation, but overall, the study fills a knowledge gap by providing a broad overview of RTK dynamics and their diffusion behavior. Overall, this work should have broad appeal to fields such as cell signaling as well as methods development in the area of single-particle tracking.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      (1) The core limitation of this review is that it functions primarily as an annotated bibliography rather than a critical synthesis.

      We completely agree. We have restructured Section 2 and rewritten major physiological sub-sections to inject a critical evaluative voice, explicitly categorizing findings into consensus, controversy, and preliminary/unstudied domains:

      “However, since a total per2 knockout model was used in that study, it remains to be elucidated whether these effects on retinal function are direct or mediated indirectly through systemic alterations (line217-220).

      Early studies suggested that embryonic circadian rhythms are maternally transmitted [108]. However, subsequent studies demonstrated that maternal factors provide only a transient pool of clock gene transcripts, whereas a functional circadian system is established through light-dependent activation of the offspring's own clock machinery [109,110]” (line466-470).

      (2) The framing of zebrafish as occupying a "crucial evolutionary and experimental niche" is asserted but not substantiated.

      This is an incredibly sharp and valid critique. Much of the foundational evidence for direct peripheral light-responsiveness is indeed derived from optically transparent embryos and larvae. We have added a dedicated new discussion to explicitly address this gap:

      “Much of our current understanding of direct light responsiveness and autonomous peripheral oscillators derives from studies in embryos and larvae, stages that are optically transparent and permit efficient penetration of environmental light into internal tissues [10]. In contrast, adult zebrafish progressively acquire pigmentation and increased tissue complexity, which may alter both the intensity and spectral composition of light reaching peripheral organs. Although clock gene rhythmicity and peripheral oscillators persist in adult tissues, whether peripheral photoreception contributes to circadian entrainment to the same extent as in larvae remains largely unresolved. This developmental transition raises the intriguing possibility that the zebrafish circadian system may undergo remodeling in adulthood” (335-344).

      (3) More interesting - and underexplored - is the comparative question of how the decentralised clock architecture of teleosts compares with that of other non-mammalian vertebrates, or indeed with invertebrate systems such as Drosophila, where peripheral tissue clocks and non-visual photoreception have also been studied.

      We appreciate this insightful suggestion. Additional comparative analysis regarding the decentralized clock architecture across teleosts, other non-mammalian vertebrates and Drosophila has been incorporated into our discussion:

      “Environmental light-dark cycles serve as the primary zeitgeber across vertebrate lineages. In mammals, circadian photic information is primarily detected by the retina and relayed to the master pacemaker in the suprachiasmatic nucleus (SCN), which subsequently synchronizes peripheral oscillators throughout the body [43]. In contrast, zebrafish possess a remarkably decentralized light-input system in which photic signals can be perceived not only by classical visual structures but also by the pineal gland, deep brain photoreceptors, and numerous peripheral tissue [10,44]. This distributed architecture provides multiple and partially overlapping routes for environmental light information to reach the circadian system, thereby creating a redundant and multi-layered network for reliable environmental signal detection and entrainment (Figure 2)” (line 172-181).

      (4) The discussion of non-canonical clock gene functions in the Future Perspectives section would benefit from being more directly connected to what zebrafish specifically can offer: given that teleost genome duplication has produced additional paralogues of clock genes, there is a concrete opportunity to dissect canonical from non-canonical functions through comparative analysis of paralogues with diverged expression patterns. This point is hinted at but not made explicitly.

      We have completely overhauled "Future Perspectives" to outline concrete experimental paradigms and emphasize zebrafish-specific genetic traits:

      “Importantly, this capacity for non-hierarchical, multi-node coordination introduces an equally profound challenge at the molecular level: separating the canonical role of core clock genes in driving the molecular loop from their non-canonical, clock-independent functions. The zebrafish provides a unique genetic advantage to address this mechanistic boundary, as its clock paralogues underwent evolutionary sub- or neo-functionalization, thereby naturally uncoupling clock-dependent oscillations from independent biochemical activities. Thus, the zebrafish stands not only as a tool for network chronobiology, but also as a primary platform for discovering novel, non-canonical regulatory networks” (lines 510-518).

      Reviewer #2 (Public review):

      (1) Line 101: The reference that clock mutations result in human disease mirroring mammals is supported by a reference from Zhadnova on melatonin. This is a stretch.

      We completely agree with the reviewer and apologize for the inappropriate over‑extrapolation of the previous reference. To fully address this, we have removed the problematic citation and added two appropriate references linking circadian dysregulation to human pathophysiology (line 102):

      1. Ruggiero, G., et al., Period 2: A Regulator of Multiple Tissue‑Specific Circadian Functions. Front Mol Neurosci, 2021. 14: p. 718387.

      2. Petzold, T., et al., BMAL1 modulates glutamine supply to control haematopoietic stem and progenitor cell expansion. Development, 2026. 153(8).

      (2) Line 170 defines light, with a reference. Why?

      Thank you for your constructive comments. We have removed the definition of light. (line 173)

      (3) Line 259. It is not clear what is meant by "in vitro" in this sentence. What is described is either in vivo or ex vivo.

      We apologize for the ambiguous terminology. We have revised the text (line 260), replacing “in vitro” with “ex vivo” to accurately describe the experimental system.

      (4) The abstract states zebrafish have emerged as a premier model for studying circadian rhythms. I would argue it is the opposite. Surprisingly little is known about circadian regulation in zebrafish compared to flies and mice, and that is why this review might be particularly timely.

      We sincerely thank the reviewer for this profound and perspective-shifting comment. We entirely agree with your assessment. Compared to the long-standing and deeply characterized genetic blueprints in Drosophila and mice, our current understanding of circadian regulation in zebrafish remains fragmented and significantly less mature.

      The revised text now reads as follows (Line 28):

      “The zebrafish (Danio rerio) has emerged as a uniquely powerful and increasingly pivotal model.”

      (5) Line 63. The statement does not make sense to me. The regulatory logic is highly similar in flies and humans. The clock is somewhat decentralized (as it likely is in humans), but there are primary pacemaker cells.

      We sincerely thank the reviewer for pointing out this insufficient description. We have further revised and polished this paragraph, and the revised text is presented as follows (Lines 60-72):

      “Among the model organisms used in circadian research, zebrafish occupy a unique and powerful position for comparative and functional studies, standing alongside mammals (such as the mouse) and invertebrates (such as Drosophila), thereby providing critical evolutionary insights [4]. The core molecular architecture of the circadian clock—centered around a transcription-translation feedback loop (TTFL)—is remarkably conserved across diverse phylogenetic taxa. As a teleost fish, the zebrafish shares a close genomic and physiological evolutionary proximity to humans, exhibiting highly orthologous core clock genes (clock, bmal, per, cry) and signaling pathways [4]. Concurrently, zebrafish possess distinct biological advantages that expand the scope of in vivo inquiry. These include external fertilization, transparent embryos permitting real-time visualization of rhythmic processes, rapid organogenesis within 24–48 hours post-fertilization, and a robust genetic toolkit for manipulation via CRISPR/Cas9, transgenesis, and morpholino knockdown [5–7].”

      Recommendations for the authors:

      Reviewer #3 (Recommendations for the authors):

      (1) Lines 60 - 66. Here are many misleading statements. This text implies fish represent evolutionary intermediates between invertebrates, such as the Drosophila and mammals, such as the mouse. This is a fundamentally flawed view. Fish and mice are highly specialised extant species of vertebrates. Fish do not represent intermediates between mammals and invertebrates. This should be rephrased. Also, the authors make inaccurate and contradictory statements in the next sentence, namely implying that mice do not "utilise distinct clock genes and regulatory logic" and also imply that only zebrafish (unlike mice and Drosophila), "exhibit a high degree of conservation in core clock genes (.....) and pathways with humans". This is clearly not the case... the clock genes in mouse and humans are also highly conserved - and this similarity extends to Drosophila. This section needs to be completely rewritten to correct these problems.

      Thank you for your constructive comments. We agree with the reviewers' suggestions and will incorporate the recommended changes into the manuscript.

      The revised text now reads as follows (Lines 60-72):

      “Among the model organisms used in circadian research, zebrafish occupy a unique and powerful position for comparative and functional studies, standing alongside mammals (such as the mouse) and invertebrates (such as Drosophila), thereby providing critical evolutionary insights [4]. The core molecular architecture of the circadian clock—centered around a transcription-translation feedback loop (TTFL)—is remarkably conserved across diverse phylogenetic taxa. As a teleost fish, the zebrafish shares a close genomic and physiological evolutionary proximity to humans, exhibiting highly orthologous core clock genes (clock, bmal, per, cry) and signaling pathways [4]. Concurrently, zebrafish possess distinct biological advantages that expand the scope of in vivo inquiry. These include external fertilization, transparent embryos permitting real-time visualization of rhythmic processes, rapid organogenesis within 24–48 hours post-fertilization, and a robust genetic toolkit for manipulation via CRISPR/Cas9, transgenesis, and morpholino knockdown [5–7].”

      (2) Lines 88 - 89. The authors need to explain more clearly why the light-input system in fish is "redundant and multi-tiered". This is not obvious.

      Thank you for your constructive comments. We sincerely apologize for the lack of clarity and the absence of explicit, specific references in our original statement regarding the "redundant and multi-tiered" nature of the fish light-input system. To clarify, the terms "multi-tiered" and "redundant" are based on the unique decentralized nature of the teleost circadian system. Specifically, the system is "multi-tiered" because light reception occurs at three distinct anatomical levels: ocular (retina), extraocular/deep-brain (pineal complex), and peripheral (individual tissue cells) . It is "functionally redundant" because these pathways serve as mutual backups; classic studies demonstrated that even when both the eyes and the pineal gland are surgically removed, peripheral tissues in fish can still directly perceive light and successfully entrain their circadian rhythms (Whitmore et al., 2005).

      1. Tamai, T.K., A.J. Carr, and D. Whitmore, Zebrafish circadian clocks: cells that see light. Biochem Soc Trans, 2005. 33(Pt 5): p. 962-6.

      “Environmental light-dark cycles serve as the primary zeitgeber across vertebrate lineages. In mammals, circadian photic information is primarily detected by the retina and relayed to the master pacemaker in the suprachiasmatic nucleus (SCN), which subsequently synchronizes peripheral oscillators throughout the body [43]. In contrast, zebrafish possess a remarkably decentralized light-input system in which photic signals can be perceived not only by classical visual structures but also by the pineal gland, deep brain photoreceptors, and numerous peripheral tissue [10,44]. This distributed architecture provides multiple and partially overlapping routes for environmental light information to reach the circadian system, thereby creating a redundant and multi-layered network for reliable environmental signal detection and entrainment (Figure 2)” (line 172-181).

      (3) Lines 140 - 141. Here are several incorrect statements: The zebrafish genome possesses THREE clock genes (clock 1a, 1b and 2 (NPAS2 homolog)), THREE bmal genes (1a, 1b and 2a) and FOUR per genes (1a, 1b, 2 and 3). See and cite the original "Wang" references on this topic (e.g. ref 36 and others not referenced here).

      We are immensely grateful to the reviewer for pointing out these factual inaccuracies regarding the specific number and nomenclature of the core clock gene families (clock, bmal, and per) in zebrafish. We apologize for our previous oversight and fully agree that precision in genomic composition is paramount.

      Following your expert guidance, we have thoroughly verified the zebrafish genomic database and integrated the pioneering work by Wang and colleagues (e.g., Wang et al. on the evolution and identification of core clock genes in teleosts) to rectify these descriptions.

      The revised text now reads as follows (Lines 140-143):

      “The zebrafish genome contains three clock genes (clock1a, clock1b, and clock2), three bmal genes (bmal1a, bmal1b, bmal2a), four per genes (per1a, per1b, per2 and per3), and at least six cry genes” [38, 39]

      1. Wang, H., Comparative genomic analysis of teleost fish bmal genes. Genetica, 2009. 136(1): p. 149-61.

      2. Liu, C., et al., Molecular evolution and functional divergence of zebrafish (Danio rerio) cryptochrome genes. Sci Rep, 2015. 5: p. 8113.

      (4) Lines 144 - 145. To my knowledge, there is no record of the Cry1a protein acting as a "bona fide photoreceptor with light-induced conformational changes". In any case, reference 36 is incorrect, since this is a Wang reference for the Bmal gene phylogeny in fish.

      We would like to thank the reviewer for pointing out this issue. "In zebrafish peripheral cells, light can directly reset the circadian rhythm. The expression of cry1a is strongly induced by light, and the degree of this induction is highly correlated with the magnitude of the clock phase resetting. Studies have shown that in many organisms, blue-light illumination triggers a conformational change in cryptochrome—specifically the rearrangement or 'opening' of the C-terminal domain—thereby exposing the interface for binding with downstream proteins. Direct or indirect structural and biochemical evidence for this mechanism exists in plant AtCRY1, Drosophila CRY, green alga CraCRY, and various members of the Cry family; therefore, it is highly likely that a light-induced conformational change is similarly relied upon in zebrafish." we have added references to support this idea.

      The revised text now reads as follows (Lines 146-147):

      “Cry1a acting as a bona fide photoreceptor potentially undergoing light-induced conformational changes” [14, 40, 41].

      1. Tamai, T.K., L.C. Young, and D. Whitmore, Light signaling to the zebrafish circadian clock by Cryptochrome 1a. Proc Natl Acad Sci U S A, 2007. 104(37): p. 14712-7.

      2. Berntsson, O., et al., Photoactivation of Drosophila melanogaster cryptochrome through sequential conformational transitions. Sci Adv, 2019. 5(7): p. eaaw1531.

      3. Partch, C.L., et al., Role of Structural Plasticity in Signal Transduction by the Cryptochrome Blue-Light Photoreceptor. Biochemistry, 2005. 44(10): p. 3795-3805.

      (5) Line 147. Reference 16 is NOT the original reference for Cry2 and Cry4, lacking the motifs necessary for CLOCK-BMAL interaction / transcriptional repression. Instead, the correct citation should be for Liu et al., Sci Rep. 5, p8113 (2015).

      We sincerely appreciate the reviewer’s careful revisions, and we have supplemented the relevant references in the revised manuscript.(line 143)

      1. Liu, C., et al., Molecular evolution and functional divergence of zebrafish (Danio rerio) cryptochrome genes. Sci Rep, 2015. 5: p. 8113.

      (6) Lines 148 - 150. The statement that the zebrafish expanded and diversified genetic repertoire "provides a natural system for probing structure-function relationships within the circadian machinery" is unclear. How does this logic operate...?

      We would like to thank the reviewer for pointing out this issue. Our core idea is that zebrafish clock genes have diversified into multiple paralogs that exhibit a clear division of labor. As exemplified by the Cry proteins in this study, variations in the amino acid sequences and protein domains among these different paralogs mean that directly comparing their structural differences could enable the precise mapping of functional domains, rendering them an ideal experimental model.(lines 150-152)

      (7) Lines 212 - 214. The authors point to reference 42 as evidence that per2 mutations impact on the retinal pathway function. However, this paper documents the phenotype of a total per2 KO, and so it is unclear whether this is a direct or indirect effect on retinal function. This caveat must be mentioned.

      We sincerely thank the reviewer for pointing out this critical distinction. We agree that because reference 42 utilized a total per2 knockout model, the observed phenotypes could potentially stem from indirect systemic effects rather than a direct impact on the retinal pathway itself. Following the reviewer's valuable suggestion, we have added this caveat to the revised manuscript to ensure a more precise and accurate interpretation of the cited literature.

      The revised text now reads as follows (Lines 213-215)::

      “Studies have shown that mutations in per2 result in phase delays in zebrafish locomotor rhythms, lengthened cycles, and a reduction in both visual sensitivity and contrast sensitivity [26, 47]. However, since a total per2 knockout model was used in that study, it remains to be elucidated whether these effects on retinal function are direct or mediated indirectly through systemic alterations.”

      (8) Line 276. To my knowledge, Reference 58 is dedicated to observations in the mouse model; there is no study of the zebrafish here. This citation should be corrected.

      We sincerely apologize for this oversight. The reviewer is absolutely correct that the original Reference 58 focused on a mouse model rather than zebrafish. We appreciate the reviewer's meticulous reading. We have corrected this error in the revised manuscript by replacing the incorrect citation with appropriate literature relevant to zebrafish deep-brain photoreception.(line 277)

      1. Fernandes, A.M., et al., Enlightening the brain: linking deep brain photoreception with behavior and physiology. Bioessays, 2013. 35(9): p. 775-9.

      (9) Line 288. Reference 5 has no reference to circadian clocks or the circadian timing system. Again, this citation should be corrected.

      We deeply apologize for this careless mistake and any confusion it may have caused. The reviewer is entirely correct that the original Reference 5 was irrelevant to the circadian timing system. We are very grateful for your rigorous review and for catching this error.

      We have thoroughly checked and corrected this citation in the revised manuscript. The incorrect reference has been replaced with the appropriate literature that establishes the decentralized nature of the zebrafish circadian system.(line 289) 28. Wang, Z., et al., Light-regulated microRNAs shape dynamic gene expression in the zebrafish circadian clock. PLoS Genet, 2025. 21(1): p. e1011545.

      1. Tamai, T.K., A.J. Carr, and D. Whitmore, Zebrafish circadian clocks: cells that see light. Biochem Soc Trans, 2005. 33(Pt 5): p. 962-6.

      (10) Line 321. Reference 72 makes no mention of the zebrafish or zfCry1a!!.

      We highly appreciate your rigorous checking. In the revised manuscript, we have corrected this citation by replacing it with the definitive literature that demonstrates the light-induction of cry1a in zebrafish.(line 322)

      1. Tamai, T.K., L.C. Young, and D. Whitmore, Light signaling to the zebrafish circadian clock by Cryptochrome 1a. Proc Natl Acad Sci U S A, 2007. 104(37): p. 14712-7.

      (11) Line 365. Reference 66 does not explicitly indicate a specific role for the molecular clock in cardiovascular tissue in the zebrafish. it just shows rhythmic expression of clock mRNA in the heart.. Is this a reasonable citation to make...?

      We thank the reviewer for this careful comment. We agree that the original reference only demonstrates rhythmic clock gene expression in the heart, rather than a specific functional role of the molecular clock in zebrafish cardiovascular tissue. We have removed reference 66 and added more appropriate citations that directly support circadian clock function in the zebrafish cardiovascular system.(line 366)

      1. Xu, W., M.K. Jain, and L. Zhang, Molecular link between circadian clocks and cardiac function: a network of core clock, slave clock, and effectors. Curr Opin Pharmacol, 2021. 57: p. 28-40.

      2. Fong, C.K., et al., Daily rhythms in heartbeat rate are intrinsic to the zebrafish heart. Curr Biol, 2021. 31(5): p. R239-r240.

      (12) Line 369: Reference 51 is completely inappropriate. Instead, this citation reports the shutdown of photoreceptor function in zebrafish larvae at night.

      We are deeply grateful to the reviewer for pointing out this critical error. Upon re-verifying our source material, we realized that the statement regarding "bmal2 mutants losing heart rate rhythms and developing bradycardia" was a severe writing mistake and factual error during our manuscript drafting. It did not accurately reflect the findings in zebrafish literature, and Reference 51 was indeed entirely irrelevant. To rectify this and maintain the highest level of scientific accuracy, we have completely removed this erroneous description of the bmal2 mutant phenotype from the manuscript. Instead, we have revised the text To focus strictly on well-validated data from credible zebrafish studies concerning the regulatory effects of circadian clock genes on the expression of key hematopoietic marker genes [78].

      The revised text now reads as follows (Lines 368-369)::

      “Moreover, circadian clock genes can regulate the expression of key hematopoietic marker genes [85].”

      1. Zhong, Y., et al., Ezh2 promotes clock function and hematopoiesis independent of histone methyltransferase activity in zebrafish. Nucleic Acids Res, 2018. 46(7): p. 3382-3399.

      (13) Line 382: Reference 22 is not appropriate. This documents oscillations in the pineal and brain - to my knowledge, there is no link made with the liver here.

      We are deeply embarrassed by this error and offer our sincerest apologies to the reviewer. You are entirely correct—the original Reference 22 strictly investigated molecular oscillations in the pineal gland and brain, containing no data regarding hepatic rhythmicity. Introducing it here was a major referencing blunder on our part. We highly appreciate your rigorous checking, which helped us correct this false citation. In the revised manuscript, We have removed the inappropriate citation and replaced it with highly relevant literature that directly supports circadian clock function in zebrafish hepatic and metabolic tissues.(line 383)

      1. Boyle, G., et al., Comparative Analysis of Vertebrate Diurnal/Circadian Transcriptomes. PLoS One, 2017. 12(1): p. e0169923.

      2. Paredes, J.F., et al., Daily rhythms of lipid metabolic gene expression in zebra fish liver: Response to light/dark and feeding cycles. Chronobiol Int, 2015. 32(10): p. 1438-48.

      (14) Line 431: In this "Reproductive Rhythmicity" section, how much work relates specifically to the zebrafish and how much is a general feature of vertebrates?

      We thank the reviewer for this insightful comment. We agree that a clearer distinction between zebrafish-specific findings and general vertebrate features is necessary. We have substantially revised this section (Lines 431–446) to accurately delineate these aspects.

      The revised text now reads as follows (Lines 440-452):

      “In addition, the ovary possesses an independent melatonin synthesis machinery and a peripheral circadian oscillatory system, in which the rhythmic expression of core clock genes and melatonin synthesis-related genes exhibits prominent tissue specificity and light dependence [102]. As a core biomarker for human reproductive diseases, anti-Müllerian hormone (Amh) binds specifically to the Bmpr2a/Bmpr1bb receptors on the surface of pituitary gonadotropes, activates the phosphorylation of downstream Smad1/5/9, and binds to multiple cis-regulatory elements of clock genes to sustain the high-amplitude oscillation of clock gene expression [103]. Furthermore, the expression of key genes governing DNA methylation and demethylation in the gonads exhibits distinct circadian rhythmicity. This rhythm is characterized by both environmental light synchronization and endogenous autonomy, while displaying pronounced sex-specific differences [104].”

      1. Khan, Z.A., et al., Melatonin biosynthesizing enzyme genes and clock genes in ovary and whole brain of zebrafish (Danio rerio): Differential expression and a possible interplay. General and Comparative Endocrinology, 2016. 233: p. 16-31.

      2. Lin, Q., et al., Anti-Müllerian hormone signalling sustains circadian homeostasis in zebrafish. Nat Commun, 2025. 16(1): p. 4359.

      3. Paredes, J.F., et al., Circadian expression of DNA methylation and demethylation genes in zebrafish gonads. Chronobiol Int, 2018. 35(7): p. 920-932.

      (15) Line 447. Reference 96 and the prediction that zebrafish show maternal inheritance of circadian clock function have been disproved subsequently in numerous publications. It is, therefore, misleading to cite this particular paper and these conclusions.

      We sincerely appreciate the reviewer’s critical oversight on this point. We acknowledge that the theory regarding the maternal inheritance of fully functional circadian clock components in zebrafish embryos has been challenged and disproved by subsequent comprehensive studies. Retaining this claim would indeed be misleading. We have removed the statement claiming that "embryos inherit maternal clock gene products through oogenesis and initiate their own rhythms" along with the problematic reference [96].

      Again, we sincerely thank all reviewers for their time and expertise. The current revision addresses all objective factual and citation errors. The broader conceptual and structural improvements suggested by the reviewers will be incorporated in a future revised version.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      Using cryofixation and serial block-face electron microscopy (SBEM), P. Vijayakumar and K. Cauwenberghs characterize extracellular vesicles (EVs) and non-vesicular extracellular particles (NVEPs) within native Drosophila olfactory sensilla. The study provides a unique and valuable dataset comprising approximately 7,800 extracellular particles, systematically describing their morphology, size, density, and distribution. The ultrastructural analysis across different sensillum classes offers insights into the potential biogenesis and functions of these extracellular particles.

      Strengths:

      Cryofixation preserves EVs and NVEPs within native tissue conditions. The detailed quantification of a very large dataset provides a unique source of information on extracellular particle number, categories, and distribution. The expertise of the group in the method and the tissue explored, as well as their detailed quantification, provide confidence in the dataset and observations.

      We thank the reviewer for their positive assessment of our work. We are pleased that the value of cryofixation for preserving native ultrastructure, as well as the scale and rigor of our quantitative dataset, were recognized. We hope this resource will be useful to the broader community studying extracellular communication in sensory systems.

      Weaknesses:

      Major comments

      (1) As the authors state, the rare observation of EV budding or MVB release events suggests that these are transient processes, whereas EVs and NVEPs are retained for relatively long periods within the sensillum lumen. The current analyses may overinterpret steady-state vesicle abundance as differences in vesicle production.

      We agree with this important distinction. In our manuscript, particle number reflects steady-state prevalence within each sensillum class, not production rate. Biogenesis events were analyzed separately as transient indicators of production, with the caveat that EM captures static snapshots rather than dynamic rates. We have now clarified this explicitly in the first paragraph of the “EV and NVEP number” section in the Results. The revised text now reads:

      “To compare particle abundance across sensillum classes, we counted EVs and NVEPs within the sensillum lumen. These snapshot counts reflect the steady-state pool at fixation; they do not capture dynamic rates of production or turnover. Quantification of particle number per sensillum revealed class-dependent differences ...”

      (2) Given the above conclusion, differences between sensillum classes may be somewhat overstated.

      (a) The absolute number of EVs and NVEPs per sensillum is highly variable, even within the same sensillum class (Figure3D). For example, a substantial proportion of coeloconic sensilla have an empty lumen (Figure 3C). Consequently, expressing the data as ratios or proportions (Figures 3B, 4C, and 4E) may exaggerate differences between sensillum classes and should therefore be interpreted with caution.

      We thank the reviewer for the comment. To prevent ratio distortion, we excluded sensilla containing fewer than 5 particles from ratio calculations in Figure 3B, as noted in the figure legend. Ratios derived from low particle counts are inherently unstable and skew toward extreme values (0 or 1), producing unreliable estimates. This exclusion criterion reduces within-class variance without artificially inflating between-class differences. We have also revised the "Relative abundance" Results section to avoid overstating our findings. The revised text now reads:

      “The median EV ratios of large basiconic and trichoid sensilla did not differ significantly from 0.5, whereas intermediate, small basiconic, and coeloconic sensilla showed median ratios significantly below 0.5, indicating a population-level NVEP bias (Figure 3B). Nevertheless, EV ratios varied considerably among sensilla of the same class, and distributions overlapped broadly across sensillum classes. Consequently, no pairwise differences between classes survived FDR-corrected Dunn’s post hoc comparisons despite a trend across classes (Kruskal–Wallis test, p = 4.76 × 10<sup>-2</sup>). Thus, while NVEPs were generally more abundant than EVs at the population level in most sensillum classes, both particle types co-occurred in individual sensilla with highly variable relative proportions.”

      In Figures 4C and 4E, sensilla that lacked EVs in the lumen were excluded from the analysis so they would not skew the proportional data. We also updated the figure legend to state this explicitly.

      (b) The rate of EV/NVEP production is unknown. For a similar rate of production across sensillum classes, Figure 3E suggests that the differences in lumen morphology and size may largely explain variation in EV density and distribution.

      We appreciate the opportunity to clarify this point. As the reviewer pointed out, if particle production rates were similar across sensillum classes, differences in lumen size could in principle explain variation in total particle number. However, our data in Figure 3E argue against this possibility. If lumen volume were the primary determinant of particle abundance, volume-normalized densities should be roughly uniform across all sensillum types. Instead, we observed the opposite pattern: smaller sensilla (e.g., coeloconic) exhibited substantially higher particle densities than larger sensilla (e.g. trichoid or large basiconic).

      This inverse relationship indicates that particle abundance is not a simple function of available lumen space. Rather, it suggests that underlying factors—such as differential production, release, or clearance rates—are specific to each sensillum class. We have revised the "Volume-normalized EV and NVEP abundance" Results section to make this distinction more explicit. The revised text now reads:

      “Sensillum size varied markedly across classes (Figure 1B). If EV and NVEP production rates were comparable across sensillum classes, one would expect differences in lumen size alone to account for variation in total particle number. To test whether particle counts scale with sensillum size, we compared EV and NVEP numbers normalized to lumen volume….”

      “If lumen volume were the primary determinant of particle abundance, volume-normalized particle abundance should be roughly uniform across all sensillum types. However, this was not observed. Smaller sensilla (e.g., coeloconic) exhibited substantially higher particle concentrations than larger sensilla (e.g. trichoid or large basiconic) (Figure 3E). This inverse relationship indicates that particle abundance is not a simple function of available lumen space.

      Rather, it suggests that underlying factors—such as differential production, release, or clearance rates—are specific to each sensillum class.”

      That said, I agree that ab1 sensilla display a striking enrichment of large cargo-filled EVs compared with the other sensillum classes, while coeloconic sensilla display enrichment in small dense filled EVs (Figure 4C). Together, large and cargo-filled EV observation provides strong support for differences in EV biogenesis between ab1 sensilla and the other sensillum classes. In that context, I also think the EV size distribution shown in Figure 4 - Figure Supplement 1 should be moved into the main figure, as it demonstrates that the majority of EVs in the ab1 lumen are relatively large and are therefore likely to represent microvesicles.

      We thank the reviewer for the insightful comment. As suggested, we moved the EV size distribution from Figure 4—Figure Supplement 1 into the main figure (revised Figure 4D) to highlight that ab1 EVs are predominantly large and likely represent microvesicles.

      Could you clarify why ab1 sensilla are only included in Figure 4 and not analysed in Figure 3?

      In Figure 3, ab1 sensilla were included within the large basiconic class rather than shown separately. We grouped them this way because we did not observe marked differences in particle abundance or EV ratios between ab1 and the other large basiconic sensilla examined (ab2 and ab3). Figure 4, in contrast, focuses on subtype-specific differences in EV electron density/cargo, where ab1 is analyzed separately because it displayed a distinct profile.

      (3) Approximately 10% of ORNs appear to be degenerating in 6-8-day-old flies, which seems unexpectedly high. This contrasts with the relatively infrequent occurrence of auxiliary cell apoptosis or complete sensillum degeneration. In these "degenerating ORNs", the authors state that the hallmarks of ORN apoptosis are restricted to the dendrites. As hallmarks, they state dendrite truncation, fragmentation and blebbing. Rather than apoptosis, I wonder whether these observations might instead represent ciliary truncation and ectosome shedding, followed by degradation of the shed ciliary membrane into EVs. Ciliary truncation and ectosome shedding, followed by ciliary regrowth, are dynamic processes that have been described across multiple species. This interpretation could explain large EVs that remain in the lumen long after the cilium has regenerated. It would reconcile this article with the general agreement that cilia are a prime site for the budding of EVs across species. Additional evidence supporting apoptosis of the ORNs would help distinguish between these possibilities. Otherwise, I believe the author should reconsider their interpretation.

      We thank the reviewer for suggesting the possibility that ciliary truncation and ectosome shedding could account for the affected dendritic membrane morphology. However, after careful reconsideration, we believe our original interpretation is better supported by the ultrastructural data. Below, we address the reviewer's specific concerns.

      (1) Number of degenerating ORNs: The reviewer's estimate of "~10% of ORNs" likely conflates sensilla with individual neurons. Among 352 sensilla analyzed, we identified 32 sensilla containing at least one degenerating ORN. However, because each sensillum typically houses 2–4 ORNs and not all ORNs within these sensilla were affected, the actual number of degenerating ORNs was 47 out of 802 surveyed ORNs—less than 6%, not ~10%. We have now clarified this calculation in the revised text to prevent confusion.

      (2) Morphological evidence: While ciliary ectosome shedding and truncation are well-documented across multiple species, the structural hallmarks we observe differ in two key respects.

      (1) Extent of membrane loss: Ciliary ectosomes are small vesicles (~100 nm) shed locally from the ciliary tip or base. By contrast, the degenerating ORNs in our data show severe fragmentation or truncation affecting >1/3 of the total dendritic length (Figure 7)—a scale of disintegration inconsistent with localized membrane turnover.

      (2) Absence of regrowth: Ciliary truncation is a transient event typically followed by regrowth. If the dendritic truncation we observed reflected this process, we would expect to find ORNs containing both truncated cilia and nascent regrowth. However, we found no evidence of concurrent regeneration in our datasets.

      (3) Consistent with prior reports of ORN apoptosis: Basal ORN apoptosis has been documented in 1-week-old Drosophila (Fernández-Hernández et al., 2020) and can be induced by innate immune signaling (Takeuchi et al., 2022). The ~6% frequency we observe is therefore biologically plausible. We cannot exclude that our genetic background (carrying the UAS-APEX2 transgene) may modestly elevate this baseline rate: APEX2 is a peroxidase, and even low-level leakage expression could increase reactive oxygen species and sensitize cells to stress-induced apoptosis. As stated originally in the text, this survey was not intended as a quantification of ORN degeneration. In the revision, we now clarified that the absolute numbers should be interpreted with caution given the transgenic background. The revised text now reads:

      “In addition to sensilla with intact ORNs, we identified 32 sensilla containing ORNs with morphological features of apoptosis (Figure 7). Consistent with previous observations of ORN apoptosis (Chihara et al., 2014; Fernández-Hernández et al., 2020; Takeuchi et al., 2022), affected dendrites exhibited hallmark features of apoptotic degeneration, including truncation, fragmentation, and membrane blebbing (Nagata, 2018; Xu et al., 2019). These abnormalities were observed across sensillum classes, including 6 coeloconic, 10 small basiconic, 7 large basiconic, 1 intermediate, and 8 trichoid sensilla. In some sensilla, both ORNs appeared affected, whereas in others only a single ORN exhibited signs of degeneration. Together, these sensilla accounted for 47 affected ORNs out of 802 surveyed (~6%). The observation of degenerating ORNs in these SBEM volumes provided a unique opportunity to examine the ultrastructure of apoptotic bodies and degeneration-associated extracellular particles in situ within native olfactory sensilla.”

      “We note that this survey was not intended to provide an exhaustive quantification of ORN degeneration or to estimate the frequency of degenerating ORNs. Our flies carry the UAS-APEX2 transgene, and even low-level leakage expression of this peroxidase might elevate reactive oxygen species and thereby increase susceptibility to apoptosis; therefore, these frequencies should be interpreted with caution. Rather, these observations demonstrate that ORN degeneration can occur across multiple sensillum classes and provided a unique opportunity to compare the morphological properties of EVs and NVEPs in sensilla with either degenerating or intact ORNs….”

      We appreciate the reviewer's thoughtful suggestion of an alternative model, but the severity of dendritic disintegration and the absence of regrowth signatures together argue against ciliary truncation and ectosome shedding. We have added a brief discussion acknowledging ciliary EV shedding as a physiological process in other systems, which reads:

      “Ciliary extracellular vesicle shedding is well documented across evolutionarily distant systems, from the flagella of Chlamydomonas to the sensory cilia of C. elegans and mammalian primary cilia (Wang & Barr, 2016, 2018). It is therefore notable that we did not capture active EV budding from ORN dendritic cilia in our adult Drosophila preparations. This absence likely reflects both biological and technical constraints: ciliary EV production may be developmentally regulated and reduced in 1-week-old adults relative to earlier stages, and static volume EM may miss rare, transient release events….”

      Reviewer #2 (Public review):

      Summary:

      This paper presents a large structural survey of extracellular vesicles (EVs) and non-vesicular extracellular particles(NVEPs) in the olfactory sensilla of Drosophila melanogaster. Using high-pressure freezing and serial block-face SEM, the authors avoid many of the artifacts associated with conventional fixation and analyze more than 7,800 particles across352 sensilla. The manuscript maps the distribution of these particles, describes their morphological heterogeneity, and examines their likely origins across different sensillum classes in both normal and degenerating tissue.

      Strengths:

      The strongest aspect of the paper is the imaging. Preservation is painstakingly controlled. The cryofixation appears to preserve the sensillum lymph in a more convincing native state than standard preparation methods, giving this work gravitas. Further, the authors characterized thousands of particles, further making this data strong. The figures are strong. They are clear, easy to read, and generally well designed; I think people will use this paper as a model for how to present complex data in a concise and straightforward manner. The manuscript is careful in how it presents the dataset and does not overinterpret the descriptive observations. As an ultrastructural resource, this paper will be useful to the field. The identification of auxiliary support cells as major secretory sites, together with the striking accumulation of EVs in degenerating tissue, will provide a useful starting point for future work.

      We thank the reviewer for this thorough and encouraging assessment. We hope this ultrastructural resource will prove useful to the field.

      Weaknesses:

      The main point that could use more clarification is the vesicle categorization. In particular, the distinction between "dense," "cargo-filled," and "double EVs" is not always easy to follow from a biological perspective. Some additional discussion of how the authors think these categories relate to one another, and whether they are intended as purely morphological groupings or as distinct biological classes, would strengthen the manuscript.

      We thank the reviewer for this important point. Our vesicle classifications are strictly morphological groupings based on electron density and membrane morphology in EM images. We do not have molecular markers that would allow us to assign these morphological classes to distinct biological functional categories. As suggested, we have revised the first paragraph of the "Variation in EV properties across sensillum classes" section to clarify that these are morphological categories and to describe how their interior electron densities relate to potential macromolecular content. The revised text now reads:

      “Among the 1,397 EVs described in the previous section, ultrastructural analysis revealed three categories based on intraluminal electron density: dense (n = 730), lucent (n = 421), and cargo-filled (n = 246) (Figure 4A). These are morphological categories strictly based on ultrastructure, not verified biological classes. Dense and lucent EVs, both displaying uniform intraluminal density, were defined relative to the surrounding sensillum lymph: dense EV interiors were similar to or more electron-dense than the lymph, whereas lucent EV interiors were less electron-dense than the surrounding lymph. In contrast, cargo-filled EVs showed heterogeneous intraluminal density: a light interior with discrete, electron-dense inclusions. These categories were readily distinguishable in SBEM images and observed across sensillum classes. They likely reflect differences in luminal content: dense and cargo-filled EVs appeared more macromolecule-rich than lucent EVs.”

      We hope this morphological classification will encourage future studies to correlate these ultrastructural categories with specific molecular markers and biological functions.

      Reviewer #3 (Public review):

      Summary:

      Using cryofixation-based serial block face electron microscopy of several subregions of the Drosophila antenna, the authors segment and assemble a high-resolution atlas of the anatomical structure, density, and spatial distribution of extracellular vesicles (EVs) and nonvesicular extracellular particles (NVEPs) in different Drosophila olfactory sensilla types. This systematic and thorough description is an important prerequisite to understanding the function of extracellular particles in intercellular signaling in the nervous system. Additionally, they describe examples of putative biogenesis events (budding/fusion), as well as neuronal and axonal cell degeneration events and measure the changes in particle accumulation in these altered microenvironments. Overall, this is a significant and comprehensive analysis and represents an invaluable resource to this burgeoning field. The authors assemble an important dataset and their claims match the level of evidence provided.

      Strengths:

      (1) The authors use segmentations from four different patches of the antenna to provide a systematic ultrastructural survey of extracellular particles in native insect sensilla. The dataset captures the diversity of sensilla types and reconstructs ~7800 particles.

      (2) We commend the authors for making the EM volumes available in the public Cell Image Library with accession numbers. It would be helpful to the community to also make the segmentations for this great resource easily accessible.

      (3) The sample preparation technique appears to minimize typical artifacts associated with chemical fixation, as evidenced by the high reported sphericity of EVs.

      We thank the reviewer for this positive and thorough assessment. As suggested, we also made the segmentations publicly available alongside the EM volumes. The information is available in the Materials and Methods, which reads:

      “The segmented 3D models (including EVs, NVEPs, ORNs, and sensilla) are available separately through the Dryad Digital Repository (DOI: 10.5061/dryad.3j9kd521p). Segmented structures were grouped according to their SBEM volume of origin (volumes 1–4) and organized into structural groups using the built-in object list dialog in IMOD (accessed via "Edit" and then "Object list" in the Model View window). This grouping allows users to extract morphometric information for selected structural groups. Detailed information about the object list function is provided in the IMOD user guide (https://bio3d.colorado.edu/imod/doc/3dmodHelp/objectList.html).

      Specific points:

      (1) In Figure 3C, the authors should include a continuous measure of particle distribution in the sensilla. Currently, the authors define three categories of particle localization. In the five examples shown in Figure 3A, the spatial distribution of these particles appears quite distinct across classes. For example, EVs/NVEPs in large and small basiconic sensilla are largely restricted to the area proximal to the base, with a limited number located more distally. In contrast, intermediate sensilla show a marked concentration of particles more distally.

      We thank the reviewer for this suggestion. Continuous measurements of extracellular particle position along the sensillum length are provided in Figure 3—figure supplement 1, where each particle is plotted as a fraction of its distance from the sensillum base.

      We agree that the five examples in Figure 3A reveal distinct spatial patterns across classes. However, these reconstructions were selected to illustrate morphological diversity rather than to represent the average distribution for each sensillum type. We observe considerable within-class variability, which is why we used categorical bins in Figure 3C to highlight the most consistent finding: that coeloconic sensilla uniquely concentrate most extracellular particles below the cuticle base. We have revised the text accordingly, which now reads:

      “The position of extracellular particles relative to the cuticle base is likely to inform their cellular targets and sites of action, particularly in the lumen above the cuticle base, where ORN outer dendrites reside. We therefore examined particle position distribution by plotting each particle’s relative distance from the sensillum base (Figure 3—figure supplement 1). This continuous distribution analysis revealed distinct, though variable, class-specific spatial patterns.”

      “To summarize these distributions, we additionally classified sensilla into three categories: no particles, particles present only below the cuticle base, or particles present above the base (including those also with particles below, as sensilla with particles exclusively above the base were rare) (Figure 3C). Most sensilla contained EVs and/or NVEPs, while few were entirely particle-free. Of note, coeloconic sensilla—the smallest sensillum type (Figure 1B)—showed the highest proportion entirely lacking particles, and when present, EVs and NVEPs were largely restricted below the cuticle base (Figure 3C; Figure 3—figure supplement 1) Thus, while most sensilla harbored particles above the base, coeloconic sensilla showed either no particles or particles restricted below the base, suggesting class-specific differences in sites of action.”

      (2) The conclusion of different EV ratios across sensillum classes stems from a Kruskal-Wallis of p = 0.0476, with none surviving pairwise comparisons. This is not a strongly supported conclusion and is probably better characterized as a trend.

      We thank the reviewer for the thoughtful comment. As suggested, we revised the "Relative abundance" Results section to avoid overstating our findings. The revised text now reads:

      “The median EV ratios of large basiconic and trichoid sensilla did not differ significantly from 0.5, whereas intermediate, small basiconic, and coeloconic sensilla showed median ratios significantly below 0.5, indicating a population-level NVEP bias (Figure 3B). Nevertheless, EV ratios varied considerably among sensilla of the same class, and distributions overlapped broadly across sensillum classes. Consequently, no pairwise differences between classes survived FDR-corrected Dunn’s post hoc comparisons despite a trend across classes (Kruskal– Wallis test, p = 4.76 × 10<sup>−2</sup>). Thus, while NVEPs were generally more abundant than EVs at the population level in most sensillum classes, both particle types co-occurred in individual sensilla with highly variable relative proportions.”

      (3) The statement "selective enrichment of large, cargo-filled vesicles within the ab1 lumen suggests specialized EV-mediated communication adapted to the coordination demands of this neuronal population" seems speculative for a Results section without supporting functional evidence. It would seem better suited for the Discussion.

      As suggested, we moved the statement from the Results section to Discussion.

      (4) Figure 4: Criteria for defining the classes of EVs.

      (a) The authors should explain the rationale for classifying EVs using relative density rather than absolute density? We would expect EVs with similar contents to have similar electron density (similar darkness in the images). Would classifying them relative to the background, which itself might vary across sensilla or regions, create a possible confound, especially when comparing across sensillum classes?

      We chose relative electron density to normalize for variation in staining and contrast across SBEM volumes. Absolute pixel values would be confounded by image-level differences in acquisition and processing. Using the local lumen as an internal reference provides a consistent, scalable metric for classifying thousands of particles as electron-lucent or electron-dense.

      We acknowledge that background lumen density can vary subtly between sensillum types. For this reason, we treat relative density as a qualitative binary classification (lucent vs. dense) rather than a continuous numeric scale, and we have clarified this rationale in the Methods, which reads:

      “Classification of EV luminal density and morphology

      The inner luminal electron density of individual extracellular vesicles (EVs) was visually classified into three categories: dense, lucent, and cargo-filled. To account for variations in staining intensity and contrast across EM images, EV luminal density was evaluated relative to the surrounding lumen background of the same image. Dense EVs exhibited luminal density similar to or greater than that of the surrounding sensillum lumen, whereas lucent EVs displayed lower luminal density. Both dense and lucent EVs were defined by the uniformity of that density throughout the EV interior. On the other hand, cargo-filled EVs contained heterogeneous, electron-dense material within the lumen….”

      (b) The two example images (in Figure 4A) of the cargo-filled EVs appear to have different densities themselves. Do the cargo-filled ones also display systematic differences in density and, if so, why is this another class instead of being a subcategory within the dense and lucent classes (i.e. dense with/without cargo, lucent with/without cargo)? The dense and lucent classes are defined by their density, whereas this is a more structural property.

      We classified EVs by the uniformity of their internal density rather than by overall density alone. Lucent and dense EVs exhibit homogeneous interiors—uniformly light or uniformly dark, respectively. Cargo-filled EVs are defined by heterogeneity: a lighter background containing discrete, highly electron-dense inclusions. Because this structural distinction reflects fundamentally different cargo packaging states, we treated cargo-filled EVs as a separate class rather than as a subcategory of lucent or dense EVs We have clarified in the Methods (see above) and Results (see below) that uniformity versus heterogeneity is the operative criterion.

      “Among the 1,397 EVs described in the previous section, ultrastructural analysis revealed three categories based on intraluminal electron density: dense (n = 730), lucent (n = 421), and cargo-filled (n = 246) (Figure 4A). These are strictly morphological categories based on ultrastructure, not verified biological classes. Dense and lucent EVs, both displaying uniform intraluminal density, were defined relative to the surrounding sensillum lymph: dense EV interiors were similar to or more electron-dense than the lymph, whereas lucent EV interiors were less electron-dense than the surrounding lymph. In contrast, cargo-filled EVs showed heterogeneous intraluminal density: a light interior with discrete, electron-dense inclusions. These categories were readily distinguishable in SBEM images and observed across sensillum classes. They likely reflect differences in luminal content: dense and cargo-filled EVs appeared more macromolecule-rich than lucent EVs.”

      (c) Regarding "Double" and "Ball-and-Socket" EVs, does the density vary between the two particles involved (e.g., does the inner structure consistently differ in density from the outer)?

      We thank the reviewer for this question. We found no consistent density differences between the inner structure and the EV lumen for either “Double” or “Ball-and-Socket” EVs.

      Double EVs are classified by the presence of an internal, membrane-bound vesicle within an outer vesicle. The luminal densities of the inner and outer compartments are typically similar, though occasional variations occurred.

      Ball-and-socket EVs are classified by their structural coupling—one vesicle fitting into a concave invagination of another. The “ball” and “socket” typically share similar densities (e.g., both lucent or both dense). While density variations can occur, they are not a consistent or defining feature of this morphological class.

      We revised the text accordingly, which reads:

      “Beyond density differences, we identified structural variants of EVs, including double EVs and ball-and-socket EVs. Double EVs, defined as vesicles that enclose one or more smaller vesicles…. The luminal densities of the inner and outer compartments were typically similar, though occasional variations occurred.”

      “In contrast, ball-and-socket EVs consist of two vesicles physically coupled in a joint-like configuration, with one vesicle partially invaginated into the other…. The “ball” and “socket” typically share similar densities (e.g., both lucent or both dense), although density variation is not a defining feature of this class….”

      (5) What was the rationale for the 200μm and 1000μm size cutoffs? A continuous distribution of maximum particle sizes would provide a clearer understanding of the data.

      We thank the reviewer for this question. The 200 nm and 1000 nm cutoffs were chosen to represent commonly used EV categories in the literature: <200 nm as the conventional upper limit for small EVs/exosome-like particles (endosomal/MVB origin), 200–1000 nm for medium EVs/microvesicle-like particles (plasma-membrane budding), and >1000 nm for large EVs or apoptotic bodies. These cutoffs facilitate comparison with prior studies and interpretation in the context of known biogenesis pathways.

      We agree that continuous size distributions are informative and have therefore shown them in Figure 8B. The continuous data reveal a modest but significant overall shift toward “smaller” NVEPs and EVs in degenerating sensilla at the population level.

      However, categorical analysis reveals an additional, biologically relevant pattern that continuous distribution summaries can obscure: because the mean is disproportionately weighted by the most abundant particle type, the predominance of small EVs can mask the appearance of a less numerous but distinct larger population. Intact sensilla frequently contain mainly small EVs (<200 nm) (27%), a category entirely absent in degenerating sensilla (Figure 8C), whereas very large EVs (>1000 nm) are rare in intact sensilla (5%) but common in degenerating sensilla (~38%). Thus, although medium-to-very-large particles are outnumbered by small EVs and therefore contribute little to the overall mean, they represent a clear emergent population in degenerating sensilla. In other words, degeneration produces more particles across sizes and, importantly, adds a population of medium-to-very-large particles.

      We have revised the Results to (1) state the literature-based rationale for the 200 nm and 1000 nm cutoffs, (2) point readers to the continuous distribution in Figure 8B, and (3) explicitly explain how the continuous and categorical analyses provide complementary insights into degeneration-associated changes in particle size and abundance. The revision now reads:

      “However, a striking pattern emerged when sensilla were categorized by the size of their largest EVs. Approximately 27% of intact sensilla only contained small EVs (<200 nm, the likely size range of exosomes), whereas this category was absent in degenerating sensilla (Figure 8C). Conversely, only ~5% of intact sensilla contained very large EVs (>1000 nm, large EVs and apoptotic bodies), compared to ~38% of degenerating sensilla.”

      “The categorical analysis reveals an additional, biologically relevant pattern that the continuous distribution alone can obscure: degeneration-associated extracellular particle accumulation is primarily driven by increased particle abundance across all size ranges. Notably, all degenerating sensilla contained EVs >200 nm, and a substantially larger fraction contained very large EVs (>1000 nm). Although apoptotic bodies are highly heterogeneous in size and can range broadly from ~50 nm to several microns (Elsner et al., 2023), these large EVs fall within the upper size range commonly associated with apoptotic bodies (Battistelli & Falcieri, 2021; Shahi et al., 2024).”

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      (1) Figure 1: For readers outside the field, a schematic illustrating the organization of a sensillum would be extremely helpful. Specifically, showing the positions of auxiliary cells relative to the ORN soma, inner dendrite, outer dendrite, and sensillum lumen would facilitate interpretation of the possible origins and fate of EVs and NVEPs.

      We thank the reviewer for this helpful suggestion. We have added Figure 1—figure supplement 1 to the revised manuscript as suggested.

      (2) Figure 4 (and possibly Figure 2C): The size distributions of dense, lucent, and cargo-filled EVs appear to be multimodal, suggesting at least two distinct populations. This could indicate heterogeneity in EV biogenesis. Could the authors analyse these distributions further?

      We thank the reviewer for the careful observation. As suggested, we analyzed the distributions further with Hartigan's dip test for multimodality.

      Hartigan's dip test measures the maximum vertical distance (the "dip") between the sample distribution and the closest unimodal distribution function. This non-parametric approach directly tests whether a dataset contains a single peak (unimodal) versus multiple peaks (multimodal) without assuming a standard Gaussian curve or requiring specific parametric distribution shapes. High p-values (p > 0.05) indicate that the data is consistent with a single, unimodal population.

      For Figure 2C, Hartigan's dip test confirmed unimodality for overall EV (p = 0.990) and NVEP (p = 0.981) diameter distributions. For Figure 4B, EV density categories similarly showed unimodality for dense (p = 0.993), lucent (p = 0.993) and cargo-filled EVs (p = 0.951).

      We have updated the figure legends accordingly to reflect these changes in the revision.

      (3) Figure 4C and Figure 4-figure supplement 1: Most EVs in ab1 sensilla are large cargo-filled vesicles, whereas coeloconic sensilla contain the highest proportion of small dense EVs and are associated with more MVBs. These observations are, in my opinion, among the strongest pieces of evidence supporting differences in EV biogenesis between sensillum classes, yet they receive relatively little discussion.

      We thank the reviewer for raising this point. We have revised the Discussion accordingly, which now reads:

      “EVs are thought to arise through endosomal release via MVBs or direct plasma membrane budding (Doyle & Wang, 2019; Malkin & Bratman, 2020; Neyroud et al., 2022; Remans et al., 2025; Singh et al., 2024; Welsh et al., 2024). Our data suggest both pathways are active but differentially favored across sensillum classes. Of note, coeloconic sensilla contain abundant small, dense EVs alongside frequent intracellular MVBs, consistent with endosomal release. Conversely, ab1 sensilla are enriched in large, cargo-filled vesicles with fewer MVBs, suggesting a preference for direct plasma membrane budding. The scarcity of both MVBs and budding figures in intact sensilla likely reflects the transient nature of EV biogenesis.”

      (4) Figure 4D-F: The ball-and-socket EVs are particularly interesting. I assume these structures are observed only among the larger EVs (>200 nm), but this information is not provided. Is there any evidence that they represent intermediates between complex EV budding events and ultimately double EVs?

      As the reviewer pointed out, ball-and-socket EVs are predominantly >200 nm in diameter. However, we found no evidence that they represent budding intermediates. These structures are typically located distally in the sensillum lumen toward the sensillum tip, distant from the plasma membranes of ORNs or auxiliary cells where active budding or exocytosis would occur. They are also morphologically distinct from double EVs: in ball-and-socket configurations, the two participating vesicles are of comparable size, whereas double EVs consist of a small intraluminal vesicle fully enclosed within a substantially larger outer vesicle.

      While static EM cannot capture membrane dynamics, the distance from cell membranes and the size symmetry between the coupled vesicles suggest that ball-and-socket EVs represent physical interactions between mature, extracellular vesicles rather than biogenetic intermediates. We have clarified these structural distinctions in the revised Results, which reads:

      “In contrast, ball-and-socket EVs consist of two vesicles physically coupled in a joint-like configuration, with one vesicle partially invaginated into the other (Figure 4D). These structures are predominantly >200 nm and typically located distally in the sensillum lumen, distant from the plasma membranes of ORNs or auxiliary cells where active budding would occur.... Unlike double EVs, which comprise a small intraluminal vesicle enclosed within a substantially larger outer vesicle, ball-and-socket configurations involve two similarly sized vesicles. Their size symmetry and distance from cell membranes suggest they represent physical interactions between mature extracellular vesicles rather than budding intermediates....”

      (5) Figures 4 and 5: The origin of NVEPs is not addressed. One possibility is that EVs and NVEPs share a common origin, which would be consistent with their frequent co-occurrence (approximately a 0.5 ratio). Could the authors investigate whether NVEPs originate from MVBs or cargo-filled EVs by comparing the size of the dense particles they contain? Figure 5A suggests that MVBs contain densely packed material that may be informative.

      We thank the reviewer for this suggestion. NVEPs lack a bounding membrane, whereas MVBs contain membrane-bound intraluminal vesicles, making a direct MVB origin structurally inconsistent. We also saw no evidence—such as ruptured membranes or degradation intermediates—that cargo-filled EVs release their dense contents as free particles. We have therefore avoided speculative biogenetic models for NVEPs. The ~0.5 co-occurrence ratio more likely reflects shared extracellular accumulation than a common cellular origin.

      (6) In C. elegans, ectosomes are observed that are directly captured by auxiliary glia surrounding the cilia base; did the authors check for membrane budding at the level of the cellcell contact between dendrite and auxiliary cells?

      We thank the reviewer for this comparison with C. elegans. We examined ORN–auxiliary cell contact sites for membrane budding and for evidence that auxiliary cells capture EVs, but found neither at these interfaces.

      (7) This dataset is exceptional for follow-up and comparative studies. I noticed that the raw dataset is available through the Cell Image Library. Are these SEM volumes segmented or annotated for EVs and NVEPs?

      We thank the reviewer for this question. The Cell Image Library hosts the raw, unsegmented SBEM volumes. As suggested, we have made the segmented 3D models—including EVs, NVEPs, ORNs, and sensilla—available separately through the Dryad Digital Repository.

      We have updated the Materials and Methods to direct readers to both repositories.

      “The SBEM image volumes are available in the Cell Image Library (http://www.cellimagelibrary.org/home) under the following accession numbers: CIL:57519 (Volume 1), CIL:54614 (Volume 2), CIL:54609 (Volume 3), CIL:57579 (Volume 4). The segmented 3D models (including EVs, NVEPs, ORNs, and sensilla) are available separately through the Dryad Digital Repository (DOI: 10.5061/dryad.3j9kd521p). Segmented structures were grouped according to their SBEM volume of origin (volumes 1–4) and organized into structural groups using the built-in object list dialog in IMOD (accessed via "Edit" and then "Object list" in the Model View window). This grouping allows users to extract morphometric information for selected structural groups. Detailed information about the object list function is provided in the IMOD user guide (https://bio3d.colorado.edu/imod/doc/3dmodHelp/objectList.html).”

      (8) The discussion would benefit from some additions. Potential differences in EV biogenesis between ab1 and coeloconic sensilla. Comparison with other species: the absence of observable EV budding from ORN cilia is surprising given reports in Chlamydomonas, C. elegans, and cultured mammalian cells, yet this discrepancy is not discussed. The introduction and discussion suggest the existence of EV-mediated communication between ORNs and auxiliary cells, but only one example is provided. Is there additional evidence supporting such communication in Drosophila? If not, it may be helpful to discuss evidence from other model organisms where EV-mediated communication between sensory neurons and supporting cells has been reported (e.g. C. elegans).

      We thank the reviewer for these suggestions. We have expanded the Discussion to address these points. The additional Discussion sections are shown below.

      “EVs are thought to arise through endosomal release via MVBs or direct plasma membrane budding (Doyle & Wang, 2019; Malkin & Bratman, 2020; Neyroud et al., 2022; Remans et al., 2025; Singh et al., 2024; Welsh et al., 2024). Our data suggest both pathways are active but differentially favored across sensillum classes. Of note, coeloconic sensilla contain abundant small, dense EVs alongside frequent intracellular MVBs (Figures 4C and 5F), consistent with endosomal release. Conversely, ab1 sensilla are enriched in large, cargo-filled vesicles with fewer MVBs, suggesting a preference for direct plasma membrane budding. The scarcity of both MVBs and budding figures in intact sensilla likely reflects the transient nature of EV biogenesis.”

      “Ciliary extracellular vesicle shedding is well documented across evolutionarily distant systems, from the flagella of Chlamydomonas to the sensory cilia of C. elegans and mammalian primary cilia (Wang & Barr, 2016, 2018). It is therefore notable that we did not capture active EV budding from ORN dendritic cilia in our adult Drosophila preparations. This absence likely reflects both biological and technical constraints: ciliary EV production may be developmentally regulated and reduced in 1-week-old adults relative to earlier stages, and static volume EM may miss rare, transient release events. Instead, our data suggest that auxiliary cells are active contributors to the luminal EV pool in adults, a view independently supported by the recent identification of support-cell-specific GAL4 drivers that label EV-like structures originating from tormogen and trichogen membranes (Ballou et al., 2026). EV-mediated exchange between sensory neurons and supporting cells appears to be evolutionarily conserved. In Drosophila olfactory sensilla, where ORNs are intimately ensheathed by auxiliary cells, EV-mediated crosstalk may similarly coordinate sensillar physiology, though future functional studies with cellspecific genetic manipulation will be needed to test this directly.”

      Reviewer #2 (Recommendations for the authors):

      There are a few places where the presentation could be improved:

      (1) Figure 3B: The numbers showing analyzed sensilla at the bottom of each bar are difficult to read because the white text overlaps with white data points. This should be an easy fix.

      As suggested, we have revised Figure 3B to improve readability.

      (2) Figure 3C: The category "particles above cuticle base" appears to combine cases where particles are found only above the cuticle base with cases where they are present both above and below. These should be separated for clarity.

      We thank the reviewer for this suggestion. In our dataset, sensilla with particles exclusively above the cuticle base were rare; “above” particles were almost always accompanied by “below” particles. A separate "exclusively above" category would yield near-zero frequencies, adding visual clutter to Figure 3C without additional biological insight. We have retained the current grouping and clarified in the revised Results section, which reads:

      “To summarize these distributions, we additionally classified sensilla into three categories: no particles, particles present only below the cuticle base, or particles present above the base (including those also with particles below, as sensilla with particles exclusively above the base were rare) (Figure 3C).”

      (3) Figure 4C: Since the text and plot separate large basiconic sensilla into ab1 and ab2/3, it would help to state in the main text that ab1 sensilla contain four neurons whereas ab2/3 contain two.

      We have revised the Results section accordingly, which now reads:

      “Among large basiconic sensilla—ab1 (four ORNs), ab2 (two ORNs), and ab3 (two ORNs)—ab1 showed the greatest enrichment of cargo-filled EVs.”

      (4) Vesicle categorization: A representative EM image showing examples of the overlaps summarized in the Figure 4B Venn diagram would be helpful.

      We thank the reviewer for this suggestion. We have revised the Venn diagram in Figure 4 to include representative EM images showing examples of these overlapping morphologies.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Reviewer #1 (Public review):

      (1) While the authors successfully inhibit PGE2, the SASP is a complex cocktail of factors. The discussion regarding the long-term presence of these "live" senescent cells is somewhat limited. Although the hydrogel retains cells locally, the potential for other chronic inflammatory factors to eventually promote tumorigenesis or tissue damage in the surrounding niche warrants careful consideration when translating this approach to patients and may require additional preclinical testing.

      We have provided new experimental data to address this concern. Specifically, we performed a serial in vivo study in which the hydrogel vaccine was injected subcutaneously, and the injection site was harvested on days 1, 3, 7, 14, 21, and 28 for gross observation of gel degradation and H&E histological examination (Figure S11).

      The results showed that the hydrogel began to degrade around day 3, degraded progressively thereafter, and was completely degraded by day 28 (Figure S11A). Importantly, H&E staining revealed no abnormal immune-cell infiltration or tissue damage in the surrounding skin at any time point, indicating local biosafety throughout the entire residence window (Figure S11B). Together with our existing biosafety data, these results indicate that the exposure of the local niche to live STCs and their secretome is temporally bounded (~4 weeks) rather than indefinite, which substantially limits the risk of chronic inflammation or pro-tumorigenic tissue remodeling.

      (2) The study posits that STCs serve as an antigen reservoir. However, the manuscript would benefit from a clearer distinction between whether the immune system is recognizing senescence-specific neoantigens or simply shared tumor antigens that are being presented more effectively due to the adjuvant effect. The authors briefly touch upon neoantigens in the discussion, but the experimental data primarily measure general anti-tumor responses.

      The detailed reply is provided in the R1-1 response.

      Reviewer #1 (Recommendations for the authors):

      (R1-1) Clarification of Antigen Source: The discussion mentions that senescence generates neoantigens. It would be beneficial to include data or an expanded discussion comparing the antigenic profile of the STCs versus the parental tumor cells. Does the vaccine protect against non-senescent tumor rechallenge primarily because of shared antigens, or are the T-cells specifically targeting senescence markers.

      To address this issue, we carried out a new therapeutic experiment, which we designed to functionally dissect the relative contribution of senescence-specific neoantigens versus shared tumor antigens (Figure S9). We established subcutaneous LLC tumor-bearing mice and compared three treatment groups on day 11: (i) PBS control; (ii) matched vaccine (LLC-CLX-Lipo@Gel: senescent LLC cell vaccine); and (iii) mismatched vaccine (B16F10-CLX-Lipo@Gel: senescent B16F10 cell vaccine). The matched LLC-CLX-Lipo@Gel achieved a tumor inhibition rate of approximately 90%, whereas the mismatched B16F10-CLX-Lipo@Gel inhibited tumor growth by only 40% compared to PBS. These findings indicate that the antitumor immunity elicited by the vaccine primarily targets tumor antigens shared between senescent cells and their parental tumor cells. The residual efficacy of the mismatched vaccine (~40%) likely reflects the SASP-driven innate components (e.g., NK-cell activation and recruitment).

      (R1-2) Comparison to Standard Lysates: In Figure 2, the authors compare STCs to "Died STCs" (cells subjected to freeze/thaw, essentially lysates at this point). While STCs performed better, it would be helpful to explicitly discuss why the live metabolic state is crucial. Is it solely the continuous secretion of chemokines (SASP) that makes the difference? A brief clarification on the duration of SASP secretion within the hydrogel in vivo would strengthen this claim.

      We have now addressed this issue in the revised Discussion. The live metabolic state of STCs may contribute through two complementary mechanisms:

      - Sustained adjuvant/secretory function: The SASP is an actively regulated, translationally controlled secretory program. Live STCs therefore continually replenish chemokines and cytokines and provide ongoing paracrine stimulation to immature immune cells within the gel depot, whereas a freeze/thaw lysate delivers only a single, finite bolus of pre-formed mediators and DAMPs. A similar advantage was also observed in a killed but metabolically active bacterial vaccine that highly elicits effector T-cell responses and benefits from the potency of live vaccines and the safety of non-proliferation (Brockstedt et al., 2005).

      - Prolonged in situ antigen release: Sustained release from an in-situ depot outperforms bolus delivery (Kim et al., 2015). In our system, live STCs persist within the gel and release antigen under continuing innate activation, consistent with the observation that senescent cancer cell vaccines outperform immunogenic-cell-death vaccines (Marin et al., 2023a) and that antigen bursts from dying cells are insufficient on their own (Liu et al., 2023). Regarding the duration, our new degradation study shows the hydrogel matrix begins degrading at ~day 3 and is fully degraded by day 28 (Figure S11A), defining the upper bound of the in vivo secretory phase at approximately 4 weeks.

      (R1-3) Hydrogel Degradation: More context or data regarding the degradation rate of the chitosan hydrogel in vivo. Knowing the physical integrity of the gel over this period is important for understanding the release kinetics of the liposomal celecoxib.

      We have performed this experiment and provided the results (Figure S11A). Subcutaneous injection sites were monitored on days 1, 3, 7, 14, 21, and 28. The hydrogel began degrading around day 3 and was completely degraded by day 28, with no inflammatory cell infiltration detected in the adjacent skin at any time point (Figure S11B). This degradation timeline aligns with the intended release kinetics for early immune-priming and subsequent safe clearance. The result shows the physical disintegration kinetics of hydrogel matrix, suggesting the upper bound of the drug release at approximately 4 weeks.

      (R1-4) Minor Point – SASP Components: The study focuses heavily on PGE2. It would be informative to check if Celecoxib treatment alters the secretion of other key SASP factors (e.g., IL-6, TGF-β) beyond just PGE2, to ensure the "good" chemokines are indeed unaffected.

      We have performed an ELISA experiment to assess the anticancer SASP factors (IL-6 and TNF-α). The results revealed that celecoxib treatment did not significantly alter the secretion of IL-6 or TNF-α compared with vehicle-treated STCs (Figure S5). This indicates that celecoxib selectively suppresses the COX2/PGE2 arm without broadly suppressing the immunostimulatory SASP.

      Reviewer #2 (Public review):

      Major Critiques:

      (1) The authors emphasize the expansion and activation of cDC1 as a key mechanism linking innate and adaptive immunity, yet it does not directly test whether cDC1 is required for the observed CD8<sup>+</sup> T-cell responses and tumor control.

      The authors should perform experiments using Batf3-deficient mice or any other cDC1-depletion strategies to provide important mechanistic validation. If such experiments are not feasible, this limitation should be more clearly acknowledged and discussed.

      We sincerely appreciate the reviewer's insightful and constructive comment regarding the causal validation of cDC1s in our therapeutic model. We fully agree that evaluating therapeutic outcomes in Batf3-deficient mice or via in vivo cDC1-depletion approaches represents the gold standard for establishing the indispensable role of this subset. Due to the current unavailability of the Batf3 knockout mouse strain and the experimental constraints, we were unable to conduct these specific animal experiments; we have thoroughly acknowledged this limitation in the revised discussion.

      (2) The authors note that senescence may generate neoantigens distinct from those present in proliferating tumor cells, but the extent to which STC-induced immunity cross-reacts with non-senescent tumor cells is not fully addressed. While it is appreciated that tumor challenge experiments are included, the author should perform a more explicit analysis of antigenic overlap that would strengthen the translational relevance of the approach. For example, they can compare senescence induced by different stimuli or directly assess immune recognition of non-senescent tumor targets, which would help clarify whether the vaccine primarily exploits senescence-specific antigens or broadly shared tumor antigens.

      We thank the Reviewer for this incisive comment. We first wish to correct the record. In the original Discussion we speculated that senescence generates neoantigens absent from parental tumor cells. Our new data do not support senescence-specific neoantigen dominance, and we have removed that statement from the revised Discussion. We address this raised issue in three parts.

      (1) Cross-reactivity with non-senescent tumor cells is an operating principle of the study. In every efficacy experiment in the manuscript, the vaccine is composed of senescent cells whereas the target is an actively proliferating, non-senescent tumor of the same lineage. STC-elicited immunity therefore necessarily engages antigens expressed by proliferating tumor cells. What had remained untested was whether this cross-reactivity is antigen-repertoire-dependent, or merely the consequence of non-antigen-specific adjuvant activity. The new experiment addresses this question.

      (2) In this new experiment (Figure S9), we compared a matched vaccine (senescent LLC) with an unmatched vaccine (senescent B16-F10) in mice bearing LLC tumors. Both cell lines are on the C57BL/6 background, and the unmatched arm isolates antigen-repertoire mismatch while excluding allogeneic rejection — the principal confounder of such comparisons. The two vaccines were prepared and administered using the same procedures, and the only variable that differs between the two arms is the antigen repertoire. Matched vaccination reduced tumor burden by ~90% versus PBS, whereas the unmatched vaccine achieved only 40%. The ~50-percentage-point difference suggests the antigen-dependent, lineage-restricted component of efficacy. It indicates that STC-elicited immunity recognizes non-senescent tumor cells, and that this cross-reactivity requires the tumor-antigen repertoire shared within the tumor lineage, rather than private senescence-specific antigens. From a translational standpoint this is favorable: the vaccine engages the proliferating tumor that constitutes the bulk of a patient's tumor burden, rather than the small senescent fraction.

      (3) The residual activity of the mismatched vaccine is antigen-independent and is consistent with the SASP-driven innate arm that we document independently. Two lines of our own data bear on this:

      - The cell-free components of the platform did not control tumor growth. In the prophylactic melanoma model, CS@Gel alone and CLX-Lipo alone — i.e., without STCs — did not restrain tumor growth (all non-STC groups exceeded 500 mm³ by day 14, versus 181 mm³ for the complete vaccine; Figure 7E–F). The residual activity of the mismatched vaccine therefore cannot be attributed to the hydrogel or to celecoxib.

      - Senescent cells activate innate immunity directly. STCs, but not their non-senescent parental cells, increase DC maturation, CD8<sup>+</sup> T-cell activation and NK-cell activation in vitro (Figure 1C–E), and elevate perforin and granzyme B in the culture supernatant (Figure 1F–G). Within the hydrogel, STCs+CLX-Lipo@Gel restored the NK–DC axis: NKG2D and NKp46 upregulation, increased NK proliferation and NK-mediated killing of tumor cells, and NK-derived CCL5/XCL1 secretion that recruits DCs (Figure 6B–K); in vivo, the same treatment increased circulating NK cells and activated NK cells (Figure 7G–I).

      This is consistent with an established literature. Senescent tumor cells recruit, and are directly eliminated by, NK cells in a chemokine- and NKG2D-dependent manner (Iannello et al., 2013; Antonangeli et al., 2016, 2019), and NK-cell-derived CCL5 and XCL1 recruit cDC1 into tumors — a pathway that tumor-derived PGE₂ suppresses and that our CLX-Lipo component is designed to release (Böttcher et al., 2018). However, we are explicit about the limits of this interpretation: because this experiment did not include a cell-free arm under identical conditions, we cannot formally partition the residual activity, and a contribution from tumor antigens incidentally shared between two C57BL/6 tumor lines, cannot be excluded. We now state this limitation in the revised manuscript.

      (3) Hydrogel encapsulation clearly extends STC persistence in vivo; however, the study provides limited information on the eventual clearance of these cells and the potential implications of prolonged SASP exposure. Given general concerns regarding chronic inflammation associated with senescent cells, additional discussion of long-term local and systemic responses would be helpful. If extended safety analyses are beyond the scope of the current study, the authors should acknowledge the limitation.

      We have generated new data directly informing the clearance question. Serial observation on days 1, 3, 7, 14, 21, and 28 showed that the hydrogel was completely degraded by day 28 (Figure S11A). H&E staining of the injection-site skin showed no immune-cell infiltration or tissue pathology at any time point (Figure S11B). The results suggest long-term local biocompatibility of the hydrogel vaccine. Yet, the long-term systemic response remains further investigation.

      (4) The immunological effects are attributed to COX2/PGE2 inhibition, but it remains unclear whether these effects are specific to celecoxib or could reflect formulation-dependent or off-target mechanisms. The authors may perform additional experiments employing an alternative COX2 inhibitor, genetic COX2 suppression, or PGE2 rescue, which could further support the specificity of the COX2/PGE2-dependent mechanism.

      We have performed the suggested experiment using two of the proposed strategies: an alternative COX2 inhibitor (meloxicam, MLX) and exogenous PGE2 rescue. We utilized a transwell chemoattraction assay for BMDCs co-cultured with treated NK cells. Both celecoxib and meloxicam markedly enhanced NK-mediated BMDC migration compared to PBS or untreated STC groups. Crucially, the addition of exogenous PGE2 reversed the enhanced DC-recruitment effect of both inhibitors (Figure S6). The data confirm that the restored NK–DC crosstalk is driven by PGE2 depletion per se, rather than off-target effects of celecoxib.

      Reviewer #2 (Recommendations for the authors):

      Minor Critiques:

      (1) Senescence heterogeneity is not addressed in the current study. Given growing awareness that senescent cells are not a uniform population, a brief discussion acknowledging this point would be appropriate.

      We have added a paragraph to the Discussion acknowledging that senescent cells constitute a highly heterogeneous population, and that senescence-inducer-dependent variability should be systematically mapped in future platform optimizations.

      (2) Terminology alternates between "live vaccine" and "whole tumor cell vaccine"; consistent terminology would improve clarity.

      Thank you for pointing this out. In the revised manuscript, we have unified the terminology, consistently referring to the platform as a “senescent tumor cell (STC)-based live vaccine”.

      (3) The discussion could be strengthened by clearly addressing translational considerations such as autologous versus allogeneic STCs, scalability, and regulatory challenges associated with live senescent cells.

      We thank the reviewer for this constructive suggestion. We have expanded the Discussion to address key translational aspects. Specifically, we contrasted the personalized antigen fidelity of autologous cells with the scalability and biobanking advantages of allogeneic platforms. We also delineated the regulatory and manufacturing hurdles associated with live senescent cells, focusing on the verification of irreversible arrest, SASP management, and GMP standardization.

    1. Author response:

      The following is the authors’ response to the previous reviews.

      eLife Assessment:

      This is an important study reporting a new phenotype for a gene cluster that has previously been associated with the responses of the Gram-negative opportunistic pathogen Pseudomonas aeruginosa to flow fluid. Expression of the froABCD gene cluster is induced by HOCl in vitro and by activated immune cells, which produce these types of reactive chlorine species and the evidence presented by the authors is in many places convincing. Overall, the authors have been responsive to the previous review, although the exact mechanism of fro induction by HOCl remains unclear. The high cysteine- and methionine content of the antisigma factor FroI hints at a direct oxidative modification of this protein during activation of the operon and a corneal infection model shows that fro is upregulated in P. aeruginosa 20 h after infection, but the evidence that HOCl is the causative agent of fro upregulation under these conditions is at present circumstantial. This study is of interest to infection biologists interested in mechanisms of bacterial pathogenicity.

      We thank the eLife editors for their valuable assessment. We respectfully request a revision to the assessment phrase “but the evidence that HOCl is the causative agent of fro upregulation under these conditions is at present circumstantial” for the Version of Record. We believe the phrase ‘under these conditions’ is unclear and could be interpreted to the conditions of the broader study, which would draw into question the core findings of the work. We are unsure whether ‘under these conditions’ also referred to the FroI oxidation model but have now clarified in the main text that this was a proposed model, not a claim, and have reduced the emphasis of this concept from the abstract.

      We respectfully offer the following minor suggestions to increase the clarity of the statement:

      (1) Add a period after “hints at a direct oxidative modification of this protein during activation of the operon” to ensure that this statement is not convolved with the subsequent statement on corneal infection.

      (2) Alter “under these conditions” to “in this infection model”.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      Foik et al. report that hypochlorous acid, a reactive chlorine species generated during host defense, activates the transcription of the froABCD in P. aeruginosa. This gene cluster had previously been associated with a potential role during flow of fluids and appears to be regulated by the sigma factor FroR and its antisigma factor FroI. In the present study, the authors show that froABCD is expressed both in neutrophils and macrophages, which they claim is likely a result of HOCl but not H2O2 production. Fro expression is also induced in a murine model of corneal infection, which is characterized by immune cells invasion. Expression of the fro system can be quenched by several antioxidants, such as methionine, cysteine, and others. FroR-deficient cells that lack froABCD expression during HOCl stress, appear more sensitive to the oxidant.

      Strengths:

      The authors provide a number of data supporting their claim that transcription of the froABCD system is induced by reactive chlorine species. This was shown by RNA-seq, qRT-PCR, and through microscopy using a transcriptional reporter fusion. Likewise, elevated expression of froABCD was shown in vitro and in vivo, excluding potential in vitro artifacts. The manuscript, while mostly descriptive, is easy to follow and the data were presented clearly and convincingly. The authors have also been responsive to concerns from the previous review.

      We thank the reviewer for their positive evaluation.

      Weaknesses:

      (1) Line 10: "HOCl preferentially oxidizes....". Please consider modifying the language to: "the second-order rate constant of HOCl is significantly higher with Met/Cys compared to other aa."

      We have made this change.

      (2) I am not sure I completely understand Fig. 1B. Is the promoter right upstream of yfp or is yfp located downstream of froA? If the latter is the case, wouldn't this be a translational fusion?

      The reporter was placed after the FroA stop codon. Both froA and yfp are under transcriptional control by the same single fro promoter within the froABCD operon. The construct is therefore not translationally fused but rather is transcriptionally fused to the fro promoter.

      (3) My previous comment regarding why fro expression is higher during phagocytosis in macrophages compared to neutrophils has been somewhat (albeit not convincingly), addressed by the authors in the response to the reviewer, but this discussion should be part of the manuscript as the macrophage data were shown.

      We have added that fro activation may also be caused by macrophage MPO-produced HOCl or another macrophage species in the discussion.

      (4) Line 122: The statement "The degree of fro inhibition by 4-ABAH...." is incorrect unless the authors can provide experimental evidence. Fro expression is not upregulated because MPO is inhibited by 4-ABAH, which results in less hOCL production.

      We have rephrased this explicitly as “The suppression of fro activation by 4-ABAH pre-treatment of neutrophils prior to PMA stimulation …” instead of “The degree of fro inhibition by 4-ABAH…” to clarify that 4-ABAH does not directly inhibit fro expression.

      (5) Can Supp Fig. 1 be quantified in a similar way it was done for HOCl to allow for a better comparison if HOCl or flow is the more potent inducer?

      We believe that comparing fro activation by flow and HOCl is an excellent experiment. However, the growth conditions for flow and HOCl stimulation are significantly different (growth phase, medium, temperature) so a comparison using the existing data is not particularly meaningful. We will perform this comparison in a future study.

      (6) Overall, the fro expression (YFP/mCherry) seems highly variable for treatment with HOCl (Fig. 2C: ~65; 2D: ~20; why is fro expression 3x lower?

      We attribute the discrepancy to maintenance changes in the fluorescence microscope equipment that were made in between the measurements, which affected fluorescence excitation and emission, and the high sensitivity of the fro reporter to small changes in the concentration of HOCl (Fig. 3B). While the results follow the same qualitative trend, we believe that the discussion of the quantitative fold-changes in the text are not necessary. We have replaced the numerical fold-changes previously used to describe Fig. 2C and Fig. 3B with qualitative descriptions instead to reduce confusion.

      (7) The authors should provide evidence that N-chlorotaurine can activate fro expression also. They said they weren't able to obtain chlorinated taurine, but this is quite simple to produce: PMCID: PMC1219228 https://pubmed.ncbi.nlm.nih.gov/9480913/

      We have now performed this measurement. Consistent with our proposed model, taurine chloramine activated fro expression (Fig. 5D).

      (8) Fig. 4 supplement 1: Please provide concentrations for the oxidants used in these experiments.

      Thank you for pointing out this omission. These have now been provided in the figure caption.

      (9) Lines 251/252: change to: upregulation of instead of in

      This change has been made.

      (10) Chaperones and other heat-shock genes are more upregulated in ∆froR, indicating elevated HOCl-mediated oxidative damage, which supports their findings.

      We thank the reviewer for this observation.

      (11) Complementation of ∆froR is missing

      We agree that this study would be strengthened by complementation. We note that this strain was previously complemented in Sanfilippo et al., Nat. Micro., 2019, confirming that the deletion functions as expected.

      (12) Line 198: The growth experiment at 4 uM shows differences between WT and mutant, but at 2 uM cells showed already low fro expression due to cell death (which has not been proven by CFU counts). This discrepancy should at least be discussed.

      The YFP reporter is sensitive to photobleaching by oxidation (i.e., Tsourkas et al., Anal. Chem., 2005). It is possible that the fro reporter is diminished at higher concentrations of HOCl but that fro components are still produced. We have now discussed this discrepancy in our discussions of Figures 3B and 6A when they arise in the Results section.

      (13) The critical in vitro experiment is missing: does purified FroI get oxidized by HOCl and dissociated from FroR?

      We agree that this is an important mechanistic prediction of our work. We feel that it is beyond the scope of the current work and emphasize it as a future direction in the Discussion.

      (14) Lines: 350-355: The claim that the fro system is the first-line defense is unproven.

      This was not a claim but rather was a proposed model. We have nonetheless removed this statement in order to reduce potential confusion.

      Reviewer #2 (Public review):

      Summary:

      Foik et al. studied the regulation of the fro operon in response to HOCl, an oxidant derived from immune cells, especially neutrophils. They use a transcriptional fusion of YFP to the froA promotor in an mCherry-expressing P. aeruginosa strain to determine fro-induction under the microscope. They use this system to study fro expression in medium, in the presence of neutrophils and macrophages, neutrophil-conditioned medium, and several chemical stimuli, including NaCl, HOCl, hydrogen peroxide, nitric acid, hydrochloric acid, and sodium hydroxide. They also use a corneal infection model to demonstrate that froA is upregulated in P. aeruginosa 20 h post-infection and perform transcriptional analyses in WT and a froR mutant in response to HOCl.

      Strengths:

      Their data clearly shows that HOCl is a strong inducer of the fro Operon. Addition of HOCl-quenching chemicals together with HOCl abrogates the response. They also show that a froR mutant is more susceptible to HOCl than WT. Their transcriptomic data reveals genes under control of the FroR/FroI sigma factor/anti sigma factor system.

      We thank the reviewer for their succinct and positive assessment.

      Weaknesses:

      Although the presented evidence is mostly solid, some of their findings need to be evaluated more carefully; explaining the rationale behind some of the experiments might enhance the article; and some of the models proposed by the authors seem far-fetched, as outlined below:

      We have addressed these issues below. We believe the ‘far-fetched’ model refers to our description that flow increases sensitivity to oxidative molecules. However, this particular finding was demonstrated in a previous publication, as described below.

      Unexpected outcomes and open questions for future research:

      (1) As outlined above, HOCl seems to be the main inducer of the fro operon. Interestingly, during interaction with immune cells, macrophages and neutrophils seem to induce a reporter gene under fro control in a similar manner, although macrophages are generally thought to produce less HOCl, when compared to neutrophils. May be this view needs to be revised, or another reactive species, produced by macrophages, can activate the fro operon as well.

      We have added to the Discussion that fro activation may also be caused by macrophage MPO-produced HOCl or another macrophage species.

      (2) HOCl is typically unstable in the presence of biomolecules. Nevertheless, medium conditioned by activated neutrophils is a strong inducer of the fro operon. The medium used by the authors for this experiment contains taurine, and, as the authors acknowledge, this taurine will likely react with HOCl to form the more stable taurine N-chloramine. Similarly, the MinA bacterial medium used to treat P. aeruginosa with HOCl directly also contains ammonium ions at mM concentrations, which could potentially react with HOCl to form monochloramine. It could be speculated that taurine N-chloramine and other chloramines are as effective as HOCl in activating the fro-operon.

      We have now measured fro expression in response to taurine chloramine, which was generated in the absence of ammonium. Consistent with our predictions, taurine chloramine activated fro expression (Fig. 5D).

      (3) The fro operon was originally described to be activated by shear stress ("flow-regulated operon"). How shear stress and HOCl-stress are related, or if fro activation by both stimuli is a coincidence, remains unclear. The authors propose a model, in which flow transports oxidizing molecules, which ultimately activate the fro operon. However, the initial work by Sanfilippo et al. (2019, Nat Microbiol) used plain LB medium in a fluidic chamber to induce the shear stress, which should be free of oxidants, and certainly of HOCl.

      We thank the reviewer for highlighting this important point. Padron et al., PNAS, 2023 showed exactly this important result: plain LB contains H<sub>2</sub>O<sub>2</sub> that activates fro expression at high shear rates. Their central finding is that shear significantly amplifies the effects of an oxidant and explains why H<sub>2</sub>O<sub>2</sub> does not activate fro expression in our experiments, which lack flow. Based on this model, one expects that flow would significantly amplify the effects of HOCl. Testing this model with HOCl is a future direction that we have noted in the discussion.

      Comments on revised version:

      The authors have addressed my concerns appropriately.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      This paper presents an fNIRS neuroimaging study with a relatively large sample of preschool children (aged 3-5) that measures both positive and negative empathy within a single task. Children watch emotional events and are asked questions about both their own emotions and the emotions of others, allowing the authors to distinguish between affective and cognitive empathy. The authors propose "foundational" models of affective and cognitive empathy and argue that their findings support the idea that cognitive empathy emerges before affective empathy in early childhood.

      Strengths:

      The paper addresses a valuable question by measuring both positive and negative empathy within a single cognitive task. The use of fNIRS with a relatively large preschool sample is commendable, and the pre-registered design strengthens the contribution. The task itself is innovative, well-suited to this age group, and achieves high compliance, which is essential and notably difficult with young children. Overall, the methods are appropriate, and the empirical work is valuable.

      We thank the reviewer for highlighting the strengths of our work.

      Weaknesses:

      The main concerns relate to the framing of the paper rather than the empirical work itself. The introduction contains several claims that are overstated or inaccurate. The statement that "we know very little about the development of this fundamental social skill during the first years of life" does not reflect the state of the field; empathy in early development has been quite extensively studied (e.g., Davidov et al., Malti et al., Uzefovsky et al., Decety et al., Feldman et al., among others). The view that emotional contagion directly develops into affective empathy is based on early theoretical accounts that have since been challenged by empirical evidence (see Davidov et al., 2025). The claim that cognitive empathy does not require theory of mind is also overstated - it is hard to see how theory of mind, the understanding that others have thoughts, beliefs, and emotions that may differ from our own, would not be required for cognitive empathy. Furthermore, the introduction neglects recent and directly relevant work (e.g., Zach et al., 2025; Uzefovsky et al., 2020; Davidov et al., 2021).

      We are grateful to the reviewer for directing us to this important body of work, and we have adjusted the description of our contribution in the Introduction accordingly, as follows: “While empirical studies on empathy are abundant in adults, we know little about the development of this fundamental social skill during the first years of life. In particular, the developmental ordering of its affective and cognitive components, and the neural changes underlying it, remain debated. However, understanding the mechanisms behind the emergence of the two empathic components is crucial for advancing our understanding of social development and the factors that can support emerging bonds for children in their natural environments” (page 2, Introduction section).

      We also acknowledged the body work cited by the reviewer as follows: “Recently, this linear, stage-based account has been challenged by evidence that affective and cognitive dimensions of empathy seem to be present together early in life, that concern for others does not develop in discrete stages, and that infants seem to show other-oriented responses to both positive and negative emotions, which have been interpreted as reflecting more than emotional contagion alone (Davidov et al., 2021, 2025; Uzefovsky et al., 2019; Zach et al., 2025).” (page 2, Introduction section)

      Regarding the statement on theory of mind, we did not intend to claim that cognitive empathy is completely independent of theory of mind altogether; as we note, cognitive empathy can involve elements of mentalising and recruits overlapping regions in adults. Our point is narrower: that the understanding of others' emotional states (cognitive empathy) does not require the broader capacity to represent another's thoughts and beliefs, which is the aspect of theory of mind that consolidates later in development. We have revised the passage to make this distinction explicit and to avoid overstatement as follows: “Cognitive empathy can involve elements of theory of mind or mentalising (5) and activates similar regions in adults, but specifically refers to understanding others' emotional states rather than the broader ability to represent another person's thoughts (4, 15). Thus, cognitive empathy may not necessarily require the broader belief-representing capacities of theory of mind, as emotional states can be read from external cues.” (page 2, Introduction).

      Most critically, the claim that "no neuroimaging studies have yet investigated brain regions supporting empathy in preschoolers" is inaccurate. Multiple studies have examined brain regions supporting empathy in children within this age range, including work using fNIRS and studies of positive empathy (e.g., Decety et al., 2018; Light et al., 2009; Levy et al., 2019; Bray et al., 2022; Brink et al., 2011). This is also not the first study to measure brain activation in response to positive and negative emotional events in children (e.g., Cheng et al., 2014; Light et al., 2009). These novelty claims need to be corrected.

      We thoroughly revised the literature suggested by the reviewer and we noted that:

      - Light et al. (2009) is an EEG study in 6–10-year-olds during emotional events;

      - Levy, Goldstein & Feldman (2019) is a MEG study of preadolescents (~10–11);

      - Bray et al. (2022) is a structural (voxel-based morphometry) study of empathy in 10-year-olds;

      - Cheng, Chen & Decety (2014) is an EEG/ERP in children aged 3–9 viewing animations of painful situations;

      - Decety, Meidenbauer & Cowell (2018) is an EEG/ERP study of 4-to-5 year-olds viewing painful vs. neutral stimuli.

      Therefore, all these works are either on older children (Light, 2009; Levy, 2019; Bray, 2022), not functional studies (Bray, 2022) used only negatively valenced pain/distress stimuli (but more on physical pain, Cheng, 2014; Decety, 2018), and in the case of EEG/ERP studies indexed temporal neural components rather than the regional activations our task was designed to localise.

      Brink et al. (2011) is indeed an fNIRS study of 4–8-year-olds processing affective and cognitive empathy stories (verbal and cartoon), but they used different stimuli for affective and cognitive empathy, which is what we argue against in the introduction of this work: “Within the foundational affective empathy model, cognitive empathy does not emerge before the age of 4. This has often been based on tasks that rely on children’s verbal abilities (Brink, 2011)” (page 2, introduction section).

      We have therefore adjusted the novelty sentence in the introduction as follows: “While previous studies have investigated neural responses to others' pain or distress as the empathy-eliciting stimulus, which may evoke personal distress in the observing child rather than a shared emotional response, and have largely been restricted to negatively valenced events (Cheng et al., 2014; Decety et al., 2018, Brink et al., 2011), this is the first study to test whether the developing preschool brain responds to emotional scenarios in regions comparable to those documented in adults, using a task that assesses both empathy components with the same stimuli”. (page 3 introduction).

      The use of "explicit" to describe cognitive empathy and "implicit" or "spontaneous" to describe affective empathy is problematic. Affective empathy can be expressed quite explicitly, through facial expressions, verbal statements, and gestures, and framing it as spontaneous overlooks the motivational dimensions of empathy (e.g., Zaki and colleagues). The authors' use of "foundational affective empathy model" and "foundational cognitive empathy model" as though these are established concepts is not well supported by the current evidence base.

      We thank the reviewer for this thoughtful and theoretically important comment. We agree that the terms "explicit" and "implicit/spontaneous" carry connotations that may not map cleanly onto affective and cognitive empathy as constructs. Affective empathy can indeed be expressed and even strategically deployed in highly explicit ways, and we acknowledge that our original framing did not adequately reflect this nuance.

      Regarding the terms foundational affective empathy model and foundational cognitive empathy model: we agree with the reviewer that these should not be presented as established, widely-accepted frameworks. We introduced these terms in a prior theoretical paper (Bulgarelli and Jones, 2023, JCPP Advances) to organise competing hypotheses about the developmental sequence of empathy components, and the present work constitutes the first empirical test of these models. We have referred to this reference through the introduction and discussion when discussing these models.

      To address this, we have revised the manuscript to avoid characterising affective empathy as inherently "spontaneous" or "implicit” and cognitive empathy as “explicit”:

      - “Empathy consists of two components: an affective dimension, which involves sharing others' emotions, and a cognitive dimension, which involves conceptually understanding others' emotions”. (page 2, introduction)

      - “To directly evaluate the explanatory value of the proposed foundational cognitive empathy model against the foundational affective empathy model, we designed a novel task to comparably assess both affective and cognitive empathy in pre-schoolers.” (page 3, introduction)

      - “In fact, if understanding others’ emotions is crucial for sharing them, then anything that supports this understanding becomes crucial for an empathic sharing to arise. Our data suggest that younger preschoolers engage more when explicitly prompted, while older preschoolers may have learned to think about what others are experiencing.” (page 8, discussion)

      - “It is in fact plausible to think that the cognitive dimension of empathy does not arise automatically (page 8, discussion)”

      The conclusions in the discussion go beyond what the data can support. The question of whether cognitive or affective empathy emerges first cannot be adequately addressed with a cross-sectional sample aged 3-5, an age at which affective empathy is likely already well established and cognitive empathy is expected to be developing around the lower end of this range. The cross-sectional design further limits what can be inferred about developmental trajectories during a period of substantial individual variability. Together, these issues make the developmental-precedence conclusions difficult to sustain. The claim that the results demonstrate "the first time that this brain specialisation for stimuli of different emotional valence may be rooted in childhood" is also inaccurate, as there is prior evidence for brain specialisation of emotional valence in early childhood (e.g., Grossmann et al., 2007).

      We have adjusted our conclusions to clarify that we present the cognitive-first (or simultaneous) account as our interpretation of the observed cortical specialisation, rather than as a developmental ordering directly demonstrated by the data. We acknowledge explicitly that a cross-sectional design cannot establish emergence order within a child, and have added this caveat. We note, however, that our findings, and a growing body of work questioning strictly affective-first stage models (e.g., Davidov et al., 2021, 2025), are in our view more consistent with a cognitive-first or simultaneous account, and we have framed our contribution accordingly. Consistent with this we edited the title as follows: “Head before heart? Cognitive empathy may emerge before affective empathy in the developing brain”; the abstract as follows: “These results may provide the first evidence that cognitive empathy is engaged early and develops alongside or ahead of affective empathy in preschoolers, challenging existing models and suggesting a new framework for understanding the development of empathy”, and we have extensively revised the entire discussion to tone down some of our conclusion and make clear that this our interpretation of the results. As the reviewer suggested we also acknowledge the limitation of the cross-sectional design as follows: “We interpret this as challenging years of speculation about the pivotal role of affective empathy in the development of its cognitive dimension, which was nevertheless supported by limited empirical evidence and not robustly investigated. We note, however, that a longitudinal design would be required to build on the current cross-sectional study of 3-to-6-year-olds to precisely establish the order in which these components first emerge within a child.” (page 8, discussion).

      Moreover, we agree with the reviewer that brain specialisation for stimuli of different emotional valence has been shown earlier in development; ours is, to our knowledge, the first study to explore it in the context of an empathy task. We have therefore edited the Discussion as follows: “Our results show that this cortical specialisation for stimuli of different emotional valence, well documented in infancy and early childhood (Grossmann et al., 2007), is also engaged in the context of an empathy task in preschoolers, to our knowledge the first demonstration of valence-specific cortical responses within an empathy paradigm at this age” (page 7, discussion section)

      Appraisal: The empirical contribution, the task design, the fNIRS data, and the analyses are sound and have value for the field. However, in its current form, the paper does not achieve what it sets out to do. The novelty claims are undermined by the omission of a substantial body of relevant prior work, and the developmental conclusions are not adequately supported by the cross-sectional design and age range studied. The abstract similarly overstates the support this study provides for the early emergence of cognitive over affective empathy.

      Impact: With appropriate revision, this work could make a meaningful contribution. The task is well-designed for studying empathy in young children and could be useful to other researchers in the field. The fNIRS data from a large preschool sample are a valuable resource. However, the contribution needs to be framed accurately, both in terms of what is genuinely novel relative to the existing literature and in terms of what conclusions the data can and cannot support.

      We thank the reviewer for highlighting the strengths of this work. We have thoroughly revised the manuscript and, following the reviewer's suggestions throughout, we have adjusted our conclusions and reframed the contribution of this work more precisely.

      Reviewer #2 (Public review):

      Summary:

      Authors examined neural substrates for cognitive empathy (conceptually understanding others' emotions) versus affective empathy (automatically sharing others' emotions) development in 3-5-year-old toddlers, and argued that cognitive empathy emerges earlier than affective empathy, challenging the predominant view that affective empathy develops earlier. The authors developed an empathy test for toddlers while measuring their brain activity with fNIRS (particularly in MPFC, STG, DLPFC, and TPJ) and heart rate. They found different brain region activation in cognitive versus affective empathy tasks, as well as age-related changes in the activation of right MPFC and right TPJ.

      Strengths:

      This work investigated the development of different components of empathy, which is a quite understudied topic. The authors developed an age-appropriate task for toddlers to measure their cognitive empathy and affective empathy, which is likely useful for future research in this field. Their methods are sound, and give a relatively large sample; the results look interesting and relatively solid, except for certain details in the reporting of methods and results.

      We thank the reviewer for highlighting the strengths of our work.

      Weaknesses:

      (1) My major concern is the roles of brain regions hypothesized and found in this paper (MPFC, STG, DLPFC, and TPJ) - the authors seemed to have omitted a large portion of the literature on this topic. Prior works have found that these brain regions may be involved in more than one process, or involved in processes that are common to both cognitive and affective empathy (see Schurz et al., 2021). In particular, MPFC seems to be indicated more often in cognitive empathy, and STG may be involved in both cognitive empathy and intermediate processes, which is contradictory to what the author claimed and hypothesized. Relatedly, when the authors made statements like "these results highlight that regions underpinning affective and cognitive empathy in preschoolers largely resemble those documented in adults" (without proper citations), I found it unconvincing due to the disagreements in the past adult research about brain regions related to empathy, which were not quite discussed in the current paper. It may be helpful if the authors do a more thorough literature review and provide a more comprehensive view of how their results fit in the existing literature.

      We thank the reviewer for this valuable point, and for directing us to Schurz et al. (2021). We have substantially expanded our treatment of the functional heterogeneity of these regions in both the Introduction and Discussion. In particular, two of our regions are well supported across frameworks. DLPFC and TPJ are consistently associated with cognitive empathy and mentalising across lesion, meta-analytic, and review evidence (Shamay-Tsoory, 2011; Fan et al., 2011; Schurz et al., 2021), consistent with our interpretation. We accept the reviewer's point regarding STG, which Schurz et al. (2021) implicate in both cognitive and "combined" processes that engage affective and cognitive functions in parallel. We have revised our interpretation of the STG findings accordingly, no longer treating this region as a clean marker of a single component, and we now discuss it as a region whose engagement is compatible with both component-specific and integrative processing.

      Regarding MPFC, we agree that its functional attribution warrants more careful treatment, but we would respectfully note that the literature does not support a single clean assignment in either direction. While several empathy-specific frameworks associate medial prefrontal regions with cognitive empathy and mentalising (Shamay-Tsoory et al., 2009; Fan et al., 2011; Schurz et al., 2021), a substantial affective-neuroscience literature implicates ventromedial prefrontal cortex in the generation, appraisal and regulation of emotion (Hiser & Koenigs, 2018), with lesion evidence linking damage on its more ventral part to deficits in empathy and emotion recognition. Critically, the spatial resolution of fNIRS does not allow us to distinguish ventral from dorsal medial prefrontal contributions, so we are not in a position to adjudicate between these accounts on the basis of our data. We would note, however, that while we cannot resolve ventral from dorsal contributions, sensitivity analyses in young children indicate that forehead fNIRS configurations register onto medial prefrontal regions, including more ventral medial portions (Bulgarelli et al., 2020, Human Brain Mapping). This supports the interpretability of our MPFC findings, particularly given that the ventral medial portion is the one most strongly implicated in affective processing.

      We have therefore revised the Discussion to acknowledge explicitly that MPFC is implicated in both affective and cognitive aspects of empathy, and we now interpret our MPFC findings as reflecting this region's role as a site of convergence rather than as a marker of a single component. Interestingly, the reviewer’s point is consistent with the results of this work, in which we find MPFC engagement for both affective and cognitive empathy

      We revised the Introduction to reflect the genuine heterogeneity of this region as follows: “At the cortical level, empathy engages a network of regions whose functional roles are partly overlapping (Schurz et al., 2021). Cognitive empathy has been consistently linked to the dorsolateral prefrontal cortex (DLPFC) and the temporoparietal junction (TPJ) (Shamay-Tsoory et al., 2005, 2011; Eres et al, 2015; Marsh et al, 2018). Affective empathy has been associated with activity in medial prefrontal cortex (MPFC) and superior temporal gyrus (STG). Notably, the MPFC has also been associated with cognitive aspects of empathy (Shamay-Tsoory et al., 2009; Hiser & Koenigs, 2018).” (page 2, Introduction section).

      While we already acknowledged the engagement of the MPFC in both affective and cognitive empathy in our results, we revised the discussion as follows to make the point even clearer: “Interestingly, we also found engagement of the medial portion of the PFC for cognitive empathy. This finding has also been documented in some studies on adults (Mitchell, 2009), and it is consistent with the functional overlap between the affective and cognitive sides of empathy (Shamay-Tsoory et al., 2009; Hiser, 2018). This engagement might be interpreted in light of the key role of the MPFC in self-reflection and self-processing (which we recently confirmed in the developing brain too (Bulgarelli, 2019)), a fundamental process for reflecting on others’ mental state and linking them to one’s own (Gusnard, 2001).” (page 7, discussion section).

      (2) Given the disagreement in the past research about the roles of these brain regions, I feel like the authors' hypotheses may be insufficiently justified, and their claim that cognitive empathy develops earlier than affective empathy is a bit overly strong - would it be possible that these brain regions' different rates/patterns of development are irrelevant to specific components of empathy? Given that behavioral data did not show any age difference, and that each brain region can engage in many functions besides empathy (e.g., generic social and emotional processing), I would be more cautious when interpreting these results.

      We thank the reviewer for these cautions. We address each in turn, conceding where our design genuinely constrains our claims and clarifying where we believe our design already accounts for the concern raised.

      Regarding the justification of our hypotheses given disagreement about regional roles, we have substantially revised our treatment of these regions to reflect the functional heterogeneity and ongoing debate in the literature (see our response to comment above), and we now frame our regional assignments as approximate associations rather than one-to-one mappings. We note that this heterogeneity is in fact accommodated by our findings: for example, MPFC was engaged for both affective and cognitive empathy in our data, consistent with its documented role as a region of convergence between the two components. Our hypotheses are now presented in light of this debated literature rather than against a presumed consensus.

      Regarding whether the regions' developmental patterns are "irrelevant to specific empathy components." We agree that the regions examined are multifunctional and engaged in processes beyond empathy, and we have added explicit acknowledgement of this. However, our design specifically guards against a purely generic interpretation. Our findings derive not from overall activation during a single condition, but from within-task contrasts using the same stimuli — emotional versus neutral events, and questions targeting affective versus cognitive empathy, presented to the same children. Generic social, emotional, attentional, and linguistic processing engaged by the scenarios is present across conditions and is therefore largely subtracted out by these contrasts. While we cannot exclude that some portion of the age-related differences reflects maturation of more general processes, a purely generic account is less parsimonious than one involving the empathy-relevant manipulation, since it is specifically the affective-versus-cognitive and emotional-versus-neutral distinctions, not overall task engagement, that varied with age. We now make this explicit in the Discussion as follows: “Importantly, the age-related differences we observed were specific to the empathy-relevant contrasts rather than to overall task engagement. Because our design compared emotional versus neutral events, and questions about emotional states compared to questions requiring cognitive reasoning, using the same stimuli within the same children, generic social, attentional, and linguistic demands were present across conditions and are therefore unlikely to account for the effects. While we cannot fully exclude a contribution from the maturation of more general processes recruited by the task, an account based on these specific empathy-relevant distinctions is more parsimonious than one invoking generic developmental change, since it was these contrasts, not overall activation, that varied with age.” (page 8, discussion section).

      Regarding the absence of behavioural age differences, we would respectfully note that neural and behavioural measures are not expected to track one another in this population, and that a behavioural null does not undermine a neural developmental effect. Indeed, the dissociation between neural and behavioural indices is a central rationale for using fNIRS with preschoolers: behavioural and verbal measures of empathy are known to be unreliable at this age, a point reinforced in our own sample by the substantial proportion of children (~16%) who deliberately responded counter to their evident understanding. Neural measures can therefore reveal developmental change that noisy, verbally-dependent behavioural measures are underpowered to detect. We interpret the neural–behavioural dissociation as consistent with this rationale rather than as evidence against developmental change.

      As mentioned throughout this review, we agree that our central claim was stated too strongly. While our regional findings are interpretable in terms of empathy components, our cross-sectional design and age range cannot establish that cognitive empathy develops earlier than affective empathy as a matter of developmental ordering. We have accordingly softened this claim throughout, reframing our contribution as evidence for the differential cortical engagement of affective and cognitive empathy across the preschool years, and we now present the developmental interpretation explicitly as one account requiring replication (see also our response to Reviewer 1 on this point).

      (3) It would be helpful if the authors report certain parts of their methods and results in more detail.

      (a) During the cognitive/affective empathy tasks, it is not explicitly clear which part of the fNIRS data were included in the analysis.

      We believe the data entering each contrast were already specified through the design matrix regressors and contrast definitions on page 12 of the methods section; however, to make this fully explicit, we have now added the duration of each task phase to the contrast descriptions, as follows: “The betas were then used to compute the following contrasts and test our hypotheses through one sample t-tests:

      - Affective empathy: “(events for the emotional negative scenarios + events for the emotional positive scenarios) > (events for the neutral scenarios), computed over the 8-second event phase;”

      - Cognitive empathy: “(first questions for the emotional negative scenarios + first questions for the emotional positive scenarios) > (questions for the neutral scenarios), computed over the 8-second event phase;”

      - Emotional valence: “(events for the emotional negative scenarios) > (events for the emotional positive scenarios), computed over the 8-second event phase. Fig 1A shows a graphical representation of the contrasts in the block design.”

      We also redirected the reader to Fig. 1A in which is a graphical representation of the contrasts of the block design.

      (b) When the authors did FDR corrections, they should include the q values and adjusted p values. I was also confused about how the FDR correction was conducted - were analyses performed on all 10 ROIs or only the hypothesized regions? I think if the authors have hypotheses about specific regions, they should test their hypotheses first, and then everything else would be exploratory analyses.

      We thank the reviewer for these points. We reported the corrected p-values (q-values) alongside the raw p-values, and the effect sizes in the results section (marked in red in the text).

      Regarding the analysis structure: the one-sample t-tests across all ten ROIs were preregistered (osf.io/crvz2) as exploratory analyses characterising which regions the task recruits, and were FDR-corrected across regions. We then tested for effects of age within the regions functionally defined as engaged by affective and cognitive empathy.

      (c) Additionally, it is unclear what brain template was used and what procedure was followed to map channels of fNIRS data to the template.

      The template used for the co-registration was selected from the Neurodevelopmental MRI Database of the University of South Carolina (http://jerlab.psych.sc.edu/NeurodevelopmentalMRIDatabase/). We have added this in the method section as follows: “Here the channels were coregistered onto an age-appropriate MRI template from the Neurodevelopmental MRI Database of the University of South Carolina (http://jerlab.psych.sc.edu/NeurodevelopmentalMRIDatabase/) (Richards, et al., 2015).”

      The procedure followed to coregister the array was described in our previous work (Bulgarelli et al., 2025): First, reference points, optodes and channel coordinates were estimated for each participant using STORM-Net (https://github.com/yoterel/STORM-Net). This tool estimates the position of the fNIRS optodes on the participant’s scalp, by locating some reference points in a video of the participant wearing the cap against an ideal cap placement onto a head model. Here, we have 3D printed a 5-year-old head model of the MRI template used for the optode coregistration for the offline stage of STORM-NET. Then, a 5-year-old MRI template from the Neurodevelopmental MRI Database of the University of South Carolina (http://jerlab.psych.sc.edu/NeurodevelopmentalMRIDatabase/) was segmented into 5 tissue types (scalp, skull, cerebrospinal fluid, grey matter (GM), white matter) and used to generate a volumetric multilayer mask. Routines from the DOT-HUB toolbox (https://github.com/DOT-HUB) employing iso2mesh were used to create a tetrahedral volumetric mesh, as well as a mesh of the brain (i.e. GM tissue type). For each participant, the MRI mesh model was registered on the participant’s head through an affine transformation using the model’s cranial landmarks (Nasion, Inion, Right and Left Preauricular points, Cz) and the same subject-specific landmarks estimated by STORM-NET. The affine transformation was applied to the GM mesh. The channel coordinates derived from STORM-NET were first co-registered onto the scalp mesh and then projected onto the GM surface mesh. A 1.25 cm radius sphere centred around each channel’s coordinate on the GM mesh was created to evaluate the anatomical regions overlapped by each channel. To this goal the LPBA40 atlas was used, and anatomical labels were assigned to each channel considering a minimum percentage of overlap to that region of 25%. Channels were then assigned to one of the 10 ROIs based on the anatomical label and the spatial location on the brain (see Table 1). Figure 5 provides a graphical representation of the optodes location on the template head and the brain areas covered by the fNIRS array used, where the ROIs are colour-coded.

      References:

      Schurz, M., Radua, J., Tholen, M. G., Maliske, L., Margulies, D. S., Mars, R. B., ... & Kanske, P. (2021). Toward a hierarchical model of social cognition: A neuroimaging meta-analysis and integrative review of empathy and theory of mind. Psychological bulletin, 147(3), 293.

      Recommendations for the authors:

      Reviewing Editor Comments:

      Note that there is a strong recommendation to make the task available to other researchers. Please also consider carefully the task validation (positive, negative, neutral are connoted, not demonstrated). The use of the term 'foundational' model, while understood, was questioned. In addition to the reviewers' comments, I am sure the authors are aware that foundational models have their own meaning in large language models, and thus, this term may be misunderstood. Please take this into account and consider a rephrasing.

      We thank the Editor for these helpful points, which align closely with the reviewers' comments and which we have addressed as follows:

      (i) regarding task availability: We have added an explicit statement that the full task is available upon request to the corresponding author, and we now highlight broader sharing and adaptation of the paradigm as a direction for future work in the Discussion.

      (ii) regarding task validation. We agree that the emotional and neutral conditions are connoted rather than independently demonstrated. We have clarified in the Methods that "neutral" is defined operationally by the non-emotional nature of the scene's central event and the factual focus of its question, while acknowledging that everyday scenarios cannot be entirely free of incidental affective associations. We also now note the converging internal evidence that the conditions functioned as intended: the absence of any significant heart rate change for neutral events (in contrast to both emotional conditions) and the absence of greater neural activation for neutral than emotional scenarios. We further highlight independent validation in more diverse populations as an important future direction.

      (iii) regarding the term "foundational." We appreciate the Editor's and reviewers' point regarding this terminology. We introduced the terms foundational affective empathy model and foundational cognitive empathy model in our prior theoretical paper (Bulgarelli and Jones, 2023, JCPP Advances) where they are defined in detail, and we have retained them here for consistency with that framework and the emerging literature that builds on it. To avoid ambiguity, we now cite our theoretical paper explicitly throughout this work so readers can locate the original definitions. We hope this preserves continuity with our published framework while addressing the concern about potential misreading.

      Reviewer #1 (Recommendations for the authors):

      (1) The opening example, while painting a vivid picture, emphasises affective empathy. It can convey both components for those familiar with the concept, but as described, it may be confusing. A slight adjustment would help make it clear how both understanding and sharing come together in the examples provided.

      We agree with the reviewer’s comment, and we edited the opening to highlight also the cognitive component of empathy as follows:

      “Sharing emotion is universal: a good friend is overjoyed when she gets promoted at work, we recognise why the news matters to her, and we genuinely feel happy for her. Or our sister loses her beloved pet, we understand what the loss means to her, and we feel sad for her loss. This ability to share someone else’s happiness or sadness and understand the reason of their emotion is called empathy.” (page 2 introduction).

      (2) The authors mention a target sample of 75. It would be helpful to know the rationale for this number. Was an a priori power analysis conducted?

      Yes the study was preregistered here https://osf.io/crvz2/overview, in which we wrote:

      - Sample size: Our target sample is 75 3-to-5-year-olds for the experiment, including 10 participants who will be part of the piloting phase. In a preliminary study ran in our lab with the same fNIRS system, we had an attrition rate of 25%, therefore we estimate to have at least 56 toddlers in the final sample.

      - Sample size rationale: Power analysis (G*Power, Faul et al., 2007) estimated that for a repeated measures ANOVA, with empathy component (affective/cognitive) as within-subjects factor, 54 participants are sufficient to detect a small effect (d=0.25), with power=0.97 and alpha=0.05.

      We added this specification also in the method section as follows: “(our target sample was 75 participants, as preregistered here https://osf.io/crvz2/overview).”

      (3) I would recommend reporting corrected p-values rather than raw p-values, and including effect sizes for the t-tests to aid interpretation.

      We reported the corrected p-values (q-values) alongside the raw p-values, and the effect sizes in the results section.

      (4) In Figure 5, there appears to be a child older than 6, though the stated age range is 3-5. Could the authors clarify this?

      We thank the reviewer for spotting this. Our initial plan was to recruit children aged 3 to 5 years (before they turned 6); however, one participant had to reschedule and had just turned 6 at the time of testing. We have corrected the age range throughout the manuscript to reflect this.

      (5) The authors state: "we did not observe any greater brain activations for neutral events compared to emotional events... suggesting that our task is well-suited to elicit empathic reactions in young children" (p. 6). Could the authors explain why the absence of greater neutral activation supports this conclusion?

      Our intended point was: had neutral events or non-emotional reasoning elicited greater activation in any region, this might indicate that condition differences reflected general task demands (e.g., difficulty, novelty, attentional capture) rather than emotional/empathic processing. The absence of any such reverse effect, combined with the significant emotional > neutral activations in empathy-related regions, supports the interpretation that our task selectively engaged empathy-related processing. We have rewritten the passage to make this reasoning explicit rather than implying that the null result alone is sufficient as follows: "Interestingly, we did not observe any greater brain activations for neutral events compared to emotional events, or for questions about neutral states compared to questions about emotional states. Together with the significant emotional > neutral activations reported above, this indicates that condition differences were specific to emotional processing rather than reflecting general differences in task difficulty or attentional demands." (page 7, discussion)

      (6) In the results, "all p <0.2" should read "all p > 0.2" to indicate non-significant differences.

      We apologise for the oversight and we corrected as suggested.

      (7) Figure 4A (left plot) shows an editing menu that needs to be removed.

      We apologise for the oversight, the editing menu has now been removed from the figure.

      (8) "Children with low-empathy traits lack affective empathy, while their cognitive empathy remains intact" is confusing and should be revised to "children with high callous-unemotional or psychopathic traits" for accuracy.

      Following the reviewer’s suggestion, we have replaced “children with low-empathy traits” with “children with high callous-unemotional traits” in the discussion section (page 9) as follows:

      - “On the other hand, it has been proposed that children with high callous-unemotional traits, characterised by reduced affective empathy alongside relatively intact cognitive empathy, may be able to understand others' emotional states without sharing them (64, 65), which may enable them to manipulate others without remorse.”

      - “However, more recent evidence suggests that both children with high callous-unemotional traits and autistic children may be deficient in both dimensions of empathy (67, 68).”

      Consistent with several scholars (Frick and White, 2008; Viding & McCrory, 2012; Frick, 2014), we refrain from using the term "psychopathy" in reference to children, as it is considered more appropriate for adults.

      Reviewer #2 (Recommendations for the authors):

      (1) It could strengthen the paper if the authors validate their task/stimulus with another population. For example, I wonder how the authors decided whether a scenario is neutral, since the example in Figure 1 (where kids wear their wellies and jump in the puddles) seems quite positive to me.

      We thank the reviewer for both suggestions. Regarding validation in another population, we agree this would strengthen confidence in the generalisability of the task, and we now highlight it as an important direction for future work in the Discussion, as follows: “Furthermore, the remarkably high percentage of participants who answered all questions correctly or as expected confirms that the scenarios were well-suited for this age group. Building on this, future work should validate the scenarios in independent and more diverse populations, including children from different cultural and linguistic backgrounds and across a broader age range, to confirm that the stimuli are interpreted as intended and to establish the generalisability of the paradigm.” (page 9, discussion section).

      Regarding the definition of "neutral," we appreciate the opportunity to clarify, as our use of the term is operational. In our task, what defines a scenario as neutral is the event itself: a non-emotional occurrence such as the teacher bringing wellies, rather than an emotional event. We acknowledge that it is difficult to design scenarios that are entirely free of any emotional association, but the defining event in the neutral scenarios was itself neutral, and the associated question probed a fact (e.g., what a character was doing or wearing) rather than an emotional state. We have revised the Methods to make this operational definition explicit, as follows: “For the neutral scenarios, we acknowledge that scenarios depicting everyday activities cannot be entirely free of incidental affective associations; what defined a scenario as neutral was the non-emotional nature of its central event and the factual focus of its question” (page 11, stimuli and procedure section).

      Importantly, our physiological data support the view that the neutral scenarios functioned as a non-emotional baseline: unlike the emotional conditions, the neutral condition produced no significant change in heart rate between the set-up and event phases of the scenario (t(90) = 0.65, p = 0.513), whereas both the emotional negative and emotional positive conditions did. The neutral scenarios also did not elicit greater neural activation than the emotional scenarios in any region. Together, these results indicate that the neutral scenarios served as an emotionally neutral baseline as intended, regardless of whether an individual scene depicts a mildly pleasant activity.

      (2) It would be helpful for future research if the authors made their task stimuli publicly available.

      We would be very happy to share the task with anyone who is willing to use it upon reasonable request. We have added this in the code and data availability section and in the discussion section as follows: ”This task can be shared with the scientific community upon request to the corresponding author and potentially used with children of different ages and backgrounds” (page 9, discussion section).

      (3) I found it weird that the authors corrected for motion artifacts using a wavelet filter but not a spline, with the reason being "fNIRS data quality was overall good". Do the results change using spline interpolation?

      Our decision not to apply spline interpolation in addition to wavelet filtering was deliberate and methodologically motivated, rather than based solely on overall data quality. Spline interpolation (Scholkmann et al., 2010) is designed to correct large, discrete motion artifacts (abrupt shifts and spikes) by modelling and subtracting them from identified segments. In our paradigm, preschoolers were seated and watched a screen without any movement requirement, so the data were characterised by low-amplitude, diffuse motion rather than large discrete artifacts. Wavelet filtering (Molavi & Dumont, 2012) is well-suited to this profile, as it attenuates motion-related components across the signal without requiring discrete artifact detection. Because each successive correction step alters the underlying signal, we chose the most parsimonious pipeline appropriate to our data, deviating from the preregistration in the conservative direction of minimal manipulation. Consistent with this, the recovered haemodynamic response functions shown in Figures 2–3 are smooth and free of residual spikes or motion-related artifacts, indicating that the wavelet-based correction adequately recovered clean haemodynamic responses.

      (4) The number of participants involved was confusing throughout the paper.

      (a) The degrees of freedom kept changing throughout the results section (there were 79, 85, 86, 87, 90, etc.). If the authors excluded participants in certain analyses, they should say so and also state the reason/criteria.

      The varying degrees of freedom reflect the fact that the number of participants contributing to each analysis differed depending on data quality at the relevant channels: when an ROI had no channels surviving our signal-quality and motion-correction criteria for a given participant, that participant could not be included in analyses involving that ROI. As ROIs differed in how many participants had at least one usable channel, the number of participants, and therefore the degrees of freedom, varies across regions and analyses. We have clarified this in the Methods as follows: “When an ROI had no channels surviving our quality criteria for a given participant, that participant was excluded from analyses involving that ROI. Therefore, degrees of freedom therefore may vary across regions.” (page 12, fNIRS data processing section).

      (b) When the authors used percentages of participants to describe the results, it is unclear to me what the population was (was it all 95 participants, or the 87 participants with valid fNIRS + heart data)? It was confusing when it says "10% did not complete all trials", and 10% of either 95 or 87 is a decimal number and not a whole number. Maybe the authors should just include the exact numbers in addition to the percentages. It would also be clarifying if the percentages were rounded to the same decimal place (i.e., 73.3% and 57.0%, rather than 73.3% and 57%; the same thing also applies to the p-values and other numbers).

      We thank the reviewer for asking us to double-check the numbers of the verbal responses to the task questions. These were originally calculated on the N = 90 participants with good fNIRS data. On reflection, we consider it more appropriate to calculate them on all N = 95 participants who observed the stimuli, regardless of fNIRS data quality, since verbal responses are independent of fNIRS signal quality. We have revised these figures accordingly and now report the exact number of participants alongside each percentage (to two decimal places throughout for consistency). Here the revised version of the results section (page 4):

      “Verbal responses to the task questions

      First, we assessed compliance with our task by evaluating how many of the 16 proposed trials (8 emotional and 8 neutral) participants attended (out of the total N=95 of participants who observed the stimuli). 88.42% (N= 84) of participants completed all 16 trials (mean number of emotional scenarios attended = 7.83/8, mean number of neutral scenarios attended = 7.79/8). Among those who did not complete all trials, all attended more than 75% of the emotional scenarios, while 63.64% (N=7) attended more than 75% of the neutral scenarios. There was no significant effect of age on the number of trials included (all p > 0.1). This suggests that our novel task is highly suitable for children aged 3 to 5 years.

      We then explored verbal responses to the task questions, both in the emotional and neutral scenarios. 86.32% (N=82) of the participants answered congruently with the character’s emotions at the first emotional question (‘how does s/he feel?’), 72.63% (N=69) of the participants answered congruently (i.e. what we would expect the child to feel) with the character’s emotions at the second emotional question (‘how does this make you feel?’), and 55.79% (N=53) of the participants made no mistakes, and 26.32% (N=25) made one mistake on the question in the neutral scenarios. Older age was associated with a lower percentage of mistakes when asked how the other child felt in the emotional scenarios (r(93) = -0.343, p = 0.001) and about events within the neutral scenarios (r(93) = -0.357, p = 0.001). Age did not associate with accuracy when asked ‘how does this make you feel?’ (r(93) = -0.147, p = 0.157).”

      (5) Given that the results come before methods in this paper, it would be helpful for readers if the authors included some very brief description of the numbers being reported in the results section (e.g., the beta values) as well as the experimental procedure.

      We have added a brief description of the task at the start of the Results, as follows: “N = 95 preschoolers watched 16 scenarios (8 emotional, with 4 positive and 4 negative, and 8 neutral) featuring child characters experiencing emotional or neutral events, while neural activations and heart rate were recorded. In emotional scenarios, the emotional event served to elicit affective empathy, and was followed by a question about the character's emotional state ('how does s/he feel?', cognitive empathy), a question about the child's own feelings ('how does this make you feel?'). Neutral scenarios followed the same structure with a non-emotional event and a factual question. Full details are provided in the Methods (see also Figure 1A).” (page 4, results section).

      We have also added and a short explanation of the beta values and their interpretation where neural results are first reported as follows: “Beta values index the strength of the haemodynamic response for each condition derived from a general linear model; a positive value reflects greater activation for the condition of interest relative to the comparison condition (see Methods).” (page 4, results section).

      (6) The paper mentioned "see Table 1 and Figure 4" when describing fNIRS data, but I didn't see a Table 1, and Figure 4 does not contain fNIRS data (maybe it is supposed to be Figure 3?).

      We refer to Table 1 and Figure 4 of our other work C. Bulgarelli, P. Pinti, N. Aburumman, E. J. H. Jones, Combining wearable fNIRS and immersive virtual reality to study preschoolers’ social development: a proof-of-principle study on preschoolers’ social preference. Oxford Open Neuroscience 2, 1–15 (2023). in which we described the coregistration and the process to create the ROIs.

      (7) I found this statement confusing: "There was no significant effect of age on the number of trials included (*all p < 0.25*)". Were p-values < 0.05 also true or not? Or were they between 0.05 and 0.25? There was another sentence that says p < 0.2 (was p < 0.05 also true or not?)

      We apologise for the oversight. The correct sign of the p-value was >, not <. We have corrected the statement as follows: “There was no significant effect of age on the number of trials included (all p > 0.25)”. (page 4 results section).

      (8) For a question like "how does this make you feel?", how is accuracy defined? Is it just whether or not the answer is congruent with the emotion shown in the picture?

      Yes, accuracy is defined by whether the participant's answer is congruent with the emotional event (i.e., what we would expect the child to feel). We specified this in the text as follows: 73.3% of the participants answered “congruently (i.e. what we would expect the child to feel) with the character’s emotions at the second emotional question (‘how does this make you feel?’)” (page 4 results section).

      (9) Relatedly, when discussing the results between age and accuracy of 'how does this make you feel?' (r(90) = -0.180, p = 0.089), I think concluding that "any age-related changes in general performance were not related to empathy" is overly strong. Since p < 0.10, there may be very weak evidence of an association, and I would be more cautious when interpreting this result.

      We thank the reviewer for this point. Following our re-analysis of the verbal responses on the full sample (N = 95; see our response to comment 4b), this correlation is now r(93) = −0.147, p = 0.157, i.e. non-significant. We agree that our original interpretation was too strong, and we have revised the sentence accordingly. We no longer conclude that age-related performance changes were unrelated to empathy; instead, we report simply that accuracy on the 'how does this make you feel?' question was not significantly associated with age.

    1. Author response:

      The following is the authors’ response to the previous reviews.

      Public Reviews:

      Reviewer #2 (Public review):

      This paper proposes two changes to classic RSA, a popular method to probe neural representation in neuroimaging experiments: computing RSA at row/column level of RDM, and using linear mixed modeling to compute second-level statistics, using the individual row/columns to estimate a random effect of stimulus. The benefit of the new method is demonstrated using simulations and a re-analysis of a prior fMRI dataset on object perception and memory encoding.

      The author's claim that tRSA is a promising approach to perform more complete modeling of cogneuro data, and to conceptualize representation at the single trial/event level (cf Discussion section on P42), is appealing.

      (R2.1) I wish the authors had more extensively edited the Introduction to better contextualize the work and clarify the specific settings in which they see the method as being beneficial over classic RSA. For example, some of the limitations of cRSA mentioned on page 6, e.g. related to presenting the same stimuli to multiple subjects, seem to be quite specific to settings where the researcher expects differential responses across subjects to fundamentally alter the interpretation, rather than something that will just average out by repeatedly offering the same stimulus, or combining data across subjects. It's not clear to me how the switch from 'matrix-level' to 'row-level' analysis in tRSA necessarily addresses this problem. It would be very helpful if the authors would more explicitly outline what problem the row-level aspect of tRSA is solving; what problem statistical inference via LMM is solving; and walk the reader through a very specific use case.

      We agree that the Introduction would benefit from more clearly distinguishing the specific methodological contributions of (1) row-level estimation of representational strength and (2) hierarchical mixed-effects inference. In the revised manuscript, we have added clarifying text that explicitly separates these two components and outlines the distinct problems each change addresses. We have also included a concrete illustrative example of a memory experiment to walk readers through a specific use case in which tRSA enables modeling of item-level variability that is not accessible in classic RSA. We believe these additions clarify the methodological contribution without substantially restructuring the manuscript.

      “It is important to clarify that the two components of tRSA (row-level estimation and mixed-effects inference) address distinct methodological limitations of cRSA. First, the row-level computation yields trial- or stimulus-specific representational strength estimates that are otherwise collapsed when the lower triangular entries of the RSM are vectorized and summarized into a single correlation coefficient. By retaining one representational strength estimate per trial (or per row of the RSM), tRSA enables representational strength to be modeled as a function of stimulus-level or trial-level properties without requiring discretization or aggregation. Second, the use of linear mixed-effects models addresses a separate inferential concern. When the same fixed set of stimuli is presented to multiple participants, variability attributable to stimulus identity cannot be modeled if representational strength is reduced to a single subject-level summary statistic. Retaining row-level estimates makes it possible to include both subjects and stimuli as a random effect, thereby allowing generalization beyond the specific sample of participants and items.

      To illustrate, consider a memory experiment in which 100 objects are presented once per participant. Some objects may be inherently more memorable than others, independent of participant-level variability. Under cRSA, one might compute representational strength separately for remembered and forgotten trials, yielding one value per subject per condition. However, it would not be possible to test whether item-level object memorability itself predicts representational strength, nor to model item-level variability explicitly. In tRSA, each object receives its own representational strength estimate, allowing memorability to be entered as a continuous predictor in a mixed-effects model with random intercepts for both subject and stimulus. This framework permits direct testing of item-level hypotheses and supports appropriate generalization beyond the specific stimulus set used in the experiment.”

      (R2.2) A few weaknesses mentioned in my previous review were not adequately addressed. To demonstrate the utility of the method on real neural recordings, only a single dataset is used with a quite complicated experimental design; it's not clear if there is any benefit of using tRSA on a simpler real dataset.

      We have analyzed an additional open-source dataset (Clarke citation) and added these analyses and results to the Appendix. Broadly, tRSA replicates cRSA findings in a simple object naming paradigm. See Appendix 4 Figure 15.

      “To further evaluate the sensitivity of trial-level RSA (tRSA) relative to classical RSA (cRSA), we conducted an additional representational similarity analysis using a simple categorical semantic model applied to an existing object-naming fMRI dataset originally reported by Devereux et al, 2018. The original study examined representational gradients along the ventral visual stream using a combined deep visual-semantic neural network model across early visual cortex, posterior ventral temporal cortex (pVTC), and perirhinal cortex (PRC). Methods and Results are reported in the Appendix.

      Representational Similarity Matrices

      The dataset consisted of 131 object images drawn from six semantic categories: animals, fruits, vegetables, vehicles, tools, and musical instruments. For the model RSM, a categorical model was constructed based on the six semantic categories. Stimulus pairs belonging to the same semantic category were maximally similar (1), whereas stimulus pairs belonging to different categories were maximally dissimilar (0). Diagonal elements, as is typical for both cRSA and tRSA approaches, were excluded from all analyses. Neural RSMs were created for 10 bilateral ventral-stream ROIs demonstrated to mediate object representation (Clarke et al., 2014; Devereux et al., 2018; Davis et al., 2021) spanning early visual cortex through anterior temporal cortex: left/right V1, V2, V3, posterior ventral temporal cortex (pVTC), and perirhinal cortex (PRC). For each participant and ROI, representational similarity matrices (RSMs) were computed from trial-level multivoxel activation patterns across the 131 stimuli. Neural similarity structure was compared against a categorical model RSM reflecting semantic category membership.

      Representational Similarity Analysis

      For cRSA, lower-triangular elements of each participant’s neural RSM were vectorized and correlated with the corresponding lower-triangular elements of the category model RSM using Spearman correlation. This produced a single similarity estimate for each participant and ROI. To test whether neural similarity structure significantly reflected categorical organization, one-sample one-tailed t-tests were conducted across participants separately for each ROI, testing whether cRSA similarity estimates were greater than zero.

      For tRSA, similarity structure was quantified at the stimulus level. For each participant, ROI, and stimulus, the corresponding row of the neural RSM was correlated with the matching row of the category model RSM, excluding self-comparisons. This produced trial-level similarity estimates for each stimulus within each ROI and participant. Trial-level effects were analyzed using mixed-effects models with random intercepts Participant and Item.

      False discovery rate (FDR) correction was applied separately to cRSA and tRSA analyses across the 10 ROIs using the Benjamini–Hochberg procedure (q < .05).

      Results

      Both cRSA and tRSA revealed reliable category-level similarity structure across ventral visual regions. However, across ROIs, tRSA produced effect sizes and statistical significance that were comparable to, and in several regions slightly larger than, cRSA. The strongest effects were observed in bilateral pVTC and early visual regions. In right pVTC, both methods produced highly robust category-model fits (cRSA: t = 5.46, tRSA: t = 5.47). Similarly strong effects were observed in right V1 (cRSA: t = 5.18, tRSA: t = 5.35) and right V2 (cRSA: t = 5.65, tRSA: t = 5.32). Both methods detected significant positive effects following FDR correction.

      Across ROIs, cRSA and tRSA estimates were highly correlated, indicating strong agreement between the two approaches in the spatial distribution of representational similarity effects. Nevertheless, tRSA consistently enhanced statistical sensitivity while additionally modeling trial-level variance and hierarchical random effects. Overall, these findings are consistent with our main findings that tRSA reproduces the canonical category-level similarity organization previously observed along the ventral visual stream while providing a more flexible inferential framework.”

      (R2.3) Moreover, the cells of an RDM/RSM reflect pairwise comparisons between response patterns. Because the response patterns are repeatedly compared, the cells of this matrix are not independent of one another. While the authors show examples that failure to meet independence assumptions do not affect results in their specific dataset, it does not get acknowledged as a problem at a more fundamental level.

      We agree that individual cells within an RDM/RSM are not statistically independent because each trial contributes to multiple pairwise comparisons. This dependency is an inherent property of representational similarity matrices and is shared by both classical RSA and our proposed tRSA approach. Importantly, however, our mixed-effects model does not use individual RDM cells as observations. Instead, each observation corresponds to a row-wise correlation between the neural and model RSMs, which summarizes the representational structure associated with a single stimulus. Each row-wise correlation is computed across all pairwise similarities involving that stimulus (excluding the diagonal and, where applicable, within-run comparisons), thereby reducing the pairwise information to a single trial-level summary statistic. We acknowledge that these row-wise correlations are themselves not completely independent because different rows share many of the same pairwise similarity values. Rather than requiring complete independence among row-wise observations, our linear mixed-effects model accounts for participant- and stimulus-level sources of variability while acknowledging that row-wise observations retain some dependence because they are derived from a common RSM. Consequently, inference is based on variation across participants and stimuli rather than treating every pairwise comparison as an independent observation.

      More importantly, while this shared-information structure remains a characteristic of RSM-based analyses, our simulations and empirical validation demonstrate that it does not produce inflated false-positive rates or qualitatively alter statistical conclusions relative to conventional RSA. We discuss this issue in the limitations and advise readers to assess their covariance structure and perform permutation-based testing where applicable. We have also added such permutation-based testing on our main real data and simulation data. We have also added this in-principle limitation to our Discussion.

      “One limitation of the proposed tRSA framework is that row-wise correlations are derived from a common representational similarity matrix and therefore are not strictly independent. This dependency is inherent to analyses based on representational similarity matrices and is not unique to tRSA. Although our linear mixed-effects model accounts for major sources of dependence through random effects for participants and stimuli, the shared-information structure among row-wise observations may vary across datasets and experimental designs. In the present study, simulations, empirical analyses, and additional permutation-based tests demonstrated that this dependency did not inflate false-positive rates or meaningfully alter statistical conclusions. Nevertheless, we recommend that researchers applying tRSA evaluate the covariance structure of their own data and, where appropriate, complement mixed-effects analyses with permutation-based inference to verify the robustness of statistical conclusions.

      These diagnostics supported the assumptions of normality, homoscedasticity, and conditional independence of residuals. In addition, we conducted permutation-based inference, similar to prior improvements to cRSA (Nili et al., 2014), using a nested model comparison to test whether the mean similarity in this ROI was significantly greater than zero. The observed likelihood ratio test statistic fell in the extreme tail of the null distribution (Appendix 3, Figure 14), providing strong nonparametric evidence for the reliability of the observed effect. We emphasize that this type of model checking and permutation testing is not merely confirmatory but can help validate key assumptions in RSA modeling, especially when applying mixed-effects models to neural similarity data.

      See also R2.3 for the public comment addressing this concern. Nevertheless, because mixed-effects models may not fully account for all forms of dependence or model misspecification, this issue remains a consideration in principle. In settings where assumptions about the error structure are uncertain or difficult to verify, permutation-based inference provides a valuable complementary approach because it does not rely on parametric assumptions and can offer more robust significance testing.”

      (R2.4) Finally, while the paper now states that 'simulations and example tRSA code' are publicly available, the link points to the lab's general GitHub page containing many lab repositories, in which I could not identify a specific repository related to this paper. A dedicated repository, including documentation, READMEs and tutorials/demo's to run simulations, compare methods, etc., would greatly enhance the paper's contribution.

      We apologize for this oversight, and have added a more specific reference to code and a tutorial for tRSA to the Methods: https://github.com/ElectricDinoLab/Trial-level-RSA

      (R2.5) The authors seem to have confused two King et al. papers here; the paper I was referring to before was by King, Groen, Steel, Kravitz and Baker (2019) (for which I provided the full citation at the end of my review); not to the TICS paper on temporal generalization by King & deHaene (2014), which I would agree is not relevant for the current study. Figure 8B in King et al., (2019) includes a plot of the correlations between individual rows of a brain-based RDM and a behavioral RDM (not at single-trial level but at category level).

      King, M. L., Groen, I. I., Steel, A., Kravitz, D. J., & Baker, C. I. (2019). Similarity judgments and cortical visual responses reflect different properties of object and scene categories in naturalistic images. NeuroImage, 197, 368-382.

      I suggest removing the newly introduced section on temporal generalization referencing King & DeHaene, 2014, and instead give credit to the paper above when referencing prior work that has considered RDMs at the individual row level.

      We apologize for the incorrect citation. We have included the appropriate reference to the individual row correlations from the King 2019 paper.

      Recommendations for the authors:

      Reviewer #2 (Recommendations for the authors):

      (R2.6) The authors are stepping a bit too lightly [previous reviewer comment R2.4/R2.10] over my suggestion to demonstrate the utility of their proposed tRSA method on another dataset than just their own. Even if the dataset they use here consists of two different tasks, it's data from the same participants in the same experimental setting. Since the authors intend here to 'formally introduce' tRSA and argue, repeatedly, that tRSA offers advantages over classic RSA (or at least no disadvantages) beyond the specific setting of their study, it would be good to support that with at least one application to a different dataset.

      Please see R2.2 for our new application to a different dataset.

      (R2.7) Also here, I felt like the author's response [to Reviewer comment R2.5] was not entirely adequate. The matter of the non-independence of cells in an RSM/RDM is not an empirical matter (i.e. something that 'could happen' in the experiment due to issues with uneven sampling or noise in the measurements) but is a principled ‘given’, because the values of these cells are computed from pairwise comparisons of a set of response patterns (or model features). Even if these patterns are independent from one another, their pairwise comparisons are not, because they involve repeatedly comparing the same patterns; stimulus A with stimulus B, stimulus A with stimulus C, etc; hence the correlation between A-C is also related to the correlation between A-B. This is also why the first simulation of the original manuscript (now moved to the Appendix) is an invalid simulation; due to the way the cells of the RSMs are computed, they cannot be independent random measurements. I would like the authors to explicitly discuss why they, given this property, believe it is valid to enter the cells of an individual row as an entry into an LMM model, instead of using e.g. non-parametric, permutation-based testing that does not assume independence.

      While we understand the reviewer’s concern that the concern is not merely empirical, but in principle, we would like to stress that the novelty in approaching RSA in a trialwise manner extends RSA to the trial level, enabling behaviorally relevant inferences that are not possible with cRSA. The row-wise observations derived from the neural RSM are not fully independent within subjects, and we think careful model construction is required to account for this and meet model assumptions. Furthermore, our VIF analyses indicated low multicollinearity among predictors, and permutation testing supported the robustness of our statistical inference. These analyses also supported the assumptions of normality, homoscedasticity, and conditional independence of residuals. Nonetheless, we acknowledge this concern and have added text to the Limitations along with our permutation-based testing.

      “These diagnostics supported the assumptions of normality, homoscedasticity, and conditional independence of residuals. In addition, we conducted permutation-based inference, similar to prior improvements to cRSA (Nili et al., 2014), using a nested model comparison to test whether the mean similarity in this ROI was significantly greater than zero. The observed likelihood ratio test statistic fell in the extreme tail of the null distribution (Appendix 3, Figure 14), providing strong nonparametric evidence for the reliability of the observed effect. We emphasize that this type of model checking and permutation testing is not merely confirmatory but can help validate key assumptions in RSA modeling, especially when applying mixed-effects models to neural similarity data.

      See also R2.3 for the public comment addressing this concern. Nevertheless, because mixed-effects models may not fully account for all forms of dependence or model misspecification, this issue remains a consideration in principle. In settings where assumptions about the error structure are uncertain or difficult to verify, permutation-based inference provides a valuable complementary approach because it does not rely on parametric assumptions and can offer more robust significance testing.”

      See also our response to R2.3.

      (R2.9) In the Introduction p3, the authors now argue that tRSA is necessary because other proposed improvements require stimulus repetition 'to examine the representational structure'. It would be more accurate to say that stimulus repetition is used to separate estimates of (measurement) noise from the true underlying neural pattern (as explained by reviewer 1). It would be good if the paper makes more explicit why tRSA does not suffer from the problem that it is impossible to separate noise from signal for an individual trial.

      We thank the reviewer for this important clarification. We agree that the primary motivation for repeated stimulus presentations in several RSA approaches is not simply to "examine representational structure," but rather to improve estimates of the underlying neural response by separating measurement noise from the true signal. We have revised the Introduction to reflect this distinction.

      Importantly, tRSA does not overcome the fundamental limitation that single-trial activation estimates contain measurement noise, nor do we intend to suggest that it recovers a noise-free representation from a single presentation. Rather, tRSA takes a different analytical approach and treats noisy single-trial estimates of neural activity as observations to estimate representational structure. The mixed-effects framework then models the relationship between neural and model representational similarity across participants and stimuli, allowing population-level inference while accommodating trial-to-trial variability.

      To make this distinction clearer, we have revised the Introduction to clarify the aim of stimulus repetition approaches.

      “Further, model comparison RSA strategies (Diedrichsen et al., 2021) and generalization techniques across stimuli and participants (Schütt et al., 2023) have improved sensitivity and inference. Nevertheless, a common feature shared across most of these improvements is that they require stimuli repetition to separate estimates of noise from the underlying neural activity patterns.”

      We also clarified the aim of tRSA and included the principled concern in the Discussion.

      “Additionally, the multi-level structure of RSA measures introduces potential dependencies across subjects, stimuli, and trials, which can violate assumptions of independence if not properly modeled. In the present study, we used a model that included random intercepts for both subjects and stimuli, which accounts for variance at these levels and improves the generalizability of fixed-effect estimates. Still, there is a potential for systematic dependence across trials within a subject. To ensure that the model assumptions were satisfied, we conducted a series of diagnostic checks on an exemplar ROI (right LOC; middle occipital gyrus) in the Object Perception dataset, including visual inspection of residual distributions and autocorrelation (Appendix 3, Figure 13). Unlike approaches that rely on repeated stimulus presentations to improve estimates of the underlying neural response, tRSA does not seek to recover a noise-free representation for each individual trial. Single-trial activation estimates inevitably contain measurement noise, and this limitation is shared by any analysis based on single-trial fMRI estimates. Instead, tRSA treats these estimates as noisy observations of representational structure and leverages mixed-effects modeling to estimate the relationship between neural and model representational similarity across participants and stimuli. Consequently, the method does not eliminate measurement noise but rather accommodates it within the statistical model, allowing population-level inferences without requiring repeated stimulus presentations.”

      (R2.10) I'm not sure I agree with the author's definitions in the newly added footnote 1 (bottom of page 4), namely that estimating 'representational geometry' necessarily uses stimulus repetition and model comparison; in my understanding, representational geometry just refers to the notion that neural (or model) representations of stimuli can be thought of as points/vectors in a high-dimensional representational space, with 'geometry' capturing the spacing between these points/vectors altogether (cf Kriegeskorte and Kievit, 2013, Figure 1A). The main difference between cRSA and tRSA then is that cRSA considers the geometry of all stimuli simultaneously, whereas tRSA focuses on one stimulus vs. all others at a time. Representational strength on the other hand, refers to the correlation between the geometry of one model system (e.g. brain data) versus the another (a hypothesized cognitive model), i.e. what Fig 1 in the manuscript refers to as first-level RSA.

      We now clarify that cRSA does not rely on repetition. We also clarify that this is how we define representational strength, and that the term has been used differently in the literature. 

      “Representational geometry refers to the pattern of similarities or dissimilarities among stimuli in a representational space, as captured by a representational similarity (or dissimilarity) matrix (Kriegeskorte & Kievit, 2013). This concept is independent of how the representational space is estimated and does not inherently require repeated stimulus presentations. Throughout this paper, we use the term representational strength to refer to the degree of correspondence between a neural representational geometry and a hypothesized model RSM (i.e., the first-level RSA correlation). We note that the term representational strength has been used differently in other contexts, and our definition is adopted here for clarity.”

      (R2.11) Similarly, it would be good to clarify why the authors think that 'testing of competing conceptual models' (Discussion, page 46) could not be done with a regular full-matrix cRSA comparison. In the example mentioned here - testing whether neural representations are more driven by taxonomic vs. encyclopedic features - it seems to me one could create a stimulus set in which these two features would very different predictions of the overall representational geometry (i.e., all the pairwise distances), i.e. RSM_tax and RSM_enc. If the RSM_brain then has a higher cRSA score with RSM_tax than RSM_enc (on average across all subjects), the two competing conceptual models are adjudicated, right? What does doing this at the row-by-row level add in terms of interpretation/result, in this context?

      We agree that conventional cRSA can compare competing representational models, and this was not our intended implication. We have revised the Discussion to clarify that the advantage of tRSA is not model comparison per se, but rather the ability to model trial- and stimulus-level predictors within a hierarchical regression framework while comparing representational models.

      “At a broader level, the tRSA approach also engenders a host of other innovative techniques. While a number of studies have addressed the validity of measuring representational geometry using designs with multiple repetitions, a conceptual benefit of the tRSA approach is the reliance on a regression framework that allows competing conceptual models of stimulus representation to be evaluated while simultaneously modeling trial- and stimulus-level predictors within a hierarchical framework (e.g., taxonomic vs. encyclopedic semantic features, as in Davis et al., 2021).”

      (R2.12) Small point: The Sucholutsky et al. (2025) reference ("Getting aligned on representational alignment") is missing from the reference list. Here's the full citation:

      Sucholutsky I, Muttenthaler L, Weller A, Peng A, Bobu A, Kim B, Love BC, Cueva CJ, Grant E, Groen IIA, Achterberg J, Tenenbaum JB, Collins KM, Hermann KL, Oktar K, Greff K, Hebart MN, Cloos N, Kriegeskorte N, Jacoby N, Zhang Q, Marjieh R, Geirhos R, Chen S, Kornblith S, Rane S, Konkle T, O'Connell TP, Unterthiner T, Lampinen AK, Müller K-R, Toneva M, Griffiths TL (2025). Getting aligned on representational alignment. Transactions on Machine Learning Research (TMLR), https://openreview.net/forum?id=Hiq7lUh4Yn

      We have corrected this citation.

    1. Author response:

      The following is the authors’ response to the original reviews.

      We thank the reviewers for the thorough assessment of our manuscript. In the revised manuscript, we have addressed the majority of the concerns, as indicated below. Major changes include:

      - New data on expression levels of NOTCH and its transcriptional targets arising from new analysis of teratoma scRNA-seq data (Supplementary Figure 7 in the revised manuscript).

      - The original Supplementary Figure 6 has now been divided into Supplementary Figures 6 and 8 in the revised manuscript.

      - We have added a new author on the manuscript, Hannah Dada, who helped with analysis of scRNA-seq data.

      eLife Assessment:

      In this important study, Bready et al. investigate how a highly conserved long-range enhancer mediates neural-specific SOX2 regulation during neural differentiation using human neural stem cells. This study has broad appeal to developmental neuroscience; however, the data remain incomplete given the need for homozygous enhancer knockouts and biological replicates in the scRNAseq assays.

      We thank the expert reviewers and eLife editors, for complimenting our work and deeming it an “important study” of “broad appeal to developmental neuroscience”. We also acknowledge some of the limitations of our work, including the lack of homozygous deletion of the enhancer element. As we detail below, we tried tirelessly to identify human embryonic stem cell (hESC) clones with homozygous deletions but were unable to. As we speculate in the discussion, this failure may represent a biological property of the enhancer element (possibly an essentiality manifested even in hESCs), or a technical limitation related to the large size (2.7 kb) of the genomic element targeted for deletion. We also clarify that every scRNA-seq assay included cells from multiple teratomas.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      In this study, the authors examine how a developmentally regulated cis-regulatory element controls SOX2 expression during neural differentiation of human stem cells. The results suggest that this highly conserved long-range enhancer mediates neural-specific SOX2 regulation and offer insight into the role of promoter-enhancer contacts in this process. Although the findings are interesting, several limitations need to be addressed.

      Strengths:

      A central question in developmental biology is how genes are regulated in a context-dependent manner. SOX2, a major pluripotency factor, is expressed in diverse tissues during development, and therefore understanding the mechanisms that control its spatiotemporal expression is critical. This study addresses this important question by examining the functional relevance of a neural-specific, developmentally regulated SOX2 enhancer and its associated promoter-enhancer contacts in driving gene expression during human neural development. Using multiple model systems and techniques, the authors test the requirement of this enhancer by analyzing SOX2 expression in mutant lines, providing evidence for its role in this process.

      We thank the reviewer for highlighting the significance of our work in the field of developmental biology.

      Weaknesses:

      A key limitation of the study is the absence of data from homozygous SOX2 enhancer deletion, which leaves the analysis incomplete and tempers the conclusions that can be drawn. Furthermore, the suitability of teratomas as a model system is questionable, given their limited capacity to recapitulate the spatial patterning, regional specification, and organized developmental processes characteristic of the human forebrain. Finally, the manuscript remains largely descriptive with little mechanistic insight.

      We appreciate the reviewer’s disappointment with lack of data from a homozygous SOX2 enhancer deletion. We too felt disappointed when we started genotyping our hESC clones. In fact, we spent a year screening multiple hESC clones for a homozygous deletion but were unable to find one. We performed several assays to better characterize the heterozygous clones, including Sanger sequencing, whole-genome sequencing (WGS) and fluorescent in situ hybridization (FISH). All assays pointed in the direction of hemizygous deletion. We do not understand the reasons for the absence of homozygous deletion clones. One possibility is that homozygous deletion of the enhancer is selected against in hESCs, thus preventing growth of colonies. Another possibility is the technical challenge of achieving a large deletion (2.7 kb) in hESCs. We also entertained the possibility of the excised enhancer being excised from the genome but retained as extrachromosomal (ec) DNA, thus producing the hemizygous genotype. However, several assays, such as FISH and PCR diagnostics, argued against this possibility.

      The teratoma assay was chosen as an in vivo metric of spontaneous differentiation of hESCs into the three germ layers, because our overarching hypothesis was that perturbing the enhancer element and 3D chromatin loop regulating SOX2 transcription would impair specification of neuroectodermal precursors. We believe that teratomas offer an opportunity to allow pluripotent cells to declare any predilections toward germ layers in unbiased fashion. Importantly, we did not rely solely on teratomas to assess effects of our genomic perturbations on specification of neuroectoderm, but also pursued cerebral organoids as an orthogonal approach focused on the tissue of interest, the central nervous system.

      Our work does not only describe an important mechanism for regulation of SOX2 transcription in the transition from pluripotency to neuroectodermal specification, but also provides mechanistic insight into the question of whether the developmentally co-regulated activation of the enhancer and formation of the 3D chromatin loop are dependent on each other. Our findings indicate that the two processes occur independently of each other, as evidenced by the fact that the enhancer is uncoupled from chromatin folding, as occurs when the adjacent CTCF motif is deleted. This finding raises the possibility that enhancer activation occurs through yet-to-be-determined transcriptional events, and that establishment of the local 3D chromatin architecture helps fine-tune its influences in the Topologically Associating Domain (TAD) of interest.

      We are further pursuing mechanisms that regulate activation of the enhancer within neuroectodermal lineages and may explain its actions on genomic elements other than the SOX2 locus within the relevant TAD. We are also investigating reasons explaining why hemizygous enhancer deletion produces stronger phenotypes than deletion of the CTCF motif that helps stabilize the 3D chromatin loop.

      Reviewer #2 (Public review):

      Summary:

      The authors use a combination of genomics, genome conformation assays, and CRISPR-mediated deletion to study the transcriptional regulation of the SOX2 gene in human neural stem cells (hNSCs).

      Strengths:

      The authors show that two distal elements, located ~550 kb downstream of the SOX2 gene, are important for SOX2 transcription in hNSCs. They investigate both the deletion of these elements in established hNSCs and in hNSCs generated by differentiation of human pluripotent stem cells, suggesting these elements are important in both the establishment and maintenance of SOX2 expression in hNSCs.

      We thank the reviewer for appreciating the importance of this regulatory mechanism in the establishment and maintenance of SOX2 expression in the human neural lineage.

      Weaknesses:

      Homologous elements have been studied in the mouse genome and have conserved function in mouse NSCs, yet these findings are not mentioned. Inclusion of biological replicates for the scRNA-seq and replicate CRISPR-deleted clones would strengthen the study.

      We appreciate the recommendation of the reviewer to better acknowledge prior work in mouse neural development. We have ensured full acknowledgement of these studies in the revised manuscript.

      We also appreciate the suggestion for biological replicates in our scRNA-seq assays. We clarify that each scRNA-seq arose from combining multiple teratomas from each experimental group, thus ensuring that findings reflect reproducible biology rather than isolated findings from single teratomas. This clarification will be emphasized in the revised manuscript.

      Finally, we absolutely agree with the reviewer that more CRISPR-deleted clones would have strengthened the study. Unfortunately, we realized that characterization of each clone takes multiple years and addition of more clones would have made the study too lengthy.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      Major weaknesses:

      (1) A major weakness is the lack of data from homozygous Sox2 enhancer deletion, which leaves the analysis incomplete and weakens the conclusions.

      We agree with the reviewer that the homozygous enhancer deletion would be ideal, but we were unable to generate it unfortunately, as explained above.

      (2) The capacity of teratomas as a model to accurately replicate spatial patterning, regional specification, and organized human forebrain developmental processes is questionable, raising doubts about their appropriateness for this purpose.

      As discussed above, the teratoma assay was chosen as an in vivo metric of spontaneous differentiation of hESCs into the three germ layers, because our overarching hypothesis was that perturbing the enhancer element and 3D chromatin loop regulating SOX2 transcription would impair specification of neuroectodermal precursors. We believe that teratomas offer an opportunity to allow pluripotent cells to declare any predilections toward germ layers in unbiased fashion. Additionally, we did not rely solely on teratomas to assess effects of our genomic perturbations on specification of neuroectoderm, but also pursued cerebral organoids as an orthogonal approach focused on the tissue of interest, the central nervous system.

      (3) I appreciate the authors' effort to rigorously characterize SOX2 expression. However, it is not clear how a 30% reduction in SOX2 protein levels (and a 50% reduction at the RNA level, Figure 2F, G) is sufficient to produce the observed phenotype. This relationship requires further explanation or supporting data.

      We agree with the reviewer that is a very interesting question, which can essentially be rephrased as: why does SOX2 haploinsufficiency generate these phenotypes? Our Discussion section utilizes clinical data to answer this concern. In humans, haploinsufficiency of transcription factors SOX2 and FOXG1 results in developmental abnormalities. Therefore, complete loss of SOX2 is not required for the manifestation of these phenotypes – reduced expression is sufficient to perturb neural development.

      (4) The manuscript is largely descriptive and lacks mechanistic insight. The authors do not address the downstream transcriptional targets altered in the mutants in detail. For instance, is Notch signaling, a well-known target of Sox2, altered in the enhancer or CTCF motif deletions?

      We thank the reviewer for suggesting this analysis. We have reanalyzed our teratoma scRNA-seq data (Supplementary Figure 7 of the revised manuscript). Our analysis shows reduced expression of NOTCH1 and several of the Notch pathway transcriptional targets (HES and HEY genes) in neural lineages within teratomas.

      (5) There appears to be a discrepancy between the phenotypes resulting from the CTCF site mutation versus the Sox2 enhancer deletion. This difference is particularly evident in the teratoma single-cell data, where cell composition differs substantially between the two conditions (Figure 3E). This is also apparent in the analysis of the FOXG1 gene (Figure 4B), where FOXG1 expression in forebrain neurons appears to be increased in the CTCF motif mutant.

      We agree that the phenotypes of the two genetic perturbations are not identical, with differences manifesting in several assays, including the scRNA-seq cellular clusters (Figure 3E). However, expression of both FOXG1 and EMX2 is decreased in forebrain progenitors within the DHS1332 and Dnmotif conditions relative to control (Figure 4B).

      (6) The ChIP-seq data of H3K27ac and H3K27me3 are confusing and insufficiently explained. It is unclear how the seemingly aberrant deposition of H3K27me3 within the Sox2 locus in the enhancer mutant relates to Sox2 expression reduction and the subsequent observed phenotype. Furthermore, Figure 4 suggests that there is no contact between the Sox2 promoter and the H3K27me3-marked region, making the proposed mechanism unclear.

      We agree that these findings are interesting and mechanistically difficult to explain given the lack of 3D contacts between the enhancer and these H3K27me3 peaks. This is a question that merits future investigation.

      Minor Weaknesses:

      (1) The analysis provided in Figure 1 is framed as a major finding. However, this Sox2 enhancer is already well established and extensively characterized by Hi-C data (for instance: PMID: 29053968 and PMC6842117- either not cited), including data previously published by the authors themselves (PMCID: PMC5687844). As such, Figure 1 does not present a novel finding and would be more appropriate as a supplementary figure.

      We thank the reviewer for this suggestion. We have included these citations in the revised manuscript. We believe the data presented in Figure 1 lay the groundwork for the experimental dissection of the proposed mechanism and therefore plays an important role in the manuscript.

      (2) It is unclear why the authors chose to focus specifically on HS1332, given that it represents only a portion of the enhancer (Figure 1A) and not the entire enhancer region.

      We also tried to delete the entire enhancer element (HS1332 and HS1332b), but were unable to do so. We speculate that our failure is explained by a) technical reasons relating to the larger size of the deletion; or b) deleterious effects in hESCs.

      (3) Figure 1E appears to be a reproduction from the authors' original work with very minor modifications (PMID: 29053968), but this is not clearly stated or properly referenced.

      The graphic in Figure 1E is not identical to the one in the Modrek et al. manuscript. It has been modified to represent the hypothesis tested in this manuscript.

      (4) Virtual 4C analysis is not described in the Methods section, despite being presented in the Results.

      Virtual 4C has been added as a method in the revised manuscript.

      (5) The manuscript is overly technical, particularly in the description of how the HS1332 deletion was generated. These details would be more appropriately placed in the Methods section.

      We chose to include some of these details in the body of the manuscript in order to help the reader understand some of the challenges in testing clones for the intended genetic alterations.

      (6) The conclusion that the enhancer is "critical for forebrain development" (line 221) is overstated. Changes in only a couple of genes are insufficient to support such a strong claim. Additionally, teratoma is not a good model for studying forebrain development due to its cellular heterogeneity.

      We have changed the language to “These findings suggest that the HS1332 enhancer and the associated chromatin loop contribute to neuralization, and particularly forebrain development”. As stated above, we think that teratoma is a good assay to understand germ layer preferences of hESC carrying the genetic perturbations of interest. Additionally, we performed assays in cerebral organoids to specifically study neural development.

      (7) The yellow and gray highlights in Figure 5 are not described in the figure legend and should be clarified for better interpretation.

      The figure legend explains the highlights in the revised manuscript.

      (8) The criteria for assessing rosette formation in Figure S6 are unclear. Specifically, it is not stated whether quantification was based on rosette number, size, or both.

      The criterion here was the qualitative presence or absence of neural rosettes on H&E stain of teratoma tissue. This assessment was performed by blinded pathologists. This is now stated in the Methods section of the revised manuscript.

      Reviewer #2 (Recommendations for the authors):

      Major Points:

      (1) In the first section of the results, starting at line 85, the authors fail to mention that interaction between the HS1332 equivalent and Sox2 has been shown in mouse NSCs in vitro (PMID: 29053968, PMID: 27152443) and in vivo (PMID: 36717694). Furthermore, in mouse NSCs homozygous deletion of this element, termed DNE, has been shown to greatly affect Sox2 expression (PMID: 36717694). This needs to be made clear in this section and/or the introduction.

      We appreciate this suggestion. We acknowledge this work in the Results and Discussion.

      (2) It appears there are no replicates in the scRNA-seq or any biological replicates of the deletions. The use of SNPs to show disruptions to expression on the deletion-linked vs intact allele would strengthen the work.

      The scRNA-seq analysis included cells from multiple teratomas. We appreciate the suggestion to use SNPs to differentiate between the alleles linked to the deleted enhancer vs. their wild-type counterparts, but we have been unable to do it unfortunately.

      (3) The observed Impaired Forebrain Specification after deletion of HS1332 is similar to the observed disruption to forebrain specification in mouse NSCs with a deletion of a proximal enhancer cluster in Tobias et al. 2025 (PMID: 39849901). Although this paper is cited, the similarities in observed phenotype after Sox2 enhancer deletion are not mentioned. This needs to be commented on in the discussion.

      We appreciate this suggestion. The Tobias et al. paper is discussed and cited in the revised manuscript.

      (4) DHS1332 is incompletely genotyped. The integrity to the WT allele needs to be shown.

      We agree that the integrity of the wild-type allele in the DHS1332 condition is not shown directly but can be inferred from the WGS in Supplementary Figure 2B.

      (5) DnMotif may overlap the mouse VISTA element mm639, if this is the case then this needs to be clearly stated when the region is first introduced. Also, indicate that this VISTA element did not show activity in the developing nervous system.

      We thank the reviewer for this astute observation, which we included in the revised manuscript.

      (6) The authors suggest that the size of the deletion may contribute to the lack of homozygous clones obtained for HS1332 or that the region is required in hESCs. "The reason that we were able to achieve only a hemizygous but not a homozygous deletion of the HS1332 is unclear. The size of the genomic sequence targeted for deletion, 2.7 kb, may be a contributing factor in reducing the efficacy of the excision. Alternatively, it is possible that homozygous deletion of the enhancer is deleterious to hESCs." Neither one of these explanations is very satisfying, as much larger deletions have been conducted successfully with CRISPR, and the element appears inactive in hESCs. Also suggested is, "An alternative explanation is that this enhancer regulates multiple elements within the TAD beyond just the SOX2 gene". This is a completely testable hypothesis as there are few genes within the SOX2 TAD. Testing this with SNP-sensitive primers would be the best approach, as changes to the trans-regulatory state associated with low SOX2 could confound these findings.

      We agree with the reviewer that the possibility that the enhancer regulates multiple elements within the TAD is an intriguing hypothesis, which we hope to test in the future.

      Minor Points:

      (1) At Line 47: the authors state "topologically associating domains (TADs), which are 0.5-1.0 Mb-long chromatin 47 loops that facilitate intra-loop 3D contacts3,4" This is incorrect, TADs are not loops, they are interacting domains, loops show less interaction within the loop compared to the loop ends, TADs show increased interactions within the TAD compared to outside of the TAD.

      We thank the reviewer for this correction. We have modified the text accordingly in the revised manuscript.

      (2) "In mice, the analogous enhancer is approximately 450 kb telomeric to SOX2 and displays a robust degree of conservation" - add reference to PMID: 36717694, which studies this region in mouse development and in NSCs.

      We thank the reviewer for pointing this out. We have cited this manuscript, as suggested.

      (3) "We discovered that in hESCs the SOX2 locus does not form strong 3D contacts with other elements within the TAD and the HS1332 enhancer is silent but not repressed, as suggested by lack of facultative repressive H3K27me3 modifications." Similar observations were made in mouse cells, add reference to PMID: 29053968, PMID: 27152443, PMID: 36717694 here.

      We thank the reviewer for this suggestion. These references have been cited in the revised manuscript.

    1. Author response:

      The following is the authors’ response to the previous reviews.

      Public Reviews:

      Reviewer #3 (Public review):

      Combining a five-year field experiment with a global meta-analysis, Wu et al. investigate how grazing intensity influences ecosystem carbon dioxide (CO<sub>2</sub>) fluxes in grasslands and how these effects are regulated by environmental conditions such as grazing duration, wetness index, and soil temperature and moisture responses.

      The authors show that the response of net ecosystem productivity (NEP) to light grazing shifts from negative to positive along a wetness gradient, whereas heavy grazing consistently suppresses NEP across wetness conditions. Importantly, this pattern is supported by both the field experiment and the meta-analysis, suggesting that may help maintain moderate levels of grazing can potentially enhance both plant productivity and carbon sequestration under favorable moisture conditions.

      The integration of experimental data with a global synthesis is a particular strength of the study, allowing the authors to evaluate grazing impacts across both temporal variability (precipitation fluctuations in the field experiment) and spatial variability (wetness gradients across global grasslands). Overall, the conclusions are well supported by the data.

      Overall, the principal conclusions are generally supported by the reported results, and the study provides useful evidence that the effects of grazing on grassland carbon cycling depend on both grazing intensity and environmental context. The comparison between field and synthesis results is potentially valuable for understanding why grazing effects vary among grassland systems. However, some aspects of the meta-analysis remain insufficiently documented. In particular, the study-selection numbers presented in the new PRISMA diagram require clarification, and the manuscript does not clearly explain how individual response ratios were weighted when estimating the pooled effect sizes. Resolving these reporting and methodological issues would improve the reproducibility and interpretation of the synthesis.

      Thank you for the recognition of the manuscript and the constructive comments. The meta-analysis has been clarified in the revised manuscript to improve the reproducibility and interpretation of the synthesis.

      Recommendations for the authors:

      Reviewer #3 (Recommendations for the authors):

      (1) Literature search and screening: The literature-search and screening process remains unclear. The Methods report searches in Web of Science and CNKI, whereas the PRISMA diagram (Fig. S9) also lists Google Scholar. In addition, removing 7,883 duplicates from 10,586 records retrieved from only two or three databases seems unusually high and requires verification or explanation. The reasons for excluding 429 articles between full-text screening and eligibility assessment, followed by a further 142 articles before the final inclusion of 62 studies, are also unclear. Please report the number of records retrieved from each database and the number of full-text articles excluded for each specific reason.

      Thank you for the comment. We have supplemented Google Scholar as one of the literature search databases in the revised manuscript. The relatively large number of duplicate records mainly resulted from our use of multiple search terms and combinations of these terms in several rounds of literature searches. Considerable overlap occurred among the records retrieved using different search strategies, and duplicate records were also identified across different literature sources. Consequently, a relatively high proportion of duplicate records was generated during the literature search process. In addition, we have further clarified the specific reasons for study exclusion and the corresponding numbers of excluded articles at each stage of the screening process. Of the 633 articles that entered the full-text screening stage, 429 were excluded because they did not meet the eligibility criteria related to the grazing topic. The remaining 204 articles were further assessed for eligibility based on the carbon-flux-related criteria. Studies were excluded for reasons including unavailable data, simulated (e.g. clipping or mowing) rather than actual grazing treatments, meta-analyses or review articles, insufficient information on experimental design, flux-tower-based studies, fewer than three replicates, and studies in which the reported carbon flux represented soil respiration rather than the carbon flux variables considered in our analysis. Ultimately, 62 studies met all eligibility criteria and were included in the final analysis. We have now explicitly listed the reasons for exclusion and the corresponding numbers of articles in the revised PRISMA flow diagram (Fig. S9) and have provided the corresponding clarification in the Methods section of the revised manuscript.

      “To assess the effects of grazing on GPP, ER, and NEP in global grasslands, we conducted a systematic literature search for relevant papers published up to June 8, 2025, using the Web of Science (http://apps.webofknowledge.com/), China National Knowledge Infrastructure (CNKI, https://www.cnki.net) and Google Scholar (https://scholar.google.com/).”

      (2) Weighting of response ratios: The revised description clarifies that RR<sub>++</sub> represents the estimated model intercept, but it remains unclear how individual response ratios were weighted in the mixed-effects model. Including study as a random effect accounts for non-independence among observations from the same study but does not itself weight effect sizes by their sampling precision. Please report whether a weighting variable was supplied to the lmer model and explain how the sampling variance of each response ratio was incorporated. If the model was not weighted, the terms "weighted response ratio" and RR<sub>++</sub> should be reconsidered, and the implication s for the meta-analysis should be addressed.

      Thanks for the comment. In the meta-analysis, observations were weighted by sample size, with the weights calculated according to Equation (4). In addition, we confirm that the calculated weights were incorporated into the lmer models. For example, the R code used for the GPP analysis was:

      GPP <- lmer (GPP_RR ~ 1 + (1|Site), weights = GPP_Wr, data=dat1)”

      We have made following changes in the revised manuscript as follows:

      “The weighing of each observation (W<sub>RR</sub>) was calculated as (Pittelkow et al., 2015):

      Where N<sub>T</sub> and N<sub>c</sub> are the replicate numbers of treatment and control, respectively.”

      (3) R package citations: The package references do not appear to have been fully updated. For example, "ez" should be cited as Lawrence (2026), ez: Easy Analysis and Visualization of Factorial Experiments*, R package version 4.5-0; "lme4" should be cited as Bates et al. (2015), "Fitting Linear Mixed-Effects Models Using lme4," *Journal of Statistical Software*, 67(1), 1-48. Please use `citation()` in R to obtain the recommended citation for each package.

      Thank you for the comment. The citation formats are provided below:

      Archer E. (2025) rfPermute: Estimate Permutation p-Values for Random Forest Importance Metrics. R package version 2.5.5 https://CRAN.R-project.org/package=rfPermute

      Bates, D., Mächler, M., Bolker, B., & Walker, S. (2015) Fitting Linear Mixed-Effects Models Using lme4. J Stat Softw 67: 1–48. https://doi.org/10.18637/jss.v067.i01

      Canty A, Ripley B. (2025) boot: Bootstrap Functions. R package version 1.3-32 https://CRAN.R-project.org/package=boot.

      Lawrence, M. A. (2026) ez: Easy Analysis and Visualization of Factorial Experiments. R package version 4.5-0 https://CRAN.R-project.org/package=ez

      Lefcheck, J.S. (2016) piecewiseSEM: Piecewise structural equation modelling in r for ecology, evolution, and systematics. Methods Ecol Evol 7: 573-579 https://doi.org/10.1111/2041-210X.12512

      Liaw, A., & Wiener, M. (2002) Classification and regression by randomForest. R news 2: 18-22 https://CRAN.R-project.org/doc/Rnews/

      Lüdecke, D., Ben-Shachar, M. S., Patil, I., Waggoner, P., & Makowski, D. (2021) performance: An R Package for Assessment, Comparison and Testing of Statistical Models. J Open Source Softw 6: 3139 https://doi.org/10.21105/joss.03139

      The R packages used in this study have been appropriately cited in the revised manuscript as follows:

      “The repeated measures ANOVA (the ezANOVA function of the “ez” R package) was used to examine the effects of grazing treatment and sampling years on ecosystem CO<sub>2</sub> fluxes (GPP, ER, and NEP), microclimatic variables (soil temperature and moisture), and plant biomass parameters (AGB, BGB, and root/shoot ratio) across the five-year study period from 2019 to 2023 (Chen et al., 2024; Lawrence et al., 2026).

      “A linear mixed-effects model, with ‘study’ included as a random factor, was employed to estimate the weighted response ratio (RR<sub>++</sub>) across studies or within a specific group, fitting with restricted maximum likelihood using the ‘lmer’ function in the ‘lme4’ package (Bates et al., 2015; Feng et al., 2023).”

      “When the assumption of normality was violated, bootstrapping with 999 iterations was performed using the ‘boot’ package to derive the 95% confidence interval (CI) for each RR<sub>++</sub> (Chen et al., 2021; Canty et al., 2025).”

      “The random forest model was conducted using “randomForest” and “rfPermute” packages to identify the relative importance of the predictor variables (wetness index, grazing duration and intensity, the responses of soil moisture and temperature and livestock types) of GPP, ER, NEP, AGB and BGB in the meta-analysis (Archer, 2025; Liaw et al., 2002; Liao et al., 2024).”

    1. Author response:

      The following is the authors’ response to the original reviews.

      eLife Assessment:

      The worldwide decline in the health of coral reefs is well documented, and overgrowth by microbial consortia can be a contributing factor. Kelman and colleagues used metagenomic analysis to interrogate potential changes in phage-associated genes predicted to be involved in central carbon metabolism. The study addresses the hypothesis that metabolic genes associated with carbon metabolism that are encoded by viruses reflect the health of the corals. The study contributes a valuable perspective on the potential role of phages in coral health, although limitations of the data and analyses offer an exploratory examination rather than a definitive result. Overall, the evidence supporting the major findings is incomplete, in part because the conceptual model relies on qualitative assumptions rather than empirical data.

      We want to first thank both reviewers and the editor for their comments. They were incredibly constructive and thoughtful, and provided a roadmap to a much stronger paper for us to follow. Guided by the comments, we have sought not only to address the individual points raised below, but also to expand upon them where doing so improved the clarity and accessibility of the work. The paper is now stronger, more focused, more conservative, and more robust because of the guidance provided by the reviewers. Thank you.

      In addition to more point-by-point issues, the manuscript has been strengthened in three main ways:

      (1) Clarified the distinction between observations, inferences, and broader ecological implications, ensuring that empirical results, conceptual synthesis, and model predictions are clearly separated throughout the manuscript.

      (2) Reframed and expanded the presentation of the conceptual model, clarifying its purpose as a qualitative framework for integrating our observations with established reef ecology and for generating experimentally testable hypotheses, rather than as an additional source of empirical evidence.

      (3) Clarified the analytical framework and statistical interpretation, including expanding the Methods to better explain the inferential pipeline, the interpretation of community-level metabolic associations, and the use of bootstrapped confidence intervals to quantify uncertainty around ecological effect sizes.

      Although the reviewers approached the manuscript from different perspectives, we found their recommendations to be remarkably complementary. Reviewer 1 consistently encouraged us to improve the clarity, transparency, and accessibility of the manuscript, while Reviewer 2 challenged us to more carefully align the strength of our conclusions with the strength of the available evidence. Rather than addressing these concerns independently, we used them as the basis for a broader restructuring that simultaneously improved the manuscript's organization, transparency, clarity, and evidentiary discipline. We believe the result is a substantially stronger paper.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      Microbialization (bacterial overgrowth) is a recognized component of degraded, eutrophied coral reefs where there is a shift from coral to algal dominance on the benthos. In addition, previous work has demonstrated that virus communities shift from a lytic strategy dominated (kill-the-winner) to a temperate (lysogenic) strategy dominated with reef microbialization. Kelman et al. sought to leverage previously published virus metagenomes produced from the water column of healthy and degraded coral reefs to assess virus community metabolic shifts. The authors also produce a conceptual model to demonstrate the potential impact of the observed metabolism shifts on reef fates.

      Strengths:

      The main strength of the manuscript is the findings from their metagenomic analyses and results. The virus metagenomes were produced using established approaches in the field and yield sufficient data per sample for their analyses. Interesting results regarding the shift in the types of genes from anaplerotic to cataplerotic provide the foundation for testable hypotheses to determine the magnitude of impact virus strategies have on reef health. The introduction is also well written and sets up the scene very well.

      Weaknesses:

      (1) The methods text currently omits important information related to the sampling design. It is not clear how many metagenomes are from healthy and degraded communities. This impacts the interpretability and robustness of the statistical results. Furthermore, it is unclear if analyses are based on assembled contigs or read-based alignments. Improving the clarity and organization of the Methods is essential for reproducibility.

      (2) Regarding the bioinformatics approach, normalization using the "per cent known" approach within samples may not fully account for discovery bias related to sequencing depth. While Supplementary Table 1 shows variability in read counts, the lack of community-level metadata makes it difficult to determine if sequencing depth covaries with community type (healthy vs. degraded). The study would benefit from a rarefaction analysis or subsampling to ensure that gene frequency trends and Spearman correlations are biological signals rather than artifacts of sequencing effort.

      (3) The qualitative model in Figure 5 is positioned as evidence for the role of viruses in reef health, but it does not provide independent support for the authors' hypotheses. Since the model is parameterized using "arbitrary units" to reflect the authors' assumptions rather than being derived from the empirical metagenomic data, it serves as a helpful illustration of a hypothesis but not as a validation of the findings.

      (4) Results and discussion require revisions to improve readability and connectivity across sections. Ensuring a clear distinction between empirical data and model-based speculation would help the audience better appreciate the science.

      We thank the reviewer for their thoughtful and constructive review. Their comments were particularly helpful in identifying opportunities to improve the clarity, organization, and reproducibility of the manuscript. In response, we substantially expanded and reorganized the Methods, streamlined the Results and their connection to the Discussion, and clarified the role of the conceptual model as a framework for integrating our observations and generating testable hypotheses rather than as independent empirical evidence. We respond to the specific comments below.

      Reviewer #2 (Public review):

      Summary:

      The manuscript by Kelman and coauthors investigates how viral communities differ in the genes they encode in healthy and degraded coral reef ecosystems. Across 19 viral metagenomes from Central Pacific reefs, the authors assess the frequency of integration/excision genes as a proxy for viral community temperateness and ask whether genes associated with central carbon metabolism covary with signatures of temperateness. The main finding is that viral communities with more temperate-related genes encode more genes from the Entner-Doudoroff pathway and other reactions interpreted as anaplerotic, whereas more lytic-associated viral communities show greater representation of some pentose phosphate pathway, TCA, and redox-associated genes interpreted as cataplerotic. The authors propose a model based on these patterns in which lytic viral metabolism helps suppress bacterial overgrowth on healthy reefs, while temperate viral metabolism may promote microbialization on degraded reefs. The study addresses an interesting and potentially important concept - that viral auxiliary metabolic genes are important components of microbial communities and can affect ecosystem functioning. Linking viral metabolism to coral reef microbialization is a creative conceptual advance. The manuscript is clearly written, and the reported enrichment of anaplerotic genes in temperate-associated viromes is an interesting pattern that could motivate future work on how viral metabolic potential varies across reef states.

      Strengths:

      (1) The study connects viral lifestyle, central carbon metabolism, bacterial overgrowth, and reef degradation in a framework that could be useful for future studies of coral reef ecosystems and viral ecology. This is an interesting synthesis that links viral auxiliary metabolism to broader questions about microbialization and reef state.

      (2) The manuscript is generally clearly organized around a testable prediction: viral metabolic gene content should vary along a lytic-to-temperate viral community gradient. The reported enrichment of anaplerotic genes in viromes with a larger fraction of temperate viruses is a compelling result.

      (3) The authors highlight several virus-encoded metabolic genes that may not have been previously reported in viral datasets or genomes. If supported by further validation, these observations could expand the known repertoire of viral metabolic potential.

      (4) The modeling helps clarify the feedbacks the authors propose may connect viral lifestyle, bacterial metabolism, and coral reef degradation. It provides a foundation for generating hypotheses about how viral metabolic genes could influence reef microbial dynamics.

      Weaknesses:

      (1) The main limitation is that the evidence for several key claims remains indirect. The core analysis is based on correlations between metabolic gene frequencies and integration/excision-related genes. This does not demonstrate that the metabolic genes occur in temperate viral genomes, are physically linked to lysogeny genes, are expressed during infection, or alter host metabolism. Thus, the data support an association between VLP-associated metabolic annotations and a community-level temperateness proxy, but not a direct link between temperate phages and these metabolic functions.

      (2) It is important not to equate community-level gene frequencies with genome-level or infection-level metabolic programs. A virome may contain more anaplerotic genes overall, but that does not demonstrate that individual viruses reprogram their hosts in an anaplerotic manner nor that infection produces a net anaplerotic effect. Individual viruses may encode both anaplerotic and cataplerotic genes, and a smaller number of cataplerotic genes could have stronger metabolic consequences depending on expression, enzyme efficiency, pathway position, and host context. This is an important limitation that should be acknowledged and, if possible, addressed with contig- or genome-level analyses.

      (3) The ecological interpretation assumes that viral infection is strong enough to influence reef-scale bacterial population dynamics. However, the study does not directly measure infection frequency, lysis rates, viral production, burst size, lysogeny frequency, prophage induction, gene expression, or bacterial mortality. If viral mortality or lysogenic conversion were rare in these systems, the observed gene-frequency patterns could have limited ecosystem-level consequences. This makes claims about viral metabolism suppressing bacterial overgrowth, accelerating microbialization, or acting as a conservation lever more speculative than suggested.

      (4) There are statistical limitations related to the use of relative gene frequencies. Because genes are normalized as percentages of known genes, the data are compositional. Apparent increases in some categories may partly reflect decreases in others. Bootstrapped Spearman correlations are useful for assessing the robustness of these associations, but they do not address compositionality or multiple testing.

      (5) The anaplerotic/cataplerotic classification is central to the manuscript's conclusions and would benefit from more support. The framework is useful, but it depends on both annotation confidence and biochemical context. Sequence-similarity annotations alone may be vulnerable to misannotation, especially for central metabolic enzymes that share conserved domains across functionally distinct proteins. Stronger evidence that key genes contain key functional domains and/or are phylogenetically related to characterized enzymes would help support the proposed functions. In addition, many central carbon enzymes are reversible or context-dependent, so a clearer rationale for each classification would strengthen the interpretation.

      Overall, the manuscript presents a valuable hypothesis and highlights new ecological patterns in coral reef viral metagenomes, but falls short of the evidence needed for the strongest claims. The work would be strengthened by analyses that directly link metabolic genes to viral genomes or lysogeny markers, address compositional effects, validate key annotations, and more clearly distinguish observed gene-frequency associations from hypothesized effects on infection, host metabolism, and reef state.

      We thank the reviewer for their careful and constructive assessment. Their comments were particularly valuable in sharpening the evidentiary boundaries of the study. In response, we revised the manuscript throughout to distinguish more clearly between the community-level gene-frequency associations we observe and genome-level linkage, infection-level metabolic effects, and ecosystem-level consequences that remain hypotheses for future testing. We also revised the statistical presentation and discussion of methodological limitations to better reflect the strength and scope of the available evidence. We respond to the specific comments below.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      (1) Significance

      General comments

      Well written and highlights the findings of the study. However, the final sentence needs rewording to be clearer regarding the claims being made (see below).

      Specific comments:

      Lines 86-88 - I suggest revising the final sentence to better match the strength of the data presented. As currently written, the sentence makes broad causal claims that are not directly supported by the results.

      For example, the phrase "viral metabolism can either reinforce reef resilience or exacerbate collapse" implies a level of mechanistic certainty that the current data do not demonstrate. The results show shifts in viral community metabolism, measured through gene abundances, that are likely associated with changes in the environment, host assemblages, and virus community diversity. These shifts may potentiate the DDAM feedback loop, but additional data and experimental work would be needed to determine whether viruses actively maintain resilience or contribute to collapse.

      Similarly, the phrase "making it a hidden driver of ecosystem fate" feels too strong for the results presented. A more appropriate framing would be to present viral community metabolism as a promising and important avenue for future research into reef trajectories and ecosystem change.

      Finally, the phrase "a potential target for conservation strategies" is somewhat unclear. It is not obvious whether viral metabolism is being framed as something conservation efforts should directly manipulate, or as an indicator/marker of reef condition and recovery. Clarifying this would strengthen the significance statement.

      We thank the reviewer for this thoughtful and constructive suggestion. We agreed that the Significance statement occasionally conveyed greater mechanistic certainty than was supported by the observational nature of the data. Guided by these comments, we revised the section throughout to more clearly distinguish between our empirical observations, the ecological interpretations they support, and the broader hypotheses and implications they motivate. In particular, we softened causal language regarding the role of viral metabolism in reef resilience and decline, reframed the discussion of conservation to emphasize future opportunities rather than immediate application, and clarified that the manuscript provides a conceptual ecological framework for future investigation rather than direct evidence of ecosystem-scale mechanisms. We believe these revisions now more accurately reflect both the strengths and the limitations of the study while preserving its central ecological significance (lines 78-93).

      (2) Abstract

      Specific comments

      Lines 97-102 - Add commas to improve readability:

      Original: We found that viral metabolism shifted broadly from being dominated by metabolism that builds up pools of central intermediates on degraded reefs dominated by temperate viral infection ('anaplerotic' reactions) to metabolism that consumes these pools to prioritize production of metabolic precursors for virion construction on healthy reefs dominated by lytic infection ('cataplerotic' reactions).

      Revised: We found that viral metabolism shifted broadly from being dominated by metabolism that builds up pools of central intermediates on degraded reefs, dominated by temperate viral infection ('anaplerotic' reactions), to metabolism that consumes these pools to prioritize production of metabolic precursors for virion construction on healthy reefs, dominated by lytic infection ('cataplerotic' reactions).

      Thank you. We agreed that this sentence needed revision for clarity. In addition to improving its readability, we revised it to describe the observed pattern explicitly at the level of viral-community metabolic gene content rather than implying a demonstrated shift in metabolism itself (lines 102-107).

      (3) Introduction

      General comments

      Very well written introduction that sets up an exciting scene!

      Specific comments

      Lines 134-136 - Minor revision to improve readability:

      Original: "Viral predation could, in principle, preclude microbialization by killing proliferating microbes, as lytic infection and lysis rates are predicted by established predator-prey models to rise with host densities and growth rates"

      Revised: "Viral predation could, in principle, preclude microbialization by killing proliferating microbes, as lytic infection and lysis rates are predicted to rise with host densities and growth rates by established predator-prey models."

      Thank you. We are glad the Introduction was engaging. We have adopted this edit (lines 140-142).

      (4) Methods

      General comments

      The methods text needs to be revised to increase readability and transparency. I would love to really appreciate the work done and the results produced, but some aspects are unclear, which leaves me with a cloudy understanding of how the data was processed and the results were generated. I am also concerned that the qualitative model makes many assumptions regarding ecological interactions between the components. It might be good to clearly state these assumptions and their impact on the outcome in a table or explicitly within the text.

      We thank the reviewer for these thoughtful comments. We agreed that the original Methods section did not always provide sufficient detail to allow readers to fully understand the analytical framework or the inferential pathway from the underlying sequence data to the ecological conclusions presented. Rather than addressing these comments individually in isolation, we substantially reorganized and expanded the Methods to improve transparency, readability, and reproducibility throughout. In particular, we clarified the study design and sampling framework, explicitly distinguished between the previously generated viral metagenomic datasets and the new analyses performed in this study, and expanded our description of the bioinformatic and statistical workflows. We also more clearly explain our decision to retain the community-level, read-based analytical framework of the previous studies while extending those analyses using the MG-RAST annotation platform. By avoiding a fundamentally different analytical approach, we maintain conceptual continuity and direct comparability. Finally, we clarified the assumptions underlying the conceptual model and its intended role as a qualitative framework for hypothesis generation rather than empirical validation. Collectively, these revisions provide a clearer, more transparent, and more reproducible account of the analytical framework used throughout the study (lines 206-390; this spans the entire Methods section).

      Specific comments (reordered for clarity where needed)

      Line 189-190 - Sentence needs rewording. Currently, it reads a bit awkwardly, and it should be clearer that these metagenomes were previously produced and sourced from a different manuscript. It reads as if data were generated from new samples and processed as previously described, rather than a reanalysis of a dataset.

      Line 189-212 - Information related to the sample design (e.g., how many metagenomes from how many reefs/reef health states) is missing and should be added in this section to provide more context for the reader.

      We thank the reviewer for this helpful suggestion. We have substantially revised the opening of the Methods to clarify that this study is an analysis of previously generated virus-like particle (VLP) metagenomes, most of which had been used in prior publications, from Pacific coral reefs rather than newly generated samples. We also expanded the description of the sampling design, including the number of metagenomes analyzed and their relationship to previous studies, and explain that we retained a bioinformatic framework closely aligned with those earlier analyses to maintain methodological continuity and enable direct comparison with the published work. We agree that these additions improve the clarity, transparency, and reproducibility of the study (Intro lines 173-176, Methods lines 206-211, Supplementary Table 1).

      Line 208-210 - This sentence produced concern upon reading it. If contamination is a worry and would have a direct impact on the results (especially given that results seem to be based on read alignments to a reference database), I suggest a bacterial read removal step with Kraken or alignment to a bacterial reference be performed prior to functional annotation. Given that there were multiple steps in the VLP DNA processing/extraction, there is unlikely to be a large amount of bacterial sequence reads; however, it would be good to confirm.

      Lines 213-218 - It is unclear if the reads were assembled into a contig prior to annotation. In addition, in the Supplementary Table 1, please clarify if "sequences" is equal to reads or assembled contigs. 

      We thank the reviewer for these helpful comments. We have clarified that the analyses are based on read-level annotations rather than assembled contigs, consistent with the original virome studies and with our aim of maintaining methodological continuity with those published analyses. We also expanded the Methods to describe the multiple safeguards used to minimize cellular contamination, including 0.45-µm filtration and chloroform treatment, cesium chloride purification, DNase treatment, microscopy confirming the absence of cells, and PCR confirmation of the absence of detectable 16S rDNA amplification. While no purification protocol can completely exclude the possibility of trace contamination, these independent purification and validation steps substantially reduce this possibility. We have therefore retained the existing read-level analytical framework while making both its basis and its limitations clearer in the revised manuscript (lines 205-252).

      Line 219-224 - I am concerned that allowing alignment lengths as short at 15 bp will lead to false positives. Considering the minimum read length is 100 bp, a 50 bp alignment length is a more reasonable cutoff.

      We thank the reviewer for drawing our attention to this point. In reviewing the MG-RAST parameters, we identified that the original manuscript incorrectly described the minimum alignment-length setting as 15 bp. The MG-RAST parameter used in our analysis is a minimum alignment length of 15 amino acids, and we have corrected the Methods accordingly. We have also clarified that these are the default MG-RAST annotation settings and that, because they are permissive, the resulting read-level annotations are used here for relative comparisons of broad functional representation among identically processed viromes rather than to establish the function of any individual read (lines 243-252).

      Lines 231-232 - The described normalization approach does not account for sequencing depth per sample since, based on how I interpret the text, you are calculating the relative abundance of genes within a sample. This does not control for the potential increase in the number of detected genes within a sample driven by higher sequencing depth. To confirm that sequencing depth does not influence results, I suggest performing a rarefaction analysis or having a subsampling step to test for the sensitivity of read depth on results.

      We thank the reviewer for this thoughtful comment. Our objective was to compare the relative frequencies of annotated functional categories within viral communities rather than estimate absolute gene abundance or gene richness. We therefore normalized gene frequencies within each virome as the proportion of annotated ("known") genes, allowing direct comparison of relative community composition among metagenomes with differing sequencing depths. This normalization strategy is also consistent with our previous community-level analyses of these viromes. To make this analytical framework clearer, we have substantially expanded the Methods to explain the rationale for this normalization approach, how higher-order functional categories were constructed, and how gene frequencies were compared across samples (lines 296-316).

      We also clarify a related consequence of this normalization. Because gene frequencies are expressed as proportions of a common total of annotated genes, the data are compositional, and an increase in the relative frequency of one category is necessarily accompanied by decreases in others. We have now added an explicit statement of this limitation to the Methods and clarify that the values reported here represent relative community composition rather than absolute gene abundance (lines 253–257).

      Line 240 - Define "EC" -> "... Enzyme Commission (EC) numbers...". All abbreviations should be clearly defined prior to use throughout the manuscript.

      Line 262 - Minor: Define the acronym "CIs" here - "Confidence intervals (CIs)..."

      We thank the reviewer for identifying these omissions. We now define Enzyme Commission (EC) upon first use in the manuscript in the Methods and Results sections (lines 261 and 423). Similarly, we now define confidence intervals (CIs) when introduced in the Methods and Figure 1 legend (lines 283–286 and 777–778).

      Lines 264-265 - This sentence is repeated later in the manuscript, and it's not clear what is meant as is. I would revise to make it more clear it is meant to signal that the CIs will be within brackets within the text. Or, it may be best to just have CIs like so:

      Example from line 372:

      Original = "(Figure 1; ρs = -0.81; [-0.95, -0.58])"

      Suggested revision throughout the manuscript = "(Figure 1; ρs = -0.81; CIs: -0.95, -0.58)"

      We thank the reviewer for this helpful suggestion. To improve clarity, we now explicitly state in the Methods that 95% confidence intervals are reported in square brackets following each Spearman's rho estimate (lines 285-286), and we have changed Figure 1 to be consistent with that (lines 777-778). We retained this notation because it provides a compact and consistent presentation of the effect size and its associated uncertainty.

      Lines 270-273 - Unclear what is being measured, diversity of genes within samples? Or is taxonomic diversity present within samples?

      Thank you for pointing this out. We have now clarified that diversity is the Shannon index (H’) using the relative frequencies of annotated functional genes in each sample (lines 290-293).

      Line 276-279 - Add "to" in "...was defined aid our..."

      We thank the reviewer for identifying this issue. This sentence has been revised as part of our broader effort to improve the clarity of the manuscript (lines 319-322).

      (5) Results

      General comments

      I believe this section would benefit from a bit of reorganization to help the flow of the manuscript. Certain sections, like the "Functional homologues as viral lifestyle markers", are not descriptive enough, and it is unclear how "the divergent correlations in these genes across a viral temperateness spectrum may reflect viral life strategies" is justified. Also, several results are not discussed in the discussion.

      We thank the reviewer for this helpful observation. We agree that the Results would benefit from clearer organization and stronger links between individual observations and their broader interpretation. In response, we substantially reorganized the Results to improve their logical progression. We moved explanatory material describing the analytical framework to the Methods and reorganized the remaining Results from broad community-level patterns to increasingly focused analyses of central carbon metabolism. We also revised the Discussion to ensure that the principal observations presented in the Results are revisited and interpreted within the broader ecological framework developed in the manuscript. More broadly, the revised framing now consistently presents individual observations as community-level associations and their ecological implications as hypotheses rather than definitive functional interpretations (Introduction lines 190-195, Methods lines 296-316, 317-327 and 328-330; Results lines 392-518; Discussion, lines 525-529).

      We agree that the original “Functional homologues as viral lifestyle markers” section overinterpreted these community-level associations. Because the confidence intervals for the two fructose-bisphosphate aldolase homologues both span zero, we have removed this subsection rather than present these patterns as evidence for viral lifestyle markers. The individual estimates remain reported in Table 1 for completeness.

      Specific comments

      Lines 346-369 - Overall, this "Hallmarks of viral temperateness" text seems more appropriate for the methods section and/or a figure/table caption rather than a results section. It is unclear to me whether there are any results being presented here; instead, it reads more like a description of how to interpret upcoming results. The text should be revised to make the results more clearly presented or moved to a more appropriate section of the manuscript.

      We agree, and have moved the explanatory material into the Methods/Analytical Framework and rewritten the opening of the Results so that this section now presents observations rather than instructions for interpreting subsequent analyses (Methods, lines 296-316; Results, lines 392-403).

      Line 353-355 - This sentence needs revision. It feels like two similarly themed, but mismatched, sentence fragments. The first part sets up for a methods statement, but the second part defines a metric?

      Sentence: "As a measure of how consistently or monotonously gene frequency and sample temperateness covary, Spearman Rho (ρs) values reflect the strength and sign of their correlation."

      Maybe it is just how I am reading it, but I feel it should be revised to (or something similar):

      "As a measure of how consistently or monotonously gene frequency and sample temperateness covary, a Spearman's Rank Correlation analysis was performed, generating Spearman Rho (ρs) values reflecting the strength and sign of their correlation."

      We thank the reviewer for this helpful observation. We agree that the opening of the Results conflated methodological explanation with the presentation of results, resulting in awkward phrasing and reduced clarity. Rather than simply revising the sentence, we substantially reorganized this portion of the manuscript. The analytical framework, including the rationale for the temperateness proxy, the interpretation of Spearman's ρ, and the relationship between Figures 1–5, has now been moved to a dedicated Analytical framework subsection of the Methods. This allows the Results to focus directly on the empirical observations while presenting the methodological context in its more appropriate location. We believe this restructuring substantially improves the clarity and flow of the manuscript (lines 272-316 and 392-403).

      Line 357 - Missing a closing parenthesis on "(ps < 0."

      Line 357-358 - In this sentence, it says the 95% confidence intervals are listed in square brackets (I am assuming in Figure 1). But Figure 1 has confidence intervals in parentheses, and this is stated within the figure caption as well. Needs to be made consistent across components of the manuscript. Revisiting this comment as I read the next section of the results, I understand now what was meant regarding the brackets. This should be clarified here (and previously).

      Corrected. The missing parenthesis was added during the revision and restructuring of this section, and the presentation of confidence intervals has been standardized throughout the manuscript using square brackets for consistency and clarity (lines 285-286, 394-397, and the Figure 1 legend, line 777-778).

      Lines 465-500 - The text here presents model results as valid biological outcomes. There is also a bit of discussion text in this section. Given this is a qualitative model with many strong assumptions, it's best to illustrate hypotheses rather than being framed as evidence.

      We thank the reviewer for this important observation. We agree that the original presentation did not always sufficiently distinguish between the empirical observations presented in this study and the qualitative hypotheses generated by the conceptual model. We therefore substantially revised both the Results and the Discussion to more clearly separate these two levels of inference. Throughout the manuscript, the conceptual model is now consistently presented as a qualitative framework for integrating our observations with established reef ecology and for generating experimentally testable hypotheses, rather than as independent empirical evidence. Correspondingly, we adopted more conservative language throughout this section to ensure that model outputs are interpreted as conceptual scenarios illustrating possible ecological consequences of the observed community-level metabolic associations, rather than as demonstrated biological outcomes. We believe these revisions more accurately reflect both the purpose of the model and the observational nature of the underlying data (Methods, lines 317-330; Results, lines 483-518; Discussion, eg line 527).

      (6) Discussion

      General comments

      There are a lot of results explicitly mentioned in the Results section left out of the discussion. Revisions can be made to increase the connectivity between sections and streamline the story of the manuscript to help the reader appreciate the findings and implications.

      We thank the reviewer for this suggestion. In revising the manuscript, we substantially reorganized the Discussion to focus on the principal findings and their broader ecological implications. The revised Discussion now revisits the major observations underlying our conclusions while distinguishing more clearly between empirical observations, ecological inferences, and conceptual hypotheses. We elected not to discuss every individual observation in detail, instead focusing the Discussion on those findings most central to the manuscript's overarching conclusions.

      (7) Figures

      Figure 1 - A previous comment was made regarding the mismatch between the CIs in brackets and the figure containing them in parentheses (not a fatal error, just a quick fix in the text). An additional recommendation for this figure is to make it clearer which gene correlations are significant. In the main text and within the figure caption, it states that:

      "Genes where the 95 % confidence intervals exclude zero are significant at the p < 0.05 level."

      Within the figure, there are a few genes that don't seem to be significant given this guideline (Cell division & cycle, Stress response, Protein metabolism). I suggest some sort of visual aid that would allow the reader to determine which are significant and which are not. Adding an asterisk to all significant correlations (or removal of non-significant) could help interpretability for the reader.

      The authors may also want to consider some visual way to signal temperature-associated vs lytic-associated genes in the figure. One way may be to organize the panels into lytic- and temperate-associated groups.

      Thank you for these suggestions. Confidence intervals are now presented consistently in square brackets throughout the manuscript. We substantially revised the statistical presentation throughout the manuscript (lines 285-286, 397, 777-778). Rather than emphasizing null hypothesis significance testing, we now consistently present bootstrapped median Spearman’s ρ estimates together with 95% confidence intervals to quantify uncertainty around each estimate (lines 287-289). We believe this presentation more clearly communicates the magnitude, direction, and uncertainty of the observed community-level associations. Because these confidence intervals are not adjusted for multiplicity, we elected not to add asterisks to Figure 1 or to use confidence-interval exclusion of zero as the primary basis for our conclusions. The Figure 1 legend instead states that the confidence intervals quantify uncertainty and do not represent multiple-testing-adjusted significance (lines 785-786). Asterisks retained in Table 1 and Figure 2 are provided only as visual guides and are not interpreted as formal discoveries (lines 765-766, 797-799). Instead, our interpretation emphasizes the magnitude, uncertainty, direction, and coherence of associations across predefined pathways and functional categories.

      In terms of figure layout, we retained mean gene frequency ordering of the functional categories to facilitate navigation of the figure. Because Figure 1 serves primarily as a reference across a broad range of SEED Level 1 functional categories, we felt that mean gene frequency ordering provides the clearest and most accessible presentation to help contextualize our results. We now clarify the meaning of positive and negative correlations in the figure legends for Figures 1 and 2: “Positive Spearman’s ρ values indicate temperate-associated gene categories, whereas negative ρ values indicate lytic-associated gene categories” (lines 778-780, 792-794).

      (8) Data availability

      I tried to access data on MG-RAST servers and was unable to find them due to a server error.

      We thank the reviewer for bringing this to our attention. We have also occasionally encountered intermittent server availability on MG-RAST. To ensure continued accessibility of the underlying data, the FASTA files for all metagenomes, together with the project code, annotations, and simulation files, are also available through our GitHub repository (https://github.com/hopefulmonstersucla/viral-metabolism; lines 583-590). We continue to provide the MG-RAST accession numbers as the primary archival record of the datasets, while the GitHub repository provides an alternative access route should MG-RAST be temporarily unavailable.

      To end, we again thank the reviewer for their thoughtful and constructive review. Throughout the revision, their comments consistently encouraged us to improve the clarity, organization, and accessibility of the manuscript. We believe the resulting paper is substantially clearer, more transparent, and more accessible to readers, and we are grateful for the roadmap the reviewer provided.

      Reviewer #2 (Recommendations for the authors):

      (1) My largest concern is that the language in the manuscript moves from gene frequency correlations to claims about viral metabolism driving reef decline, supporting bacterial proliferation, and offering a conservation lever. The abstract says the findings position viral metabolism as both a driver of reef decline and a conservation lever, with "re-viralization" as a restoration strategy. I do not think the current data support that level of inference. I believe the authors should consistently and clearly distinguish between conclusions that the data support (Viral communities are associated with different metabolic gene profiles. Those genes may indicate different metabolic potentials.) and those that are speculative, not demonstrated outcomes (Those potentials may influence host metabolism during infection. Those infection-level processes may alter reef-scale microbialization.) in their writing.

      We thank the reviewer for identifying what we also came to view as the central issue in revising the original manuscript. We agree that the original framing did not always clearly distinguish between our empirical observations, the ecological inferences they support, and the broader hypotheses that they motivate. Addressing this concern became a major focus of the revision. Throughout the manuscript, we now consistently distinguish between community-level observations, conceptual interpretation, and broader ecological implications. We substantially revised the Significance statement, Abstract, Introduction, Results, Discussion, and conceptual model to ensure that the strength of our conclusions reflects the strength of the underlying evidence. In particular, we now present the observed metabolic associations as community-level patterns, while framing their potential consequences for infection, host metabolism, microbialization, and reef resilience as hypotheses generated by our conceptual framework rather than demonstrated outcomes. We believe this distinction now more accurately reflects both the scope of the data and the purpose of the study.

      (2) A broader issue is the presentation and interpretation of the many correlation analyses. Figures 1 and 2 contain a large number (20+) of small panels, and it is difficult to assess which relationships are most important, what the direction of each relationship is, and which results are well supported. Because the manuscript's conclusions rely on recognizing broader patterns across many categories and genes, I think these figures should do more to guide interpretation. Some combination of color and symbol could improve readability. For example, using different colors for positive vs negative correlations and a separate indicator for whether confidence intervals exclude zero or whether results remain significant after multiple-testing correction. A compact summary panel or heatmap may also help readers synthesize the overall pattern more efficiently. Relatedly, the manuscript appears to evaluate a large number of separate correlations, but I do not see a correction for multiple testing. Interpreting each correlation based on whether its 95% bootstrap confidence interval excludes zero does not address false discovery across the full set of comparisons. I recommend that the authors report the number of tests performed and apply an appropriate false discovery rate correction, such as Benjamini-Hochberg. This would make it much easier to distinguish the most robust results from more tentative patterns.

      We thank the reviewer for this thoughtful suggestion. We agreed that the original presentation required clearer guidance to help readers interpret the broader patterns across the many community-level correlations. In response, we substantially revised both the analytical framework and the figure framing. The manuscript now explicitly explains the interpretation of positive and negative Spearman’s ρ values within the Methods, and the legends for Figures 1 and 2 now clarify that positive correlations indicate temperate-associated gene categories whereas negative correlations indicate lytic-associated gene categories (lines 778-780, 792-794). Figure 1 retains all functional categories and presents their bootstrapped ρ estimates and 95% confidence intervals without asterisks. Its legend states that the confidence intervals quantify uncertainty and do not represent multiple-testing-adjusted significance (lines 785-786). Table 1 and Figure 2 retain asterisks only as visual guides to intervals that exclude zero, and their legends explicitly state that these do not represent multiple-testing-adjusted significance (lines 765-766, 797-799).

      With respect to multiple testing, our objective was not to identify a small subset of individually significant genes through formal hypothesis testing, but rather to characterize broad community-level metabolic patterns across predefined functional categories and pathways. Accordingly, we emphasize bootstrapped effect sizes together with their associated confidence intervals to quantify uncertainty around each estimate, rather than relying primarily on null hypothesis significance testing. We therefore retained this estimation-focused analytical framework throughout the manuscript (eg lines 287-289). Finally, because Figures 3 and 4 already synthesize the pathway- and functional-level patterns emerging from the individual correlations shown in Figures 1 and 2, we elected not to add an additional summary heatmap, as we felt this would largely duplicate information already presented.

      We also thank the reviewer for raising compositionality, which we agree we had not engaged with adequately in the original manuscript. Because gene frequencies are expressed as proportions of a common total of annotated genes, the data are compositional, and an increase in the relative frequency of one category is necessarily accompanied by decreases in others. We have now added an explicit statement of this limitation to the Methods and clarify that the values reported here represent relative community composition rather than absolute gene abundance (lines 253–257).

      (3) The manuscript would be strengthened by additional scrutiny of the gene annotations and the viral origin of the metabolic genes. The conclusions depend on the interpretation that specific central carbon metabolism genes are encoded by viral communities and vary with viral lifestyle. However, the current analysis appears to rely primarily on read-level annotation against SEED/MG-RAST categories. This is useful for broad screening, but I do not think it is sufficient on its own to support the stronger claims about viral metabolic strategy. I recommend that the authors add additional validation steps for the key metabolic genes that drive the manuscript's conclusions. For example, metagenomic assembly could be used to determine whether central carbon metabolism genes occur on contigs with viral hallmark genes, especially integrases, excisionases, structural genes, or other viral replication genes. This would help establish whether the metabolic genes are physically linked to viral genomes (likely, but good to independently test) and whether they are associated specifically with temperate viral genome fragments (currently unclear). If assemblies are limited by read depth or read length, the authors should report this clearly and present the analysis as a limitation. I also recommend additional functional validation of the key enzyme annotations. For the genes that support the main anaplerotic/cataplerotic conclusions, the authors could use protein-domain-based annotation, reciprocal best-hit approaches, HMM searches, or phylogenetic analyses to confirm that these reads or contigs encode the proposed enzyme functions. These additional analyses do not need to validate every annotated gene in the dataset, but they should focus on the subset of genes that carry the main conclusions and those that are the most novel. This would make the manuscript's central claims much more convincing and would help distinguish robust viral metabolic signals from more tentative read-level functional assignments.

      We thank the reviewer for this thoughtful suggestion. We agree that contig-level analyses, protein-domain validation, and phylogenetic confirmation would provide valuable complementary evidence regarding the genomic context and evolutionary history of individual metabolic genes. However, these analyses address a different question from the one considered here. Our objective was to characterize community-level associations between viral metabolic gene frequencies and a previously established proxy for viral community temperateness using the same read-based analytical framework as the earlier studies on which this work builds. To make this scope clearer, we substantially expanded the Methods to explain our rationale for retaining this analytical framework and revised the manuscript throughout to ensure that our conclusions are explicitly limited to community-level metabolic associations rather than genome-level linkage or infection-level function (eg 206-208, 296-316). We now consistently present these observations as generating hypotheses regarding viral metabolic strategies that future genome-resolved studies can test directly (eg lines 185-195, 317-330, 525-529). We believe these revisions more accurately align the strength and scale of our conclusions with the evidence presented.

      (4) The anaplerotic/cataplerotic classification in Table 1 is a core part of the manuscript, but the rationale for several gene assignments is not sufficiently clear. I appreciate that the authors define these terms more broadly than their conventional TCA-cycle usage. However, many of the enzymes listed in Table 1 are reversible or participate in multiple pathways, so their classification depends on assumed flux direction and physiological context rather than gene presence alone. I recommend that the authors add a supplementary table explaining the rationale for each anaplerotic/cataplerotic assignment, including the assumed reaction direction and the relevant substrate and product pools.

      We thank the reviewer for this thoughtful suggestion. We agree that anaplerotic and cataplerotic classifications depend on biochemical context and do not imply that every enzyme involved is intrinsically irreversible. These terms are also commonly applied within the TCA cycle to reversible reactions when their predominant net flux, under a given physiological context, replenishes central metabolite pools (anaplerotic) or draws from those pools toward energy production or specialized biosynthetic precursors (cataplerotic). We use the terms in this broader functional sense rather than restricting them to TCA-cycle reactions alone (lines 102-107, 262-271). Accordingly, the assignments in Table 1 reflect the expected predominant role of each reaction within the pathway context represented in Figure 3 (see line 271), rather than a demonstrated in vivo flux direction during infection. Figure 3 explicitly distinguishes reversible reactions with double-headed arrows from irreversible reactions with single-headed arrows, while Table 1 presents each classification alongside its pathway, gene identity, and enzyme annotation. We therefore felt that an additional supplementary table would largely duplicate information already presented across the Methods, Table 1, and Figure 3.

      (5) Minor comment: I suggest revising phrases such as "the conceptual model reveals" to something like "the numerical model suggests" (e.g. line 179).

      We thank the reviewer for this helpful suggestion. Throughout the revised manuscript, we adopted more cautious language when describing the conceptual model and its outputs. We now consistently use language such as suggests, illustrates, explores, and predicts rather than wording that could imply direct empirical demonstration. These changes permeate the entire revised manuscript. These revisions are consistent with our broader effort to present the model as a qualitative conceptual framework for integrating our observations with established reef ecology and for generating experimentally testable hypotheses, rather than as an independent source of empirical evidence (lines 111-118, 185-195, 317-330, 483-518, and 569-582).

      To end, we again thank the reviewer for their thoughtful and insightful review. Their comments consistently challenged us to better align the strength of our conclusions with the strength of the available evidence. As a result, we substantially strengthened the manuscript by more clearly distinguishing between empirical observations, ecological inferences, and conceptual hypotheses. We believe these revisions have made the manuscript more rigorous, more transparent, and ultimately a stronger contribution, and we are grateful for the careful consideration the reviewer gave to our work.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      When contemplating the role of any sensory area in the brain, an essential question is: How much of the neural code is inherited from the inputs versus constructed de novo by the local circuitry? This study tackles that important question for the case of the mouse superior colliculus (SC), a visual brain area that receives direct input from the retina. The specific aspects of the neural code are the representation of line orientation and direction of motion in the visual image. Over the past 10 years or so, there have been reports that the preferred directions and orientations of neurons vary systematically across the SC in a global map that is not present in the retina, and therefore computed locally.

      Here, the authors revisit this question by expanding the range of measurements: They record from the axonal boutons of retinal ganglion cells in the input layer of the SC, from the post-synaptic neurons there, and from neurons in deeper layers of the SC. They conclude that at any given location in the SC, the signals in retinal boutons recapitulate the tuning of retinal ganglion cells, and that SC neurons follow that organization, though it is lost in the deeper layers. Notably, they find no evidence for a global map of these response properties other than what is contributed by retinal input.

      Strengths:

      The study combines multiple recording methods - calcium imaging and electrical recording - to capture the activity of retinal inputs to the colliculus, the tuning of neurons in the superficial layers close to the input, as well as neurons in deeper layers.

      Furthermore, the work connects to the recent literature on gradients of tuning properties among retinal ganglion cells. All these set the stage for testing the correspondence between retinal inputs and collicular outputs.

      Weaknesses:

      The methods used to identify direction-selective and orientation-selective neurons based on visual responses are overly permissive and don't match common usage in this research area. Furthermore, the measurements covered only a small fraction of the visual field, which limits their ability to distinguish between different hypotheses for the global map of visual response properties. Relatedly, the claim that retinal input patterns explain much of the layout in the superior colliculus should be made more quantitative.

      We thank the reviewer for this constructive assessment.

      First, we agree that classification based only on statistical significance can be overly permissive and can depend on the number of trials. We have therefore revised the analysis so that units are classified as direction- or orientation-selective only if the corresponding selectivity index is both significantly larger than zero and at least 0.1. This change only minimally affected the results and did not alter the main conclusions. We also clarified that direction and orientation tuning were not treated as mutually exclusive, because our question of interest was how much information about each stimulus feature is present in the responses, rather than assigning units to exclusive functional classes.

      Second, we agree that our two-photon recordings sample only part of the visual field and therefore do not provide a complete reconstruction of direction and orientation preferences across the entire SC. However, our aim was not to discover a global map organization de novo. Instead, we tested whether our data were consistent with previously proposed organizations of direction and orientation tuning in SC. In particular, we asked whether tuning preferences were consistent with a single preference map, in which one direction or orientation dominates each visual-field location in a layout that is stereotyped across animals. We did not find evidence for such an organization. Rather, within the sampled visual-field region, retinal boutons and SC neurons were more consistent with the topographic organization of direction and orientation preferences previously described in the retina, in which several predicted direction and orientation preferences are present at each visual-field location, together with local mixing of preferences. These two organizational features are not mutually exclusive: local populations can contain mixed preferences while the relative prevalence of a small number of preferred directions and orientations varies systematically with visual-field location.

      Third, we clarified the interpretation of our comparison to the retinal topographic models. We now emphasize that the median angular difference between measured and predicted preferences is the effect-size measure of model performance. We compare this error with two controls: a permutation control that preserves the overall preference distribution but disrupts the relationship between receptive-field location and tuning preference, and a control in which preferences are drawn from a uniform distribution of angles. We also explain why the permutation control is particularly stringent in our dataset: because model predictions vary only modestly across the sampled visual-field region, permuting receptive-field locations produces a null distribution that can be close to the measured data even when the measured preferences are systematically aligned with the topographic organization previously described in the retina. In addition, we evaluated a conventional variance-explained measure, which yielded high explained variances (85–97%). However, because this metric does not specifically test the spatial correspondence between measured preferences and the topographic organization, we concluded that the angular-error measure together with the receptive-field location permutation test more directly addresses the biological question of interest.

      Together, these revisions clarify the operational definition of tuned units, the spatial scope of the conclusions, and the quantitative support for the relationship between retinal input organization and tuning preferences in SC.

      Reviewer #2 (Public review):

      In this study, the authors investigate the spatial organization of direction and orientation selectivity in the mouse superior colliculus (SC) and its retinal inputs. By combining two-photon imaging of retinal boutons and SC neurons with Neuropixels recordings, they assess whether tuning preferences form structured maps or are arranged in a salt-and-pepper fashion. They further compare SC tuning organization to previously described retinal geometric models to determine the extent to which collicular responses inherit retinal topography. The authors conclude that SC inherits a cardinally biased topographic scaffold from the retina, which progressively weakens with depth, and that strong global maps are absent.

      A major strength of the study is the impressive combination of methodologies, including imaging of retinal boutons, imaging of SC neurons, and large-scale electrophysiological recordings across SC depth. The direct comparison to retinal geometric models is particularly valuable, as it situates the SC within a broader framework of retinotopic information transfer and advances our understanding of how retinal computations are transformed in downstream targets.

      A limitation of the study, however, is that the imaging experiments sample only a relatively small and spatially homogeneous region of the visual field, whereas the electrophysiological recordings cover a different portion of SC. This separation makes it difficult to form a fully integrated, global picture of the spatial organization of direction and orientation selectivity across the entire collicular map.

      This point overlaps with a comment by Reviewer 1, and we refer to our response there. In brief, we have revised the text to clarify that our goal was not to reconstruct a complete global map across the entire SC. Instead, our data test whether the sampled regions are consistent with previously proposed global maps in which each visual-field location is dominated by a single direction or orientation preference and whether this organization is conserved across animals.

      The restricted visual-field coverage reflects experimental constraints. Two-photon imaging of retinal boutons and SC neurons was performed in posterior SC, where optical access is possible while leaving the rest of the brain, including overlying cortex, intact. The Neuropixels recordings sampled a different, more anterior region and provided complementary information across SC depth, again in animals with intact brains.

      Although these datasets do not form a continuous global map, sampling multiple animals allowed us to test whether the local biases predicted by proposed global maps were reproducible across individuals. We measured retinal boutons in 8 animals, imaged SC neurons in 5 animals, and recorded SC neurons with Neuropixels in 7 animals. We did not find reproducible dominance of a single direction or orientation preference at the sampled locations.

      Reviewer #3 (Public review):

      Summary:

      The authors studied the organisation of orientation and direction-selective retinal ganglion cells' boutons in the mouse superior colliculus. They confirmed the results already published (Molotkov, 2023; de Malmazet, 2024; Vita, 2024; Laniado, 2025), that retinal ganglion cells' boutons in the superior colliculus conserve the retinal organisation. Thereby, orientation and direction preferences of retinal boutons at each collicular location reflect the tuning of retinal ganglion cells found at the corresponding retinal location, that is covering a matching receptive field location.

      The authors also studied the organization of orientation and direction-selective neurons in the superior colliculus. They report a lack of functional organisation in the superior colliculus for neurons preferring the same stimulus orientation or direction of movement. This goes against several published reports (Ahmadlou and Heimel, 2015; Liang et al., 2023; De Malmazet et al., 2018; Feinberg and Meister, 2014; Kasai and Isa, 2021; Li et al., 2020) but echoes a study from Chen et al. (Chen, 2021). The latter authors contested the strength of the anatomical clustering of tuned alike direction-selective neurons. They found, however, that in about a quarter of their recordings, direction-selective cells with similar preferred directions did cluster anatomically in the superior colliculus.

      Here, the authors of the current manuscript under review report that local clustering of tuning was weak in all neural populations and confined to very small spatial scales (1020 μm). This is one order of magnitude smaller than previously reported clusters of around 100-300μm wide. Therefore, the authors conclude that orientation and direction tuning in the mouse superior colliculus follows a salt-and-pepper organisation.

      Strengths & Weaknesses:

      Although the authors performed a solid analysis contesting the functional clustering of direction and orientation-selective neurons, there seemed to be some elements in their data in favour of a functional clustering of neurons.

      As an illustration, the authors plotted in Figure 1Q the distribution of preferred orientations from all their recorded orientation-selective cells. The curve shows a clear bias, indicating that neurons preferring horizontal orientations were found two times more often than neurons encoding any other orientations. Moreover, the authors recorded all their neurons from a defined anatomical location of the colliculus, marked by the dotted rectangle in Figure 3A-C. Therefore, this suggests that orientation-selective cells in this particular collicular location are biased towards preferring horizontal orientations. This supports an anatomical clustering of tuned alike orientation-selective cells in the superior colliculus.

      Similarly, Figure 1P shows a bias in the preferred directions of direction-selective neurons in the same recording area. Cells tended to respond more to upward and forward-moving stimuli. The bias is more modest than the one described above for preferred orientations. However, it still seems significant. For example, cells preferring upwards movements appeared to be four times more abundant than cells preferring downward movements. As a consequence, it indicates that preferred directions might not be uniformly distributed and equally represented across the superior colliculus.

      These anatomical biases are also visible in the receptive field analysis of the paper. In Figure 3G, the authors plotted the distribution of preferred orientations for every 10degree bins within the recorded field of view. Out of 26 bins containing more than one neuron, only 6 seemed to include cells not overwhelmingly preferring a single orientation. These were located towards the top right of the figure. Therefore, over almost 80% of the recorded superior colliculus, the data seem in agreement with the view that orientation-selective cells tend to prefer the same orientation at a given receptive location.

      The patch analysis in Figures 4G and H also seems to show some degree of coherence in the preferred orientation and direction of neighbouring tuned collicular cells. In both Figures 4 G and H, clear patches of similar preferred orientation and direction appeared to emerge. For example, in Figure 4H, there is a predominance of horizontally tuned patches. This was expected given the recording bias consisting of a majority of horizontally tuned cells. In addition, vertical and 45-degree patches are also visible, in blue and red, respectively. These patches overlap with the corresponding retinotopic locations in Figure 3G, where the histograms show that cells tend to prefer the same orientations, horizontal, vertical or 45 degrees.

      It is important to note that in the previous studies on functional clustering of orientation and direction, variability in the tuning of cells within clusters was always reported (Ahmadlou and Heimel, 2015; Chen et al., 2021; De Malmazet et al., 2018; Feinberg and Meister, 2014; Kasai and Isa, 2021; Li et al., 2020). This was more marked for direction-selective cells than for orientation-selective cells. In general, cells preferring all four cardinal directions were often recorded at any given collicular location. Similarly, orientation-selective cells could be found to prefer deviant orientations compared to adjacent cells. Therefore, it is not surprising to see locally mixed tuning in collicular neurons. However, what appeared significant in these studies was the overall proportion of cells with similar tuning in patches of the superior colliculus. As described above, this also seems to be the case in the data of this manuscript.

      To conclude, it seems that authors tend to overlook the sources of agreement between their data and previous reports showing functional clustering of cells in the superior colliculus. Instead, the authors tend to emphasise the dissimilarities and variability to put forward a contentious view on the organisation of orientation and direction selectivity in neurons of the superior colliculus. This, I fear, is detrimental to the field because it creates a sort of manufactured chaos that produces unnecessary confusion for readers who do not attentively read the manuscript. It would be valuable for the authors to consider rewriting the manuscript, acknowledging where their data, in fact, support some level of functional clustering.

      The reviewer’s comment highlights an important point that we now emphasize more clearly: our results do not fit neatly into a binary distinction between salt-and-pepper organization and strong clustering/global maps. We do not conclude that direction and orientation tuning in SC is purely salt-and-pepper. At the same time, our data do not support a stereotyped map in which each visual-field location is dominated by one direction or orientation preference that is conserved across animals.

      Instead, our results support a third form of organization: a topography of four direction and four orientation channels. In this organization, four preferences are represented locally, but their relative prevalence varies systematically across visual space. This explains why our data contain population biases and some local consistency, as the reviewer points out, while still lacking the strong single-preference dominance expected from previously proposed global maps.

      We also agree that our data should be discussed in relation to previous studies with attention to both agreements and differences. We find clear agreement with previous work in that direction and orientation preferences are not uniformly distributed and that local biases can be present. However, several primary studies and reviews have gone beyond this point and described stronger forms of organization, including a concentric global map of orientation preferences and large-scale direction biases such as upward motion or nasal/temporal motion in different SC regions (e.g., Ahmadlou and Heimel, 2015; De Malmazet et al, 2018, 2024; Li et al, 2020; Vita et al, 2024). Our data do not support this stronger interpretation as a general organizing principle in animals with intact brains. Thus, the disagreement is not about whether local or population biases exist, but about their organization, specifically whether one or several preferences are represented at each visual-field location, their spatial scale, and their reproducibility across individual animals.

      Regarding specific analyses, mean maps (Figure 4E-H) can reveal biases in the local distribution of preferences, but they do not by themselves show that a location is dominated by a single preference. For this reason, we quantified local consistency using inverse circular variance (Figure 4I-L) and compared it to shuffled controls (Figure 4M-T). This showed that retinal boutons had local consistency above chance, whereas SC neurons showed low consistency that was generally indistinguishable from the null distribution.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      Main recommendations:

      (1) Measurement of orientation selectivity

      (a) The definition of orientation selectivity (OS) based on responses to traveling gratings (line 589 ff) is inadequate. Any purely direction-selective (DS) response - i.e. with a single hump in the direction tuning curve - will also show up as OS by this vector sum criterion. In fact, most of the examples shown in the figures look to be purely DS; the second row in Figure 1D-H is the only exception. In Figure S1D-H, all the cells are marked as significantly OS, but all of them have a single preferred direction rather than two opposite directions. Note also the large number of responses that are called both OS and DS in Figure 1S. And the observation that "Preferred directions strongly predicted preferred orientations (Figure 1R, T)".

      (b) This flaw is well recognized in the literature, e.g. see Inayat 2015: "In fact, most of these "high OSI" cells had even higher DSI (Figure 5E), indicating that they were not truly orientation selective but were DS." Ideally, one would measure direction selectivity with a stimulus that has no orientation, and orientation selectivity with a stimulus that has no motion (e.g. Li 2020, Chen 2021, Ahmadlou 2015). Alternatively, if such data aren't available, one can reduce the confound by considering OS-only cells that are not found to be DS (e.g. DeMalmazet 2018). Or one can set a high threshold on the orientation selectivity index (OSI) that won't be exceeded by a purely DS response (e.g. Feinberg 2015, Yaakov 2025).

      (c) Here, there is no absolute threshold imposed on the OSI or the DSI, but only a criterion of statistical significance (line 89). This has the added drawback of being irreproducible: if another research group simply records data for longer or shorter durations, they will obtain a different significance and therefore classify the cells differently. All this is relevant in the present context because the authors would like to compare their results to a range of previous studies on OS and DS neurons in the superior colliculus. To ensure that one is talking about the same objects, the analysis here should be revised.

      We have revised the analysis to require both statistical significance and a minimum selectivity index. Units are now classified as direction- or orientation-selective only if the DSI or OSI, respectively, is significantly greater than zero and exceeds 0.1. This threshold is similar to criteria used in previous studies of direction and orientation selectivity in the SC, including Li et al. (2020), De Malmazet et al. (2018), and De Malmazet et al. (2024). This addresses the concern that significance alone can include units with reliable but weak tuning and depends on the amount of data collected. The revised thresholded analyses and updated plots in all figures give the same qualitative results: retinal boutons show stronger alignment with the retinal geometric model than SC neurons, while local clustering among SC neurons remains weak. Thus, the central conclusions are robust to this more conservative definition.

      We also clarified what our orientation selectivity measure is intended to quantify. The main question of our study is how information about motion direction and edge orientation is represented across the visual field in retinal boutons and SC neurons. For this question, it is not necessary that one neuron only responds to direction or orientation and we do not want to exclude a neuron’s information about orientation if it also carries information about direction.

      We agree that a strongly unidirectional response can produce a high OSI, but this does not mean that every DS response is necessarily OS by this measure. For example, a broad direction-tuning curve approximating a single cosine cycle can have significant direction selectivity but little or no orientation selectivity. Consistent with this, all neural populations in our data contained units that were classified as DS but not OS. Conversely, many units were classified as both DS and OS, and we report these categories explicitly throughout the manuscript. This overlap does not affect our interpretation, because our analyses ask how direction and orientation information are distributed within the SC, rather than assigning neurons to mutually exclusive functional classes.

      Most of our responses were measured with drifting gratings, because these or closely related moving stimuli have been widely used in previous studies of direction and orientation tuning in the SC. However, we also included additional datasets using moving bars and static gratings. For neurons tuned to orientation with both drifting and static gratings, preferred orientations were highly consistent across stimulus types. Preferred directions and orientations measured with drifting gratings and moving bars were also closely matched. These comparisons directly address the concern that the measured preferences might be specific to drifting gratings, and show that the inferred direction and orientation preferences generalize across stimulus classes.

      We have revised the manuscript text to make these points explicit: OSI measured from drifting gratings quantifies orientation/axis information in the neural response, not membership in a mutually exclusive class of purely orientation-selective cells. We also revised the Methods and Results to reflect the new DSI/OSI thresholding criterion.

      (2) Claims about retinotopy

      For example, line 150: "These findings show that retinal boutons in posterior SC closely preserve the retinal topography of direction and orientation tuning, while SC neurons preserved the topography for direction but deviated from that for orientation." How much of the variance in preferred direction or orientation is really explained by the retinal patterns? In most cases, the null distribution from permuting retinal locations randomly seems awfully close to the observed data (Figures 3L-O). Please give a statement of both effect size (e.g. fraction of variance explained) and significance for this correspondence.

      A conventional way to express variance explained would be to compare the error of the retinal topographic model with the error of a simpler null model:

      where is the angular error between the measured preference and the closest predicted direction/orientation from the retinal model, and is the angular error to the population circular mean. The numerator of this measure is therefore the same model error that we report in the manuscript, except that the errors are squared and summed rather than summarized by their median.

      Using this formulation, the explained variances were very high: 0.970 for bouton direction, 0.929 for bouton orientation, 0.955 for neuron direction, and 0.851 for neuron orientation. However, we did not include these values because they answer a different question from the one tested in Figure 3. This variance-explained measure asks how well the retinal model performs relative to a null model that explains all preferences with a single population mean. By contrast, our analysis asks whether the correct RF-specific retinal predictions explain the data better than the same predictions assigned to randomly permuted RF locations.

      The high explained-variance values are expected because the population-mean null model has only one value to explain the data, whereas the retinal topographic model provides four possible directions or orientations at each RF location. Thus, this comparison mainly shows that a four-class model captures the overall distribution of preferences better than a single mean preference. It does not specifically test whether the spatial arrangement of those preferences follows the retinal topographic organization.

      We therefore retained the angular-error measure together with the RF-location permutation test. This directly tests the relevant correspondence: whether measured preferences match the retinal predictions at their correct RF locations better than expected from the same preferences paired with randomly permuted RF locations. Because the explained-variance statistic is computed from the same angular model errors, its permutation-based significance would test the same underlying correspondence; it would not provide an independent significance assessment beyond the permutation test already reported.

      The reviewer is correct in observing that the RF-permutation null is often relatively close to the observed data. This is expected because the retinal model predictions vary only modestly across the sampled visual-field region. Thus, RF permutation is a stringent control: when the measured angular error is smaller than the permuted distribution despite this limited variation in the predicted preferences, this indicates systematic alignment with the retinal topographic model.

      (3) Claims about global patterns

      (a) Another major claim is that "Superficial SC and its retinal input lack global maps of direction or orientation" (line 165). But could the recordings here really reveal a global map if it existed? They cover only a small part of the visual field, about 40 x 40 degrees (Figures 4A-D). Within that region, the sampling is sparse at just a few locations (Figures 4A-B). Furthermore, it has to be pieced together from multiple animals. These claims about global organization should be revised or buttressed by stronger arguments.

      (b) To give just one example from the literature to which the authors compare their work: Li 2020 recorded from 100 x 100 degrees in the same mouse, and documented the variability across mice. Picking a 40 x 40 degree window out of these maps and mixing that up across animals, one would probably fail to see the organization.

      We have revised the text to define more precisely what our data do and do not establish about large-scale organization across SC. Our intended conclusion is not that we identify a new global organization, which would require sampling a larger portion of visual space in individual animals. Rather, our data test whether the regions we sampled are consistent with previously proposed global maps in which each visual field location is dominated by a single tuning preference and this organization is conserved across individuals.

      For this question, it is a strength that we sampled multiple animals across complementary experimental approaches: retinal boutons in 8 animals, two-photon imaging of SC neurons in 5 animals, and Neuropixels recordings of SC neurons in 7 animals. Although each individual two-photon dataset covered a restricted part of visual space, this design allowed us to ask whether the same local biases predicted by proposed global maps were reproducible across animals. We did not find such reproducible dominance of a single direction or orientation preference at the sampled locations.

      The comparison with Li et al. (2020) is useful but also highlights an important methodological difference. Li et al. recorded SC neurons whose RFs spanned approximately 100 × 100 visual degrees, but this broad access was obtained in mice that lacked cortex from birth. In contrast, our measurements were made in animals with intact brains, avoiding developmental or circuit consequences of cortical absence. Moreover, as discussed in the manuscript, Li et al. observed substantial variability in direction maps across the results presented from three individual animals. We suggest that such variability may be reconciled with a topography of four direction preferences: systematic or random differences in the relative strength of the direction channels across animals could make different preferences appear locally dominant, without requiring a stereotyped global map in which each location is dominated by the same single preference across individuals.

      We have revised the manuscript to avoid implying that our data rule out every possible form of large-scale organization. Instead, we state more specifically that our data do not support previously proposed stereotyped global maps dominated by a single direction or orientation at each visual-field location, and are more consistent with a topographic organization of direction and orientation that is already present in retinal input and varies systematically across visual space.

      Other suggestions:

      (1) Line 76: "All stimuli were first defined in spherical visual coordinates and then mapped onto the flat monitor surfaces". Please explain how; there's no unique way to draw a periodic grating on a sphere.

      We clarified that we mapped the visual stimuli with positions defined in azimuth and elevation onto the 2D plane of the monitors using the equirectangular mapping, also called cylindrical mapping. This mapping preserves the meridian lines as vertical lines but introduces distortion around the poles. In our case, the distortions are limited because the top-most elevation is 51° while the poles are at an elevation of 90°.

      (2) Line 78: "For each bouton and neuron, we fitted responses with a single temporal kernel aligned to stimulus onset". The method here is unclear, also in lines 565ff. What is the "General Linear Model"? What is its input? Intensity on the screen for every pixel and time frame?

      We have revised the Methods to explain our use of a General Linear Model. For all stimulus types, the design matrix was defined by the onset times of stimulus presentations in the continuous calcium trace. The model represented the calcium trace as the sum of stimulus-evoked responses, with each presentation contributing one copy of a shared temporal response kernel scaled by a presentation-specific amplitude. We now describe the model explicitly, including the formula, the construction of the design matrices used to alternately fit the temporal kernel and the trial amplitudes, and the dimensions of the fitted parameter vectors. We also added that this approach was used instead of simply subtracting pre-stimulus activity from activity during the stimulus window, because fitting all responses in one continuous trace helps separate residual calcium signals due to preceding trials from the response evoked by the current stimulus.

      (3) Line 301: "Given that neurons with both direction and orientation selectivity typically exhibit approximately orthogonal preferences, pooling DS and OS populations and relaxing selectivity criteria will naturally yield more heterogeneous local preference distributions." This pooling and relaxing seems to be what happened in the present study, see methods comments above. Is that what the authors mean?

      Yes, the reviewer’s interpretation is correct: in the main analyses, we did not treat DS and OS units as mutually exclusive populations. This was intentional. While separating DS-only and OS-only populations can be useful for identifying specific functional cell classes, our question was how information about motion direction and stimulus orientation/axis is distributed across the SC and visual field. For this question, we did not want to discard direction information carried by units that were also OS, or orientation/axis information carried by units that were also DS.

      Previous studies that separated DS and OS populations nevertheless used their results to make functional statements about the representation of direction or orientation at particular SC locations. For example, De Malmazet et al. (2024) proposed that a concentric map of orientation preferences in retinal boutons could support innate orienting behaviors, with different orientations linked to approach or avoidance. For this type of functional interpretation, we think it is more appropriate to quantify all available direction and orientation/axis information directly, rather than imposing mutually exclusive DS-only and OS-only categories.

      We have revised the manuscript to make this rationale explicit.

      (4) Line 596: "Significance of direction and orientation selectivity, respectively, was determined by a permutation test (1,000 permutations)." What was permuted, and how was significance assessed?

      We have revised the Methods to specify what was permuted: “Significance of direction and orientation selectivity, respectively, was determined by a permutation test (1,000 permutations of stimulus direction or orientation across trials).”

      For this test, the statistic was the DSI or OSI, respectively. The null distribution was obtained by randomly permuting stimulus labels across trials and recalculating the selectivity index for each permutation. A unit was considered significantly direction- or orientation-selective if its measured DSI or OSI exceeded the 95th percentile of the corresponding null distribution. The general procedure for permutation tests is described in the Quantification and Statistical Analysis section.

      (5) Line 654: "For each mouse, we optimized alpha by minimizing the discrepancy between predicted and measured direction and orientation preferences." Why treat alpha as a free parameter here to benefit the fit? If the pitch of the head is set with stereotaxy during the experiment, then alpha is known.

      We agree that head pitch should ideally be measured directly rather than treated as a free parameter. However, we did not record the exact pitch angle during surgery. In general, the head was positioned with bregma slightly lower than lambda, because this improved access to the SC, but the precise angle was not measured for each animal.

      We therefore treated alpha as an estimated parameter to account for this uncertainty. To make this transparent, we have added a plot (Figure S3I) showing the alpha values that gave the best fit for each animal.

      Reviewer #2 (Recommendations for the authors):

      Major points:

      (1) DS/OS definition:

      Orientation selectivity was defined using the doubled-angle vector method, which classifies units as orientation-selective whenever responses are aligned along a motion axis, irrespective of whether responses are symmetric for opposite directions. Based on this method, a neuron responding strongly and only to one but not the opposite direction of motion would yield both high direction selectivity and high orientation selectivity under this definition. However, this kind of response would be considered purely direction-selective in the field. This raises the possibility that a substantial fraction of the reported OS population may in fact consist of strongly direction-selective neurons rather than genuinely bidirectional axis-symmetric units.

      Indeed, most example cells in Figure 1 seem to be predominantly unidirectional in their responses. In addition, the example OS tunings shown in Figure S1F display considerable trial-to-trial variability at the preferred orientation, with some trials eliciting strong responses and others minimal responses, a pattern more characteristic of direction-selective responses than of a stable bidirectional axis tuning. The strong correspondence between preferred direction and preferred orientation reported in the manuscript (Figure 1R, T) and the fact that median direction selectivity exceeded orientation selectivity (Figure S1M, N) is consistent with this interpretation.

      In addition to the concern regarding the OS cells definition, there is another issue relating to both OS and DS cells. The authors write: "A bouton or neuron was considered direction or orientation tuned if its selectivity was significantly larger than zero". This approach may include some cells that are not clearly tuned. For example, cells 3 and 4 in Figure S1 do not appear tuned for the static gratings (panel H). Yet cell #3 has a preferred orientation. Cell #4 seems to have no significant preferred orientation (no red triangle), but it is still included in panels K and L comparing preferred orientation across stimulus classes.

      These ambiguities have several consequences for the interpretation of results:

      (a) While the authors show that direction and orientation tuning of DS-only and OS-only are overall similar to the population (Figure S3), many of the tuned cells are not included in this analysis. Choosing DS-only or OS-only does not necessarily select the strongly selective units (for example, a strong DS cell would be considered as both a DS and an OS cell as mentioned above).

      (b) The effect of monitor edges on orientation tuning may represent a mixture of direction and orientation responses, masking potential effects.

      (c) While the inclusion of static gratings with multiple spatial phases is an important and appropriate control for distinguishing true orientation selectivity from motion-axis tuning, it remains unclear whether all units classified as OS exhibit consistent and comparably sharp tuning under both drifting and static conditions.

      To solve these ambiguities, the authors may consider adding criteria for DS and OS cell definition (e.g., DSI and OSI thresholds). While this approach is somewhat arbitrary, it can be useful to set a minimum for tuning sharpness, and the effect can be tested on varying thresholds. Finally, it would be helpful if the authors indicate the direction and orientation selectivity value for all presented examples.

      This point overlaps with Reviewer 1, comment 1, and we refer to our response there for the main rationale and revisions. In brief, we now classify units as DS or OS only if their DSI or OSI, respectively, is both significantly greater than zero and exceeds 0.1. We have added DSI and OSI values to all example tuning-curve plots in Figures 1, S1, and 6.

      We have also clarified that OSI measured from drifting gratings quantifies orientation/axis information in the response, rather than defining a mutually exclusive class of purely OS cells. Accordingly, units can be classified as both DS and OS if their responses carry both direction and orientation/axis information.

      Regarding the examples in Figure S1H, cell 3 is significantly orientation-tuned; we show an additional plot in Author response image 1 with a rescaled y-axis, which makes this tuning more apparent and visually confirms the result of the significance test. Cell 4 is indeed not significantly OS and was included to show the range of response types across example neurons. We have revised the figure annotation/text to make this clearer.

      Author response image 1.

      The concern that edge effects on orientation tuning may be masked by a mixture of direction and orientation responses would apply if these preferences were unrelated. Several studies have shown that stimulus apertures or edges can induce apparent orientation preferences in a predictable relationship to the edge orientation (Roth et al., 2018; Liang et al., 2023; Borges et al., 2025). The most directly relevant study for the present concern is Liang et al. (2023), because they reported effects on both orientation and direction preferences in the mouse SC. Their results predict matched changes in direction and orientation/axis preference: a vertical stimulus edge should preferentially induce horizontal orientation/axis preferences and enhance responses to up/down motion by recruiting direction-selective neurons tuned to that motion axis. Conversely, a horizontal edge should preferentially induce vertical orientation/axis preferences and responses to left/right motion. Because preferred directions and orientations were strongly related in our data, such an edge effect should be visible in both the direction and orientation analyses rather than masked by their overlap. Figure S2 therefore tests for the expected systematic relationship between RF distance from monitor edges and measured direction or orientation preferences. We found no such relationship.

      (2) Retinal boutons:

      The authors analyze retinal boutons and compare them to neurons in the SC. This comparison can be problematic since, in the case of boutons, the same RGC can be counted multiple times. The authors acknowledge the possibility that bouton terminals originating from the same axon may increase the correlation between boutons. This may also affect the interpretation of other results, such as the organization of direction and orientation boutons (e.g., maybe certain DS or OS retinal axons tend to have more branches?). The authors removed duplicate ROIs that were close to each other in neighboring imaging planes. They could do the same for boutons recorded in the same plane. Figure 4 would also benefit from this analysis.

      Our goal was to test how the distribution of direction and orientation/axis tuning in sSC neurons reflects the distribution of retinal input. This requires measuring both postsynaptic SC neurons and retinal axon terminals in the SC, which is a central strength of the study. Previous work has characterized the distribution of direction and orientation preferences in retinal ganglion cells, but largely from in vitro retinal recordings. By imaging retinal boutons in the SC, we could directly measure the tuning of the retinal input that is available to collicular neurons.

      For this question, we do not think it would be appropriate to remove multiple boutons merely because they may originate from the same RGC. If an RGC forms several boutons in the SC, these boutons are part of the retinal input received by the SC. Removing them would no longer quantify the distribution of retinal input boutons, but instead attempt to reconstruct the distribution of presynaptic RGCs, which is a different question. Similarly, if some DS or OS RGC types form more boutons than others, this is relevant for the functional composition of retinal input to SC rather than a sampling artifact to be removed.

      Our duplicate-removal procedure was intended only to avoid measuring the exact same structure more than once. For SC neurons, this required removing duplicate ROIs across neighboring imaging planes. For retinal boutons, the relevant analyses were performed within single imaging planes, so the same bouton was not sampled repeatedly across planes.

      (3) Eye movements and gaze raise two concerns:

      First, under head fixation, eye movements are typically small (Niell and Stryker, 2010). Yet, the moving gratings are expected to strongly drive OKR, and even small eye movements would shift receptive field location, which is crucial for the alignment between measured and expected preferred directions/orientations (Figs. 3, 7). Did they track eye movements? Can they rule out eye-movement-induced variability in receptive field location?

      Second, the authors write that longitudinal and latitudinal axes "were defined under the assumption that the mouse head is pitched downward by 29° in the ambulatory posture". They then report optimizing these axes by minimizing the discrepancy between predicted and measured preferences via artificial head tilting. What were the values they received for this optimal tilting, and how consistent were they across mice? Were the elevation and azimuth of the eye/gaze position directly measured?

      With respect to this comment, it would also be helpful to (i) cite a reference justifying the 29° head pitch assumption (e.g., Oommen and Stahl 2008), and (ii) specify clearly in the main text that the mice were awake and running during recordings.

      We tracked pupil position throughout a subset of two-photon imaging sessions. To directly assess whether eye movements affected estimated RF positions, we re-fitted RFs in all sessions with available pupil data while simultaneously estimating a linear transform from pupil displacement, measured in camera pixels, to gaze shift in visual degrees (Methods; Figure S2.1A–D). This procedure accounts for frame-by-frame gaze shifts when estimating RF locations. Although we did not directly measure absolute gaze position, the combination of RF locations, pupil videos, and the fitted pupil-to-gaze transform allowed us to infer gaze position and test whether gaze shifts were large enough to affect the comparison between measured preferences and RF-dependent model predictions.

      Despite the occurrence of eye movements, RF center positions were minimally affected by correcting for eye movements. The median Euclidean distance between corrected and uncorrected RF centers was 0.55° for retinal boutons and 0.71° for SC neurons (Figure S2.1E–H). For retinal boutons, 77% and 95% of RF center shifts were below 1° and 2°, respectively; for SC neurons, 66% and 89% were below 1° and 2°. These shifts are small relative to the typical RF diameter of ~10°. At the same time, the correction reduced median RF diameter by approximately 1° (updated diameters shown in Figure 2J), consistent with eye movements causing a modest broadening of uncorrected RF estimates. Thus, the correction affected RF structure in the expected direction, but did not substantially alter RF center positions.

      We also examined gaze position during drifting-grating presentation and found that gaze shifts were small and showed no systematic dependence on grating direction (Figure S2.1I). This argues against a substantial contribution of optokinetic responses to the measured direction or orientation preferences.

      Regarding head pitch, we agree that the pitch angle should ideally be measured directly. We did not record the exact pitch of each mouse when fixing the head plate during surgery. In general, mice were positioned with bregma lower than lambda to improve access to the SC. We therefore optimized the rotation angle α to account for this uncertainty and have added a plot showing the fitted α values for each mouse and recording modality (Figure S3I).

      We have also added the reference justifying the 29° ambulatory head-pitch assumption (Oommen and Stahl, 2008), and revised the main text to state explicitly that mice were awake and free to run during recordings.

      (4) Monitors edges and orientation selectivity mapping:

      The Introduction frames the literature as a controversy between map-like versus salt-and-pepper organisation of direction and orientation selectivity in mouse SC. The authors appropriately note that discrepancies across studies may reflect differences in experimental conditions. However, the manuscript does not sufficiently engage with the stimulus-boundary explanation that has recently emerged. Liang et al. (2023) demonstrated that orientation and direction columns in sSC can be induced by retinotopic alignment to stimulus edges rather than reflecting intrinsic columnar architecture. Similar edge-dependent orientation selectivity has now been reported in the visual thalamus (Yaakov et al., 2025), and edge-induced tuning was recently observed directly in retinal ganglion cell inputs to SC (Borges et al., 2025, bioRxiv). Given the accumulating evidence that stimulus discontinuities can induce "columnar" organization in SC, this possibility should be explicitly acknowledged and discussed, both in the Introduction and in the Discussion, as a potential unifying explanation for some of the conflicting findings in the field.

      We have revised the Discussion to explicitly discuss stimulus-boundary effects as a possible contributor to some previous reports of columnar organization. Liang et al. (2023) showed that stimulus edges can induce orientation and direction columns in sSC, and related aperture- or edge-dependent orientation effects have been reported in visual cortex, visual thalamus, and retinal boutons (Roth et al., 2018; Yaakov et al., 2025; Borges et al., 2025).

      We agree that this mechanism is important to consider. However, we do not think that monitor or stimulus edges provide a complete explanation for the discrepancies across studies. First, edge-induced orientation preferences are expected primarily for units whose RFs overlap or lie close to the stimulus boundary. This would affect only a subset of units in most experiments. Second, the geometry of the predicted effect is specific: vertical edges should induce horizontal orientation/axis preferences and up/down direction preferences, whereas horizontal edges should induce vertical orientation/axis preferences and left/right direction preferences. This pattern does not obviously explain several previously proposed map layouts, such as concentric orientation maps or reported large-scale direction biases dominated by upward, nasal, or temporal motion.

      We also tested for such effects in our own data. Because our stimuli were presented on monitors, any strong monitor-edge artifact should produce systematic changes in preferred direction or orientation with RF distance to vertical or horizontal monitor edges. We did not observe such relationships (Figure S2). Moreover, our main analyses excluded units whose RF centers were within 5° of a monitor edge. Thus, while stimulus-boundary effects are an important potential contributor to some reported columnar patterns, they are unlikely to account for the organization observed in our data.

      (5) Cardinal axes:

      Although mentioned already in the title, these directions are not always cardinal. For example, the peak of the overrepresented naso-temporal direction is actually ~30 degrees apart from this direction (Figures 1N-Q). Please clarify the term cardinal with respect to these results.

      We agree that our previous use of the term “cardinal” was confusing. We have revised the manuscript so that “cardinal” is used only for fixed stimulus directions and orientations aligned with horizontal and vertical angles.

      When referring to the four direction or orientation preferences predicted by the topographic organization, which vary with visual-field location and therefore are not necessarily aligned with fixed cardinal angles, we now use the term “topographic preferences.” We have revised the title, abstract, Introduction, Results, and Discussion accordingly.

      (6) Averaging over direction or orientation preference:

      Figures 4E-H show the mean direction and orientation preferences obtained by averaging across boutons within circular patches of 10° diameter. So, cells with opposite preferred direction/orientation may create a completely new mean preferred direction/orientation that was never encountered? This may be misleading, no?

      We agree that circular means can be misleading when local preferences are broadly distributed or multimodal. For this reason, we show both the preferences of individual units (Figure 4A–D) and the mean preference maps (Figure 4E–H). We included the mean maps because related approaches have been used in previous studies, including smoothed single-cell maps (De Malmazet et al, 2018, 2024) and population imaging methods such as widefield or intrinsic imaging (Li et al, 2020; Feinberg and Meister, 2014), which effectively average responses over local populations. We agree that such approaches can produce an apparent smooth map even when local tuning is heterogeneous, and we have revised the text to make this clearer.

      Importantly, our interpretation does not rely on the mean maps. We quantified preference consistency within each 10° patch using inverse circular variance. If each visual-field location were dominated by a single direction or orientation preference, consistency should exceed the shuffled control. Instead, especially for SC neurons, local consistency was low and generally indistinguishable from the null distribution.

      Minor points:

      (1) The authors use forward/backward in Figure 1B; naso-temporal direction in the text; advance-retreat in Figure 3. It would be better to be consistent.

      We have revised the text and figures to use the terms nasal and temporal consistently instead of forward and backward. We retained the terms advance and retreat, because these refer to the established names of direction-selective retinal ganglion cell classes aligned with optic flow during forward or backward translation, and therefore describe a different convention from the nasal/temporal stimulus directions.

      (2) Figure 3L-O: light grey is barely detectable (also in other figures).

      We updated the color for increased contrast.

      (3) Page 6, bottom: "(Figure 1N, V)" - there is no Figure 1V.

      We corrected that.

      (4) Discussion: "Our results demonstrate that the topographic organization of direction and orientation tuning in mouse SC was largely inherited from the retina and then transformed within SC". I would argue that inheritance was not shown here. They showed correlations.

      We have revised this statement to avoid implying that inheritance was directly demonstrated by causal manipulation. The Discussion now states that the topographic organization previously described in the retina is reflected in retinal input to the SC and progressively transformed across SC neurons.

      (5) Figure S3 caption: fix "Error! Reference source not found".

      We corrected that.

      Reviewer #3 (Recommendations for the authors):

      Below are additional small points that could also benefit the paper.

      (1) Line 41. Kasai and Isa (2021) did show the presence of both DS and OS clustering over collicular distances of at least 100 μm, which could extend up to 300 μm in the awake state.

      We agree that Kasai and Isa (2021) reported significant local similarity for both direction and orientation preferences. We cited this study in the context of weak clustering because the magnitude of the reported effect is small compared with studies claiming strong functional maps.

      We have revised the Introduction to reflect their findings more accurately. Specifically, we now also mention weak orientation clustering, whereas the previous text referred only to weak direction clustering.

      (2) Line 77. Could you please provide a movie of the stimulus being presented on the three monitors to get an idea of the operated transformation into spherical visual coordinates and then mapped onto the flat monitor surface.

      The spherical-to-monitor mapping used by BonVision is illustrated in Lopes et al. (2021), in particular in Figure 1—figure supplement 1. We have now clarified in the Methods the specific mapping used, also in response to Reviewer 1, because there is no unique way to project spherical visual coordinates onto flat monitor surfaces. A checkerboard stimulus spanning the three-monitor setup used in our two-photon experiments would appear approximately as shown in Author response image 2.

      Author response image 2.

      (3) It might be important to note that the way the stimuli are presented around the mouse produces a different pattern of motion on the left and right eyes. A forward stimulus on the right eye corresponds to a backwards stimulus on the left eye if the gratings are moving alongside the monitors. This would mimic rotation movements rather than advancing or retreating movements. This likely doesn't interfere with the results, but it might be worth mentioning that a similar setup was used in Chen et al. (2021), who also found a weak functional clustering. There could potentially be some source of inter-colliculi interactions at play.

      We agree that our drifting-grating stimuli mimic rotational rather than translational motion. This was indicated visually in Figure 1B and described in the corresponding figure caption. We did not intend to interpret these stimuli as naturalistic advancing or retreating optic-flow stimuli.

      We do not think that this aspect of the stimulus protocol explains our results. First, Inayat et al. (2015), from the same group as Chen et al. (2021), used a different arrangement in which stimuli were presented only on a single monitor in the contralateral visual field, yet likewise found no evidence for direction-preference clustering in mouse SC. Second, although binocular or interhemispheric interactions could in principle influence SC responses, we have not found any evidence in the existing literature that such interactions systematically shape visual direction or orientation preferences in a way that would explain the weak clustering observed here. This supports the view that the use of three monitors did not substantially alter the measured tuning preferences.

      (4) Figure1 N-Q, please provide polar histograms.

      We understand that polar histograms are commonly used to visualize direction and orientation preferences. We chose linear histograms intentionally, because they allow the direction and orientation axes in Figure 1N–Q to align with the tuning-curve plots above and below them, making the corresponding preferences directly comparable across panels. The circular nature of the variables is preserved in the analysis, but the linear display makes the figure layout easier to compare.

      (5) Line 125 says that RFs were mapped, but there is no indication of how and what mapping means. Neither is there any clue in the methods. Is the RF mapping done by physically measuring the spherical angle of the RF location on the screen according to the mouse head angle? Please describe how RF were mapped.

      The original and current Methods include a subsection titled “Mapping of receptive fields,” but it may have been easy to overlook. We have now changed the formatting of the subheadings so they stand out more.

      Briefly, RFs were estimated from responses to sparse noise stimuli presented at known positions in spherical visual coordinates. The fitted RF centers in this coordinate system were then used as the visual-field locations for subsequent analyses. In addition, we now account for eye movements during RF mapping, as described in the following Methods subsection, “Correction for eye movements during receptive field mapping.”

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      The manuscript by Mengxing et al., reports an assessment of three first-order thalamic nuclei (auditory, visual, somatosensory) in a 3 x 2 factorial design to test for specificity of responses in first-order thalamic nuclei to linguistic processing particularly in the left hemisphere. The conditions are reading, speech production, and speech comprehension and their respective control conditions.

      The authors report the following results:

      (1) BOLD-response analyses: left MGB linguistic vs non-linguistic significant; left LGN linguistic vs non-linguistic significant. There is no hemisphere x stimulus interaction.

      (2) MVPA: left MGB linguistic vs. non-linguistic significant; bilateral VLN linguistic vs. non-linguistic significant; significant lateralisation in MGB (left MGB responses better classified linguistic vs. non-linguistic in contrast to right).

      (3) Functional connectivity: there is, in general, connectivity between the thalamic ROIs and the respective primary cortices independent of linguistics.

      Strengths:

      The study has a clear and comprehensive design and addresses a timely topic. First-order thalamic nuclei and their interaction with the respective cerebral cortex area are likely key to understanding how perception works in a world where one has to compute highly dynamic stimuli often in an instant. Speech is a prime example of an ecologically important, extremely dynamic, and complex stimulus. The field of the contribution of cerebral cortex-thalamic loops is wide open, and the study presents a solid approach to address their role in different speech modalities (i.e., reading, comprehension, production).

      Weaknesses:

      I see two major overall weaknesses in the manuscript in its current form:

      (1) Statistics:

      Unfortunately, I have doubts about the solidity of the statistics. In the analyses of the BOLD responses, the authors do not find significant hemisphere x stimulus interactions. In my view, such results would pre-empt doing a post-hoc t-test. Nevertheless, the authors motivate their post-hoc t-test by 'trends' in the interaction and prior hypotheses. I see two difficulties with that. First, the origin of the prior hypotheses is somewhat unclear (see also the comment below on hypotheses), and the post-hoc t-test is not corrected for multiple comparisons. I find that it is a pity that the authors did not derive more specific hypotheses grounded in the literature to guide the statistical testing, as I think these would have been available, and the response properties of the MGB and LGN also make sense in light of them. In addition, I was wondering whether the MVPA results would also need to be corrected for the three tests, i.e., the three ROIs.

      We thank the reviewer for prompting us to revisit this, as it led us to identify and correct a specification error in the original ROI ANOVAs. The original ROI ANOVAs had been fitted without subjects as a within-subjects factor, treating each subject's observations as independent. For a fully within-subjects design, this is a genuine error: it pools within- and between-subject variance into a single residual and uses an incorrect error term and degrees of freedom. We have re-run all ROI analyses as repeated-measures ANOVAs with subjects as a within-subjects factor, on the same data and contrasts.

      For the modality main effects, all three nuclei retain a significant effect of Modality under the corrected model (LGN F(2,76) = 30.02, p < 0.001, η<sup>2</sup>_p = 0.441; MGN F(2,76) = 4.56, p = 0.014, η<sup>2</sup>_p = 0.107; VLN F(2,76) = 42.28, p < 0.001, η<sup>2</sup>_p = 0.527). The corrected F-values are lower than originally reported because the original analyses used an inflated error df (465, from treating observations as independent) rather than the correct within-subjects df (76); the tests are therefore more conservative. We also replaced the original Tukey HSD post-hoc tests, which assume independent groups, with paired comparisons (Holm-corrected within each nucleus). The qualitative pattern is unchanged.

      For the Stimuli × Hemisphere analysis, the corrected model yields a significant MGN interaction (F (1,38) = 8.63, p = 0.006, η<sup>2</sup>_p = 0.185). The LGN (F (1,38) = 1.02, p = 0.318, η<sup>2</sup>_p = 0.026) and VLN (F (1,38) = 0.52, p = 0.474, η<sup>2</sup>_p = 0.014) interactions remain non-significant, consistent with the original report. We also now report the Stimuli main effects, as the reviewer requested: the LGN shows a significant overall linguistic effect across hemispheres (F(1,38) = 4.44, p = 0.042), consistent with the reviewer's observation that a main effect of stimuli appeared present in the LGN.

      The significant MGN interaction directly addresses the reviewer's concern: the left-MGN comparison is the appropriate decomposition of a reliable interaction, not a test performed after a non-significant omnibus result. This prediction was also motivated a priori by prior work on the left auditory thalamus in speech recognition and developmental dyslexia, which we set out in detail in our response to the Hypotheses comment below, as well as in the revised manuscript version (see pp. 5).

      For the LGN, the interaction is not significant, and we now present the left-LGN comparison (t (38) = 2.43, p = 0.020, d_z = 0.39) as a directional, theoretically motivated test rather than as a follow-up to a significant interaction. As detailed in our response to the Hypotheses comment, the prediction has two components: that the LGN is modulated by linguistic visual content at all (well supported), and that this modulation is left-lateralised (motivated more indirectly, and which we therefore treat as the more exploratory element). We interpret the LGN left-lateralisation with corresponding caution.

      The hemisphere comparisons are corrected for multiple comparisons using the Holm–Bonferroni procedure across the two tests; both remain significant after correction (left MGN p_Holm = 0.009; left LGN p_Holm = 0.020). The corrected statistics for all nuclei are reported in the revised Methods and Results sections of the manuscript (see pp. 10, 14, 15).

      Regarding the analysis, they showed whether the individual classification results are different from chance using a permutation test. Therefore, these are significant tests, but they do not compare results between conditions or different distributions. Here, we just built a null distribution to estimate the performance of the classifier for each ROI. Thus, multiple comparison corrections do not apply to these analyses.

      Hypotheses:

      In my view, it is relatively unclear where the hypotheses precisely come from. For example, the paragraph on the hypotheses in the introduction (p. 6-7) is devoid of references. I also have the impression that the hypotheses are partly not taking into account previous reports on first-order thalamic nuclei involvement in linguistic vs. non-linguistic processing. For example, the authors test for lateralisation of linguistic vs. non-linguistic responses in all nuclei. However, from previous literature, one could derive the hypothesis that the lateralisation in MGB for speech might be there - previous work shows, for example, that speech recognition abilities consistently correlate with left MGB only (von Kriegstein et al., 2008 Curr Biol; Mihai et al., 2019 eLife). In addition, the involvement of the MGB in speech-in-noise processing is present in the left MGB (Mihai et al., 2021, J Neuroscience). Developmental dyslexia, which is supposed to be based on imprecise phonological processing (Ramus et al., 2004 TiCS), has alterations in left MGB (Diaz et al., 2012 PNAS; Galaburda et al., 1994 PNAS) and left MGB connections to planum temporale (Tschentscher et al., 2019 J Neurosci) as well as altered lateralisation (Müller-Axt et al., 2025 Brain). Conversely, in the LGN, I'm not aware of any studies showing lateralisation for speech. See, for example, Diaz et al., 2018, Neuroimage, where there are correlations of LGN task-dependent modulation with visual speech recognition behaviour in both LGNs. Thus, based on this literature, one could have predicted the result pattern displayed, for example, in Figure 3A at least for MGB and LGN.

      In summary, the motivation for the different hypotheses needs to be carved out more and couched into previous literature that is directly relevant to the topic. The above paragraph is, of course, my view on the topic, but currently, the paper lacks different literature as references to fully understand where the hypotheses are derived from.

      We appreciate this point and agree that the hypothesis section in the original manuscript needed to be more specifically grounded. We have now revised the Introduction and have better grounded the hypotheses, organising the supporting evidence into two converging lines (pp. 3-5).

      The first concerns the left MGN. In neurotypical listeners, task-dependent modulation of the auditory thalamus during speech recognition is bilateral, but its amplitude in the left MGB specifically tracks speech-recognition ability (von Kriegstein et al., 2008; Mihai et al., 2019), and this modulation localises to the left ventral MGB under more demanding speech-in-noise conditions (Mihai et al., 2021). This evidence is complemented by left-lateralised alterations of the auditory thalamus in developmental dyslexia, including reduced left MGB responses during phoneme processing that correlate with diagnostic scores (Diaz et al., 2012) and reduced left MGB-planum temporale structural connectivity (Tschentscher et al., 2019). On this basis, our prediction of left-MGN involvement was directly motivated by prior work, and the pattern shown in Figure 3A, as the reviewer notes, broadly aligns with what this literature would lead one to expect. As discussed in our previous response to the Statistics comment, the corrected Stimuli × Hemisphere analysis confirms this prediction, revealing a significant MGN interaction and a significant simple effect in the left MGN.

      The second issue concerns the LGN, for which we distinguish between two predictions supported by different levels of empirical evidence. First, the prediction that the LGN is modulated by the linguistic content of visual stimuli is well motivated. Rather than acting as passive relays, first-order thalamic nuclei are subjected to top-down corticothalamic modulation (Mumford, 1991; Sherman & Guillery, 1996; Sillito et al., 1994), and Díaz et al.’s (2018) study showed that LGN responses are modulated during visual speech recognition. Consistent with this evidence, we observed a significant overall (bilateral) effect of linguistic content in the LGN. By contrast, the more specific prediction that this modulation would be left-lateralised is based on more indirect evidence. It follows from the strong left-lateralisation of reading and language processing at the cortical level, which may extend upstream to the thalamic visual relay, together with findings from the dyslexia literature. Morphometric studies have reported reduced left LGN volume in developmental dyslexia (Giraldo-Chica et al., 2015), although this finding has not been consistently replicated (Müller-Axt et al., 2017). More robust evidence comes from studies reporting left-lateralised alterations in LGN connectivity and function, including reduced left LGN–V5/MT connectivity correlated with rapid naming ability (Müller-Axt et al., 2017) and altered leftward functional lateralisation of the magnocellular LGN (Müller-Axt et al., 2025). However, existing functional studies report bilateral rather than left-lateralised LGN involvement during language processing (Díaz et al., 2018), and Müller-Axt et al. (2025) also note that the hemispheric origin of the magnocellular LGN lateralisation cannot be fully resolved. We therefore present the prediction of left-lateralised LGN modulation as theoretically motivated but exploratory, whereas the prediction of LGN involvement per se rests on considerably stronger empirical support. The revised Introduction now makes this distinction explicit and cites the relevant literature. We consider that the predictability of the lateralisation pattern from prior work, which the reviewer rightly highlights, is not in tension with the contribution of the present study. Our aim was not to establish that first-order thalamic nuclei participate in language processing per se, but rather to provide the first comprehensive examination of all three first-order sensory relay nuclei across reading, speech comprehension, and speech production within the same group of participants.

      Reviewer #2 (Public review):

      Summary:

      This study investigates the involvement of first-order thalamic nuclei in language-related tasks using task-based fMRI in a 3 × 2 design contrasting linguistic and non-linguistic versions of reading, speech comprehension, and speech production. By focusing on the LGN, MGN, and VLN and combining activation, connectivity, lateralization, and multivariate pattern analyses, the authors aim to characterize modality-specific and language-related thalamic contributions.

      Strength:

      A major strength of the work is its hypothesis-driven and multimodal analytical approach, and the modality-specific engagement of first-order thalamic nuclei is robust and consistent with known thalamocortical organization. This is a very sound study overall.

      Weaknesses:

      However, several conceptual issues complicate the interpretation of the results as evidence for linguistic modulation per se. A central concern relates to the operationalization of the linguistic versus non-linguistic contrast. In the present design, linguistic and non-linguistic stimuli differ along multiple dimensions beyond linguistic content. For example, written words and scrambled images differ in spatial frequency structure, edge composition, contrast regularities, and familiarity, while intelligible speech and acoustically scrambled sounds differ substantially in temporal and spectral statistics. This is particularly relevant given that first-order thalamic nuclei such as the LGN are known to be highly sensitive to low-level sensory properties. As a result, observed differences in thalamic responses may reflect sensitivity to stimulus properties rather than linguistic processing per se, and this limits the specificity of claims regarding linguistic modulation.

      We thank the reviewer for this comment and agree that stimuli differ in different low-level aspects beyond the linguistic versus non-linguistic nature of the stimuli. Rather than comparing multiple different types of stimuli in each modality to isolate effects, for example, at the visual level of spatial frequency structure, edge composition, contrast regularities and familiarity, the main goal of the present study was to examine within the same sample differential involvement of first-order thalamic nuclei as a function of language modality and the linguistic versus non-linguistic nature of the stimuli. As the reviewer points out below, the contribution of the present work lies less in establishing thalamic involvement in language or a single language modality (reading, speech comprehension, speech production) per se. Here our main goal was to examine these three modalities within the same study and with the same group of participants. And, so, it would have been extremely hard to include all the many types of stimuli needed to contrast or isolate these low-level aspects in every single modality, as we have done in previous work, for example on reading (e.g., Lerma-Usabiaga, Carreiras & Paz-Alonso, 2018). It is also true that the non-linguistic stimuli we used have been widely used as standard control (perceptual, and not lexical) conditions in previous studies (see for instance Lerma-Usabiaga et al., 2018; Mano et al., 2015; Sánchez et al., 2023; Vinckier et al., 2007, for the reading modality) and that the left-lateralized linguistic versus non-linguistic modulation that we found is difficult to reconcile with a purely low-level account, where as far as we know effects would have been bilateral.

      Based on this comment from the reviewer, we have now included as a limitation of the study in the revised version of the manuscript that the stimuli differ on other low-level sensory properties beyond their linguistic versus non-linguistic nature and that future studies may want to further investigate all these other aspects in each of the modalities examined in the present work (see p. 22).

      Relatedly, although the manuscript frequently refers to effects "depending on the linguistic nature of the stimuli," the statistical evidence for linguistic versus nonlinguistic modulation is uneven across analyses. Whole-brain contrasts collapse across stimulus type and primarily test modality effects. Similarly, the primary ROI analyses of activation amplitude are collapsed across linguistic and nonlinguistic conditions and convincingly demonstrate modality-specific engagement of thalamic nuclei, but do not in themselves provide evidence for linguistic modulation. Linguistic effects emerge only in later, more targeted analyses focusing on hemispheric lateralization and multivariate pattern classification, and these effects are nucleus-, modality-, and analysis-specific rather than general. Taken together, these results suggest that linguistic modulation constitutes a secondary and selective finding, whereas modalityspecific task engagement represents the primary and most robust outcome of the study.

      We thank the reviewer for this observation, which in our view reflects the intended logic of the study.

      The whole-brain contrasts and the primary ROI activation analyses (across modalities) were not designed to demonstrate linguistic modulation. Their role was twofold: they confirm modality-specific organisation of the first-order relay nuclei (LGN for reading, MGN for speech comprehension, VLN for production), here shown for all three nuclei in the same participants. And they validate that our ROIs were correctly identified and engaged under the same task conditions as the subsequent analyses. As the reviewer notes, this modality-specific engagement is the most robust outcome of these analyses, which it was expected since it follows directly from known thalamocortical organisation, and it is the foundation on which the study's novel question is then tested.

      The linguistic modulation is a more specific hypothesis, and it is tested in the analyses designed to address it: the Stimuli × Hemisphere ROI analyses and the multivariate classification. That the linguistic effects emerge in these targeted analyses rather than in the modality contrasts is therefore by design: the two sets of analyses ask different questions. We agree the linguistic effects are more selective than the modality effects. They are concentrated in the comprehension tasks, left lateralised, and strongest in the MGN. But this selectivity forms a coherent and interpretable pattern consistent with left-hemisphere language lateralisation, rather than a diffuse effect.

      We have revised the manuscript, and we think that the main different findings of the study are adequately reflected in the abstract and discussion sections. We have now made subtle changes along the revised version of the manuscript to make even clearer that the modality analyses are framed as a combined replication and ROI-validation step, and the linguistic modulation is foregrounded as the study's primary contribution.

      An additional interpretational issue concerns task engagement and attention. The tasks differ substantially in cognitive demands (e.g., passive reading and listening versus overt speech production), and linguistic and non-linguistic blocks may differ systematically in salience or engagement. This is particularly important given prior evidence, cited by the authors, that LGN and MGN activity can be modulated by task demands and attention. In the absence of behavioral measures indexing task engagement or compliance, it is difficult to determine whether differences between linguistic and non-linguistic conditions reflect linguistic processing per se or are mediated by attentional factors.

      We thank the reviewer, and we acknowledge that we did not collect behavioural measures of task engagement, and that linguistic and non-linguistic stimuli may differ in attention or engagement as well as in linguistic content. However, attentional allocation is in part intrinsic to linguistic processing. Comprehending a meaningful word entails allocating attention in a way that processing meaningless input does not. Cognitive functions are not a unitarity phenomenon, and it is basically impossible to tease them apart into every single element in it. For instance, reading involves visual perception, orthographic processing, phonological processing, semantics, attention, and memory. The main goal of the present study is not to isolate every single possible element. At the level of our claim, that the thalamus is differentially engaged depending on the linguistic nature of the stimuli, these attentional differences are part of the phenomenon rather than a confound to be removed. Isolating more specific levels of linguistic processing, for instance, lexical processing, via word versus pseudoword contrasts, or orthographic processing, via consonant strings, would require designs targeting those finer distinctions, which we note in the Discussion section as a direction for future work; these address narrower questions than the linguistic-versus-non-linguistic distinction examined here.

      A further consideration is that some of the effects we found are left-lateralised. A general difference in attention or engagement between conditions would not necessarily predict a specifically left-lateralised thalamic response. In our view, the asymmetry instead points to language-related lateralised processing rather than to generic differences in engagement. But of course, more studies examining more conditions and aspects in each modality are needed. The present study represents just one contribution towards that goal.

      We added some lines discussing this point in the Discussion section of the revised manuscript (pp. 20-22).

      Finally, while the manuscript emphasizes the novelty of evaluating thalamic involvement in language, thalamic contributions to language have been documented previously in both lesion and functional imaging studies. The contribution of the present work, therefore, lies less in establishing thalamic involvement in language per se, and more in its focus on specific first-order nuclei, its multimodal design, and its combination of univariate, connectivity, and multivariate analyses. Moderating claims of novelty would help place the findings more clearly within the existing literature.

      We thank the reviewer for this comment and the time dedicated to this review. We have moderated our novelty claims. We removed statements asserting priority for thalamic involvement in language, including the claim that no prior study had reported linguistic modulation at the level of these nuclei (also raised by Reviewer #1), and we no longer frame the study as the "first" to examine these questions.

      We now frame the contribution as a comprehensive examination of all three first-order relay nuclei (LGN, MGN, VLN) across reading, speech comprehension, and speech production in the same participants, combining univariate activation, functional and structural connectivity, and multivariate pattern analyses. Within this design, the differential engagement of these nuclei depending on the linguistic nature of the stimuli, left-lateralised, is the finding we foreground, situated within rather than asserted as priority over the existing literature on thalamic involvement in language.

      We have revised our abstract and conclusion to reflect this change (p. 2, p. 23)

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      There are a couple of things that could be done to strengthen the manuscript besides the ones that I've already outlined in the public review.

      (1) ROIS

      In our experience, the Iglesias et al. (2018) ROIs are unfortunately spatially imprecise, and it would be reassuring to test the results with other ROIs, e.g., Sitek ROIs for MGB and Müller-Axt ROIs for LGN.

      We thank the reviewer for this suggestion. In the present study ROI analyses were conducted in each participant's native anatomical space. Adopting the Sitek or Müller-Axt ROIs would require warping externally defined templates into native space, which introduces interpolation and registration errors that can be particularly consequential for structures of this size. Working from native-space segmentations therefore avoids a source of spatial distortion.

      We developed Iglesias et al’s (2018) atlas and its companion segmentation in our lab (Iglesias, … & Paz-Alonso, 2018), which has been reviewed, validated, and widely used in the neuroimaging literature. Although we can agree that for some nuclei, especially the smaller ones, there can be some spatial imprecisions (as in practically any available atlas of thalamic nuclei), given the type of analyses and resolution used in the present work, as well as its main goal (i.e., examining the involvement of three first-order nuclei in three main language modalities within the same study sample) we have retained the native-space from Iglesias et al.’s 2018 segmentation and note the choice in the Methods section.

      Nevertheless, we agree with the reviewer that, for investigations specifically using higher functional resolution and targeting further fine-grained subregions within these ROIs (e.g., vMGB, dMGB, and mMGB; VLa and VLp), a different segmentation strategy and, where feasible, ultrahigh-field (7 T) MRI would be ideal for more spatially precise delineations.

      We provided details in the ROI definition section to show the volumes of our ROIs and the comparison with relevant reports from other labs (p. 10).

      (2) Introduction

      It has now been decades since the 'relay nuclei' are not only relay (e.g., Sillito 1994; Sherman&Guillery 1996). So, as someone in the field, an introduction based on 'first-order thalamic nuclei are not a relay' seems a bit old-fashioned. Conversely, it would be great to review in depth the relevant literature on the topic. In my view, this would also streamline the introduction. In that context, I would appreciate a more thorough treatment of previous literature. For example, it is wrong that "Similar attention-related effects have also been observed in the MGN (e.g., Mihai et al., 2021; von Kriegstein et al., 2008)". These are not attention-related effects; in fact, the two tasks are in many studies specifically designed to have the same task difficulty to avoid attention-related effects. In the end, these tasks tap into the difference between linguistic speech recognition tasks vs. control tasks (paralinguistic, such as voice recognition or completely different, such as loudness recognition). At another point, the same studies are cited as studying speech comprehension, which, in my view, is also wrong, as I don't think that one can label one-back syllable recognition tasks as 'speech comprehension'.

      We have revised the Introduction to situate the work within the contemporary corticothalamic framework from the outset, drawing on the relevant literature (e.g. Sillito et al., 1994; Sherman & Guillery, 1996), rather than framing it against a passive-relay model.

      We thank the reviewer for pointing out the “attention-related” clarification regarding Mihai et al.’s (2021) and von Kriegstein et al.’s (2008) studies. We have revised the relevant sentence to describe these studies as demonstrating task-dependent modulation during speech recognition relative to non-speech control tasks, and removed the earlier framing that grouped them with attention effects. Also, we have revised the Introduction to distinguish our passive listening paradigm from the recognition-based paradigms (e.g., one-back syllable tasks) used in prior work, reserving "speech comprehension" for the former (see pp. 3-4).

      (3) MGB or MGN

      The MGB is called MGB because it contains not only first-order, but also second-order structures. With the resolution of 2.4 mm isotropic, it is impossible to dissociate the first-order MGB in my view.

      We thank the reviewer for this point and agree that at 2.4 mm isotropic resolution the ROI cannot be restricted to the first-order ventral subdivision alone. We have addressed this directly in the Methods section (see pp. 9-10) where the ROI is defined, noting that the segmentation derives from Iglesias et al. (2018) and that, at our functional resolution, contributions from higher-order subdivisions cannot be excluded; our findings therefore pertain to the MGN as a whole. On terminology, the manuscript uses MGN throughout, consistent with the atlas and segmentation labelling.

      (4) Reporting details

      (a) I was missing important information for the results, such as tables for coordinates (ROIs and results), volumes for the ROIs, and comparison of ROI volumes to volumes previously reported in the literature.

      As our ROIs were defined in each participant's native anatomical space rather than in a common template, MNI coordinates are not applicable. We have, however, added a sentence reporting the mean ± SD ROI volume (mm³) for each nucleus across participants, derived from the individual FreeSurfer segmentations, which characterises the size and consistency of the ROIs used. We included the ROI volumes and comparison with previous reports on p. 10.

      (b) Another point of the statistics is that the results should be reported more comprehensively: For example, it looks a bit as if there were a main effect of linguistics in the LGN, but main effects were not reported (why?) as far as I can see.

      We have added the Stimuli main effect and the Stimuli × Hemisphere interaction from the corrected ANOVA for all three nuclei to the revised Results. In brief: the LGN shows a significant overall linguistic advantage (linguistic > non-linguistic) across both hemispheres, with no significant interaction; the MGN shows no significant main effect but a significant Stimuli × Hemisphere interaction, indicating a linguistic advantage that is strongly hemisphere-specific (present in the left, absent in the right) and directly validating the left MGN comparison. The full statistics are now reported in the revised version of the manuscript (see p. 15).

      (c) Please report effect sizes throughout the study (e.g., page 7, bottom, please check the whole manuscript).

      We have added partial η<sup>2</sup> for all ANOVA effects and Cohen's d for all planned comparisons throughout the revised manuscript.

      (d) In my view, it is impossible to understand how the control stimuli were created based on the current description. For example, what does 'temporally shifting the auditory signals' mean? How much? In what direction? It would be helpful to show example stimuli.

      We agree the original description was insufficient. The non-linguistic auditory stimuli were created using a custom matlab script, which was uploaded along with the dataset to osf repository upon finalization of the manuscript. For each real word, the original waveform was temporally randomized by shuffling the data points of the audio vector in a pseudo-random permutation (randperm). This process destroyed the phonological and semantic structure of the speech while perfectly preserving the duration, sampling rate, and total acoustic energy of the original stimuli. We have clarified this procedure in the Methods (p. 6).

      (e) How far was it assessed that the reading task in the SP was not confounded by eye movements?

      We thank the reviewer. Two points address this concern. First, within the reading modality, both conditions required the same directed fixation on the screen (words in the linguistic condition, scrambled images in the non-linguistic condition), so a systematic eye-movement difference between conditions is not expected. Second, and more directly, the speech comprehension and speech production tasks were performed with eyes closed, yet the left MGN showed a reliable linguistic effect; an eye-movement account cannot explain a linguistic modulation arising under eyes-closed conditions. We have clarified this in the Methods (pp. 7).

      (f) Motivation for choosing the particular functional connectivity method unclear. Why not DCM? Why not PPI?

      We thank the reviewer and have added a methodological justification of the functional connectivity method choice to the Methods section (p. 11). Our connectivity question concerned whether each first-order nucleus maintains coupling with its corresponding primary cortex during the relevant language task, that is, the magnitude of within-condition coupling, for which the beta-series correlation method (Rissman et al., 2004) provides a direct estimate of absolute connectivity within a given condition. PPI or gPPI, by contrast, estimates the change in coupling attributable to a psychological variable, i.e., condition-specific differences in connectivity rather than the absolute coupling within a condition; it was therefore less directly suited to our primary question. We additionally tested the linguistic-versus-non-linguistic difference using simple-effects comparisons on the subject-level z-transformed beta-series values, so our design does not preclude detecting condition differences (beta-series and PPI are well suited to comparable condition contrasts; Di et al., 2021). DCM would be the appropriate framework for questions of directionality and effective connectivity; however, we had no a priori directional model of thalamo-cortical interactions to motivate the strong model specification that DCM requires. We accordingly note in the Discussion section that the absence of linguistic modulation in beta-series coupling does not preclude its detection with effective-connectivity approaches such as DCM, which we flag as a direction for future work (p. 22).

      (g) Green and red in figures can be difficult for the ca. 5% of the population that is red-green blind.

      We have revised all relevant figures to use colourblind-accessible palettes.

      (h) In multiple instances, references are missing. One point is the paragraph on the hypotheses I already mentioned, but also, for example, page 19 'language models'. Unclear which ones these are. There are multiple instances of this in the text, which I have not listed here for the sake of time, but proofreading is needed.

      We have added the missing references, including in the hypothesis paragraph and for the "language models" reference, and have proofread the manuscript in full to address remaining instances (e.g. pp. 19, 21).

      (i) Page 21 'yet no study has previously reported the modulation effect of linguistic processing at the level of the thalamic nuclei'. I don't think that this is correct. Linguistic modulation of first-order thalamic nuclei was first shown in two experiments in von Kriegstein et al., 2008, Curr Biol. I also don't understand why the authors emphasise so much 'the first' on this aspect. I think that the manuscript here does not need to be a 'first' on this aspect, as the design is fantastic and very comprehensive and could be an important novel contribution to the field in my view.

      We thank the reviewer and have revised this accordingly. We have removed the sentence claiming that no prior study had reported linguistic modulation at the level of these nuclei. We retain the more circumscribed and accurate statement that the main goal of this study is to demonstrate simultaneous modulation of all three first-order relay nuclei within a single experimental paradigm spanning reading, speech comprehension, and speech production. We have shifted the framing away from priority claims toward the comprehensive cross-modality design as the contribution (pp. 2 and 23).

      (j) "Study is in accordance with the Declaration of Helsinki". This statement is incorrect, given that the study has not been preregistered as far as I can see.

      We thank the reviewer. We have revised the Ethics statement and dropped the statement about the Declaration of Helsinki (p. 5).

      (j) References (that might be a bit harder to find)

      Sherman SM, Guillery RW. Functional organization of thalamocortical relays. J Neurophysiol. 1996 Sep;76(3):1367-95. doi: 10.1152/jn.1996.76.3.1367. PMID: 8890259.

      Sillito AM, Jones HE, Gerstein GL, West DC. Feature-linked synchronization of thalamic relay cell firing induced by feedback from the visual cortex. Nature. 1994 Jun 9;369(6480):479-82. doi: 10.1038/369479a0. PMID: 8202137.

      Thank you!

    1. Author response:

      The following is the authors’ response to the original reviews.

      Joint Public Review:

      (1) Distinction between FoxO expression and activation

      The Public Review noted that the original manuscript did not consistently distinguish FoxO expression levels from activation status.

      We agree. We revised the terminology throughout the manuscript to distinguish changes in FoxO abundance from stress-induced nuclear translocation or accumulation. Where the experiments assess subcellular localization, we now describe the result specifically as nuclear translocation or nuclear accumulation rather than inferring increased FoxO expression or transcriptional activity. Broader references to FoxO regulation or signaling are retained only in integrative contexts and do not imply that localization alone establishes transcriptional activation.

      (2) Rationale for the selection of stressors

      The Public Review requested a clearer rationale for using different environmental stressors across the experimental systems.

      We clarified that the stressors were selected to represent major classes of challenges encountered by airway epithelia, including altered oxygen availability, temperature stress, oxidative stress, and chronic airborne exposure. The aim was not to establish identical responses to every stressor in every model, but to test whether FoxO nuclear redistribution represents a recurring epithelial response to diverse environmental challenges. This rationale is now stated more clearly in the revised manuscript.

      (3) Use of the term "FoxO signaling"

      The Public Review noted that the manuscript frequently referred to "FOXO signaling" although direct signaling readouts were not measured in all experiments.

      We agree and have revised the terminology accordingly. In experiments based on imaging, we now refer specifically to FoxO nuclear translocation or nuclear accumulation. We avoid using localization alone as evidence for a complete signaling cascade and have moderated mechanistic language throughout the Results and Discussion.

      (4) Reliance on immunostaining and nuclear localization

      The Public Review emphasized that nuclear localization provides evidence of stress-responsive FOXO redistribution but, by itself, does not define the underlying regulatory mechanism.

      We agree with this limitation and now state it explicitly. The localization experiments are interpreted as evidence of stress-responsive FoxO redistribution, whereas mechanistic conclusions are based primarily on the Drosophila genetic and functional experiments. We also expanded the Limitations section to distinguish localization-based observations from direct functional evidence and to identify biochemical analyses of FoxO regulation as an important direction for future work.

      (5) Lack of airway-specific dFoxo loss-of-function experiments

      The Public Review identified the use of constitutive dfoxo mutants as a major limitation because these experiments could not distinguish airway epithelial from systemic FoxO functions.

      We addressed this point experimentally by generating trachea-specific CRISPR/Cas9 dfoxo loss-of-function animals. Selective disruption of dFoxo in the airway epithelium increased susceptibility to chronic cigarette-smoke exposure, providing direct tissue-specific genetic evidence that airway epithelial dFoxo contributes to adaptation to chronic airborne stress. These data complement the phenotypes observed in constitutive mutants and demonstrate that the cigarette-smoke phenotype cannot be explained solely by systemic FoxO deficiency.

      (6) Correlative nature of the mammalian experiments

      The Public Review correctly noted that the murine and human data are primarily correlative and do not establish a causal role for FOXO dysregulation in respiratory disease.

      We fully agree and have revised the manuscript accordingly. The mammalian experiments are now presented as comparative evidence showing stress-associated FoxO regulation and reduced FOXO abundance in asthma-related samples, without implying that altered FoxO causes asthma or other respiratory disease. Disease-related statements have been moderated throughout, and mammalian loss- and gain-of-function studies are explicitly identified as necessary future experiments.

      (7) Uncertain conservation of downstream FOXO-dependent programs

      The Public Review questioned whether the downstream FOXO-dependent pathways identified in Drosophila are conserved in mammalian airway epithelia, because comparable mammalian transcriptomic and functional analyses were not performed.

      We agree and have substantially revised the comparative framework of the manuscript. Our conclusions are now restricted to the observation that stress-responsive FoxO activation is conserved across the respiratory systems examined. We do not claim conservation of specific downstream transcriptional networks. The Drosophila RNA-seq data are interpreted as defining FoxO-associated adaptive programs within the fly airway, whereas determining the extent to which these programs are conserved, modified, or replaced in mammalian airway epithelia remains an important question for future investigation.

      Summary of changes made in response to the Public Review

      Collectively, the revisions prompted by the Public Review include: (i) more precise distinction between FOXO abundance, nuclear translocation, and broader signaling; (ii) clarification of the rationale for the environmental stress paradigms; (iii) moderation of mechanistic claims based on localization data; (iv) new trachea-specific CRISPR/Cas9 loss-of-function experiments; (v) explicit separation of mechanistic Drosophila evidence from comparative mammalian observations; (vi) moderation of disease-related causal language; and (vii) a revised evolutionary framework that distinguishes conserved stress-responsive FOXO activation from the unresolved conservation of downstream regulatory programs.

      Recommendations for the authors:

      General Comments

      (1) The manuscript does not demonstrate that specific FoxO-regulated gene networks are conserved between Drosophila and mammalian airway cells; it remains unclear whether the authors intend to claim conservation of downstream FoxO-dependent pathways or only a general conserved role for FoxO in airway stress responses.

      We thank the reviewer for raising this important conceptual point, which prompted a fundamental revision of how we frame the cross-species comparison (see Major Revision 2). We agree that the original manuscript did not clarify which of these two claims we intended to make, and that the underlying analysis does not establish conservation of specific downstream FoxO-regulated networks between Drosophila and mammals. The revised manuscript now explicitly limits its claim to the more modest and better-supported conclusion: that stress-responsive FoxO activation itself is evolutionarily conserved across the airway epithelia examined. We no longer imply that the same downstream gene networks are engaged in flies and mammals. Comprehensive transcriptomic analysis was performed only in the genetically tractable Drosophila airway, and we now state explicitly that whether comparable regulatory programs operate in mammalian airway epithelia is an open question for future investigation, rather than a claim supported by the present data.

      (2) The functional experiments using constitutive dfoxo mutants do not establish a trachea-specific role for FoxO. Tissue-specific genetic manipulation is required to demonstrate epithelial-autonomous function.

      We fully agree that this was the main mechanistic limitation of the original manuscript. To address this, we conducted the requested experiments rather than relying solely on discussion.

      As detailed in Major Revision 1, we generated trachea-specific CRISPR/Cas9 dfoxo loss-of-function animals to selectively disrupt FoxO in the airway epithelium while preserving its function elsewhere. These experiments show that epithelial FoxO is directly required for adaptation to chronic airborne stress and confirm that the stress-sensitive phenotypes are not secondary to systemic FoxO deficiency. The new data now serve as the mechanistic foundation of the revised manuscript and are integrated throughout the Abstract, Results, Discussion, and conceptual model.

      Specific recommendations

      (1) Repeat the experiments in Figures 1 and 4 (ideally also Figure 3) using trachea-specific FoxO knockdown.

      We thank the reviewer for this valuable suggestion, which we considered essential to strengthen the manuscript. In response, we generated trachea-specific CRISPR/Cas9-mediated dfoxo loss-of-function animals. These experiments show that selective loss of FoxO in the airway epithelium reproduces the increased susceptibility to chronic airborne stress observed in constitutive mutants. The revised manuscript now relies primarily on these tissue-specific experiments to support the conclusion that FoxO acts within the airway epithelium. Constitutive mutants are included to illustrate physiological effects at the whole-organism level, but are no longer the main mechanistic evidence.

      (2) Revise the Abstract because the original wording incorrectly implied trachea-specific FoxO deficiency.

      We appreciate this observation and agree that the original wording was inaccurate. The Abstract has been revised to reflect the experimental evidence in the updated manuscript. The new trachea-specific CRISPR/Cas9 experiments now provide direct tissue-specific genetic evidence for an epithelial requirement for FoxO, allowing us to clearly distinguish between the original constitutive mutant analyses and the new tissue-specific loss-of-function data. The revised wording accurately represents the experimental design and avoids overstating the original findings.

      (3) The comparison between Drosophila and mammalian airway biology remains circumstantial, and the downstream pathways have not been demonstrated to be conserved.

      We appreciate this important conceptual point and have substantially revised the manuscript in response. As detailed in Major Revision 2, we no longer assert conservation of downstream FOXO-dependent transcriptional programs. The revised manuscript now explicitly distinguishes between conserved epithelial FOXO activation and the currently unresolved conservation of downstream regulatory networks. Mechanistic conclusions are limited to the Drosophila model, while the murine and human studies offer comparative evidence for conserved epithelial stress responsiveness. We believe this revised framework more accurately represents both the strengths and limitations of the available data.

      (4) The Introduction should better define the knowledge gap and explain how this work advances the field.

      We thank the reviewer for this suggestion. The Introduction has been substantially revised to more clearly define the unresolved biological question addressed by this study. Specifically, we now distinguish between the well-established systemic roles of FoxO factors in stress adaptation and the largely unexplored function of FoxO within airway epithelial cells as an interface between the organism and the external environment. We further clarify that the principal advance of this study is not the identification of FoxO as a general stress regulator, but rather the demonstration that airway epithelial FoxO coordinates adaptive responses to chronic environmental stress and that this response exhibits conserved features across evolutionarily distant respiratory systems.

      (5) Can the authors perform genetic rescue experiments?

      We agree that rescue experiments would provide an additional layer of validation. However, during revision, we prioritized generating trachea-specific CRISPR/Cas9 loss-of-function animals, as these experiments directly addressed the principal mechanistic concern raised by both the reviewers and the editorial assessment. The resulting tissue-specific genetic evidence establishes the epithelial-autonomous requirement for FoxO and therefore provides more direct mechanistic support than would additional rescue experiments using constitutive mutants alone. We now discuss this point explicitly in the revised Discussion and acknowledge that complementary rescue experiments remain valuable for future work.

      (6) Did the authors examine the InR/AKT axis?

      We appreciate this suggestion. We fully agree that FoxO activity is regulated by multiple upstream signaling pathways, including the conserved InR/AKT pathway. However, the primary objective of this study was to investigate how airway epithelial FoxO integrates diverse environmental stressors, rather than to comprehensively dissect all upstream regulatory mechanisms. Accordingly, we have expanded the Discussion to explicitly acknowledge the established role of InR/AKT signaling in FoxO regulation and to discuss how this pathway may interact with the stress-dependent mechanisms investigated here. We also identify this as an important direction for future mechanistic studies.

      (7) The gene numbers do not match the Venn diagrams.

      We thank the reviewer for carefully identifying this inconsistency. The transcriptomic analyses and figure annotations were thoroughly re-examined, and the reported gene numbers have been corrected where necessary. The revised figures, corresponding legends, and Results section are now fully consistent.

      (8) It is not clear why glutathione metabolism is emphasized.

      We appreciate this request for clarification. The Results and Discussion have been revised to better explain the rationale for highlighting glutathione metabolism. Rather than emphasizing individual genes, the revised manuscript now interprets glutathione metabolism as one component of a broader adaptive oxidative stress program coordinated by FoxO. This interpretation is presented within the context of multiple enriched biological processes, rather than as an isolated pathway, providing a more balanced and biologically coherent interpretation of the transcriptomic data.

      (9) The transcriptomic conclusions remain unclear.

      We agree that the interpretation of the RNA-seq analyses required greater clarity. Accordingly, we substantially reorganized this section of the manuscript, as described in Major Revision 2. Rather than focusing on individual differentially expressed genes, the revised manuscript now emphasizes coordinated adaptive biological processes and clearly distinguishes transcriptional associations from direct mechanistic regulation. This revised presentation more accurately reflects the information that can be inferred from the transcriptomic analyses and strengthens the overall biological interpretation.

      (10) The authors showed FOXO nuclear localization and increased expression of cytokines in A549 cells. What was the conclusion?

      Thank you for highlighting the need for a clearer conclusion. Our experiments aimed to show that human airway epithelial cells respond to hypoxic stress with FoxO activation and a related transcriptional response, not to establish a direct mechanistic link between FoxO nuclear translocation and cytokine induction. We have revised the Results and Discussion to clearly distinguish these observations from causal inference and now only suggest direct regulation by FoxO where supported by evidence.

      (11) The manuscript repeatedly refers to "FoxO signaling", although only nuclear localization was examined.

      Thank you for raising this important point. We have revised the manuscript to clearly distinguish FoxO activation, nuclear translocation, and signaling. Where appropriate, we now refer specifically to nuclear accumulation or translocation, while broader references to FoxO signaling are retained only in integrative contexts. These changes improve precision and ensure terminology aligns with the data.

      (12) Is there an explanation why only three antimicrobial peptides were induced?

      Thank you for this observation. We have expanded the Discussion to clarify that multiple signaling pathways regulate antimicrobial peptides, resulting in stimulus-specific expression profiles. Thus, induction of only a subset of peptides is consistent with the selective hypoxic stress response in the airway epithelium. We now discuss this alongside the complexity of innate immune regulation in Drosophila and provide additional references for context.

      (13) The localization of FOXO would be more convincing with nuclear markers. Did the authors examine total FOXO expression?

      Thank you for this suggestion. We have revised the manuscript to better describe the experimental procedures for assessing FoxO localization and to clarify the limitations of the imaging approach. We also expanded the Discussion to note that complementary analyses, such as biochemical assessment of FoxO protein levels and phosphorylation status, would provide further mechanistic insight. The revised manuscript now presents nuclear localization as evidence of stress-responsive FoxO redistribution without overinterpretation.

      (14) Please clarify the difference between btl-Gal4 and ppk-Gal4 and explain why btl-Gal4 was used.

      Thank you for requesting this clarification. The revised Methods and Results now explain the expression patterns and rationale for selecting each GAL4 driver. We have also added references describing these transgenic lines and clarified their suitability for our experiments.

      (15) Please clarify the qPCR data shown in Figure 3H/I and the apparent discrepancy in glutathione pathway regulation.

      We appreciate this request for clarification. The figure legends, Results, and Discussion have been revised to explain better the rationale for the selected genes and their relationship to the transcriptomic analyses. In addition, we now explicitly discuss that enrichment analyses summarize pathway-level behavior and therefore may include genes that are regulated in opposite directions within the same biological pathway. This clarification improves the interpretation of the glutathione metabolism results and avoids the impression of an internal inconsistency.

      (16) Did the different stressors increase FoxO expression in addition to reducing stress resistance?

      We thank the reviewer for this important question. Our study was designed primarily to investigate stress-induced changes in FoxO localization and function rather than transcriptional regulation of dfoxo itself. We have therefore clarified throughout the manuscript that the experiments examine activation of pre-existing FoxO protein through stress-dependent nuclear translocation of pre-existing FoxO protein rather than de novo protein synthesis. This distinction is now consistently maintained throughout the revised Results and Discussion.

      (17) Western blots for FoxO and phospho-FoxO strengthen Figure 5?

      We concur that biochemical analyses of total and phosphorylated FOXO would offer valuable complementary data. However, the primary objective of the current experiments was to investigate stress-dependent changes in subcellular localization. Instead of incorporating additional correlative analyses, we prioritized the tissue-specific genetic experiments requested during peer review. We now explicitly state in the Discussion that future studies integrating biochemical and functional approaches will further elucidate the mechanisms regulating FOXO activation in airway epithelial cells.

      (18) A Western blot for FoxO and phospho-FoxO would strengthen Figure 6.

      We appreciate this suggestion and agree that these analyses would provide additional mechanistic insight. As noted above, the primary focus of this study is to establish conserved stress-responsive FoxO activation across species, rather than to comprehensively characterize all upstream regulatory events. Accordingly, we have expanded the Discussion to acknowledge this limitation and to identify biochemical characterization of FoxO activation as a key direction for future research.

      (19) Please revise the statement describing FOXO3A as the only human longevity gene.

      We thank the reviewer for highlighting this imprecise wording. The statement has been revised throughout the manuscript to accurately describe FOXO3 as one of the most consistently replicated human longevity-associated genes, thereby offering a more balanced representation of the current literature.

      (20) Ensure consistent FOXO nomenclature.

      We appreciate this careful observation. We conducted a comprehensive editorial review and standardized FoxO nomenclature throughout the text, figures, legends, and supplementary materials to ensure consistency with current conventions.

      (21) The conclusion regarding hypoxia-induced dFOXO translation is inaccurate because the data demonstrate nuclear translocation of pre-existing protein.

      We thank the reviewer for identifying this imprecise wording. We fully agree that our data demonstrate stress-induced nuclear translocation of pre-existing dFoxo protein, rather than de novo protein synthesis. The relevant statements have been corrected throughout the manuscript to consistently refer to nuclear translocation or nuclear accumulation, thereby avoiding any implication of translational regulation.

      (22) Please clarify why the selected antimicrobial peptides (AMPs) were analyzed and provide supporting references.

      We appreciate this suggestion. The Results and Discussion sections have been expanded to clarify that these antimicrobial peptides were selected because they are well-characterized components of the Drosophila epithelial innate immune response and have been shown to respond to environmental stress and infection. Appropriate references have been added to provide the biological rationale for their inclusion.

      (23) Please explain the purpose of the LDH-A enhancer and drosomycin reporters.

      We thank the reviewer for this suggestion. Additional information has been incorporated into both the Results and Methods sections to explain the biological rationale for these reporter constructs. We now explicitly describe the pathways monitored by each reporter and clarify their selection for assessing hypoxic and immune-related responses in the airway epithelium.

      (24) Replace the term "nuclear translation".

      We thank the reviewer for identifying this typographical error. The manuscript has been corrected throughout to refer to nuclear translocation instead of nuclear translation.

      (25) Please provide images for all human FOXO isoforms.

      We appreciate this suggestion. Representative images for the analyzed FOXO isoforms have been added to the supplementary material, and corresponding references have been included in the main text and figure legends to facilitate interpretation of the localization analyses.

      (26) The nuclear localization of hFOXO6 is surprising. Please address antibody specificity.

      We thank the reviewer for raising this important point. The Methods and Discussion sections have been expanded to clarify the validation and limitations of the antibody used in these experiments. Additionally, we now explicitly acknowledge that FOXO6 differs from other FOXO family members in its regulation and discuss this observation with greater caution, avoiding mechanistic conclusions beyond the available evidence.

      (27) Clarify whether only adult flies respond to hypoxia.

      Thank you for requesting clarification. We have revised the relevant section to specify the developmental stage analyzed in each experiment and to avoid suggesting untested developmental differences.

      (28) Clarify the wording "Nuclear what dFoxO21/21".

      We thank the reviewer for identifying this typographical error. The text has been corrected accordingly.

      (29) The conclusion regarding differences between upper and lower airway cells may be overstated.

      We agree that our original wording overstated the evidence. We have revised the Results and Discussion to describe these observations more cautiously. The text now states that the experiments demonstrate differential responses in the two airway epithelial cell models examined, without implying broader biological differences.

      (30) Reduced FOXO levels in asthma lack mechanistic explanation.

      Thank you for this important comment. As discussed in Major Revision 2, we have moderated our interpretation of the asthma data. The revised manuscript presents reduced FOXO expression as a biologically meaningful association, not a causal mechanism. We have also expanded the Discussion to outline potential biological explanations and clearly distinguish hypotheses from experimental evidence.

      (31) FOXO1 has been reported to be regulated by FOXO3.

      We thank the reviewer for drawing our attention to this interesting aspect of FOXO biology. We have incorporated this point into the Discussion and cite the relevant literature. At the same time, we refrain from drawing mechanistic conclusions because the regulatory relationship was not directly examined in the present study.

      (32) The conclusions drawn from Figure 8 may exceed the data.

      We agree and have revised the Results and Discussion accordingly. Statements about Figure 8 have been moderated to ensure conclusions are proportional to the evidence and clearly separated from broader hypotheses.

      (33) Please provide clearer future perspectives.

      We appreciate this suggestion. We have expanded the Discussion to include a detailed discussion of future research directions, highlighting the need for mechanistic analyses of FOXO-dependent regulatory networks, cell-type-specific genetic studies, and comparative investigations of evolutionary conservation.

      (34) Please cite additional relevant literature.

      We thank the reviewer for these helpful recommendations. The suggested publications have been carefully evaluated and incorporated where appropriate to provide a more comprehensive overview of FoxO biology, airway homeostasis, stress responses, and aging. These additional references strengthen the discussion and better position our findings within the current literature.

      Minor Comment

      (1) The Discussion is too long and speculative.

      We agree. The Discussion has been reorganized, streamlined, and revised. We removed speculative sections and focused on the main mechanistic findings to improve clarity and readability.

      (2) The conclusion that the trachea is the organ most affected by hypoxia is an overinterpretation.

      Thank you for this observation. We agree that our original wording was too strong. The manuscript now states that the tracheal epithelium is the most sensitive tissue for hypoxia reporter activation under our experimental conditions, which more accurately reflects the data.

      (3) Line 165 uses "translation" where "nuclear translocation" was intended.

      We thank the reviewer for identifying this wording error. We have corrected the text to specify nuclear translocation, consistent with the mechanism described throughout the manuscript.

      (4) The description of the nuclear/cytoplasmic ratio quantification (lines 512-514) is inadequate and may reflect manual, user-biased scoring rather than a rigorous, high-throughput approach.

      We agree that the original description lacked sufficient methodological detail. We have expanded the Methods to specify that nuclear regions were identified using DAPI staining as an independent marker, rather than being inferred from the FoxO channel itself, and that approximately 200 nuclei were analyzed per sample. We agree that automated segmentation approaches (e.g., StarDist) would further reduce potential observer bias and increase throughput, and we note this as a direction for future refinement of the quantification pipeline.

      (5) The Figure 5 legend states that panel F used "the same type of analysis as in D," but panels D and F show different types of data; it is also unclear what each data point in panel D represents.

      We thank the reviewer for pointing out this inconsistency. The figure legend has been revised: the cross-reference in panel F now correctly points to panel E, which shows the comparable cytokine time-course experiment, rather than panel D. We also clarify that each dot in panel D represents the mean value obtained from one biological replicate.

      (6) Figure 1 lacks a non-UAS larva control for autofluorescence, and normoxic controls are missing from several panels.

      We have no extra-control for autofluorescence and believe that they are not really helpful.

      (7) In Figure 6G and H, it is unclear what each data point represents (the same issue raised for Figure 5D).

      As for Figure 5D, we have clarified in the figure legend that each data point represents the mean value from a single biological replicate, and we specify the number of replicates analyzed per condition.

      (8) Information about the LDH-GAL4 strain, including its expression pattern, should be provided.

      We thank the reviewer for this request. We have added a description of the LDH-GAL4 strain to the Methods, including its source and expression pattern.

      (9) The statement that dFoxO-GFP remains nuclear for more than an hour after cessation of hypoxia is not supported by data shown in the figures.

      We agree that this statement requires direct supporting data or should be qualified as a preliminary observation. We have therefore deleted this sentence.

      (10) Line 236 refers to Figure 5D but should refer to Figure 5C.

      We thank the reviewer for catching this typographical error. The figure reference has been corrected.

      (11) The wording "FoxO system" (line 321) should be revised for clarity.

      We agree that this wording should be clarified. We will revise "the FoxO system" in the Discussion to more precisely describe the FoxO signaling pathway in the next revision of the manuscript.

      (12) In Figure panel 3F, the label obscures the underlying data.

      We thank the reviewer for pointing this out. We have repositioned the label in panel 3F so that it no longer overlaps with the data.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      (1) Insufficient evidence that retrieval practice specifically protects inference rather than strengthening associative memories

      Sorry for the writing led to misunderstanding,we did not aim to argue that retrieval practice protects inference without affecting associative memories. Instead, we found associative memories mediated the effect of retrieval practice on A-C inference. Specifically, we added an exploratory mediation analysis to quantify the extent to which strengthened premise memory accounted for the association between retrieval practice and later A-C inference. Retrieval practice was associated with better AB/BC premise-memory performance (a = 2.13), and premise-memory performance predicted A-C inference after retrieval practice was controlled (b = 0.012). The bootstrapped indirect effect was significant (ab = 0.026, 95% CI [0.005, 0.049]), while the direct effect of retrieval practice remained significant (c' = 0.028, 95% CI [0.002, 0.055]). We have added this analysis to Section 3.2.3, “Retrieval practice enhanced direct memory retrieval but not baseline inference,” in the revised manuscript. Thus, premise memory (i.e., AB/BC memory) partially, but not completely, mediated the association. Because premise memory was assessed after inference with a 2AFC test, we explicitly describe this analysis as exploratory and interpret it cautiously.

      (2) Importantly, the direct memory retrieval test used a two-alternative forced-choice (2AFC) format, which inherently allows a substantial proportion of correct responses to arise from guessing. Consequently, trials classified as 'successfully retrieved' may still include weak associative memory traces, making it difficult to conclude that failures in inference reflect deficits in integration rather than incomplete associative learning.

      We agree with the reviewer1 that A correct response in a 2AFC test is not equivalent to unequivocal retrieval of a strong associative trace. We therefore replaced wording such as 'recalled' or 'successfully retrieved' with the more precise phrase 'answered correctly' when referring to the AB/BC direct-memory test. We also added this limitation to the Methods(2.2.6 Memory inference phase)and clarified that restricting the analysis to both-correct AB/BC trials reduces, but does not eliminate, uncertainty due to guessing. The revised Discussion notes that future studies should use cued recall, confidence ratings, or continuous measures of premise-memory strength to distinguish incomplete associative learning from a deficit in integration more sensitively.

      (3) Apparent below-chance inference performance raises interpretational concerns

      Thank you for identifying this ambiguity. We did not present the raw ACC in the figure,therefore, the presented value cannot be compare to 0.33 to get above/below chance conclusion. Figure 4A displayed the primary normalized/conditional inference measure, which relates successful A-C performance to the availability of the directly learned AB/BC premise associations; it is therefore not a raw 3AFC proportion and should not be compared directly with 0.33. We revised the Figure 4 legend to define the plotted measure explicitly and to state that it does not represent raw 3AFC accuracy.

      (4) Between-experiment implementation of retrieval practice weakens causal inference

      We admit that experiment 2 was conducted as a follow-up experiment after Experiment 1, and the retrieval-practice factor was therefore not randomized within a single fully crossed experiment. Although the two experiments were closely matched in recruitment, participant population, laboratory setting, EEG system, task structure, and experimenter team, cohort-related confounds cannot be excluded. We have accordingly revised causal wording throughout the manuscript, described the cross-experiment interaction as an association, and added this limitation to the Discussion. We also state that a within-experiment 2 x 2 design (Stress x Retrieval Practice) is needed to provide stronger causal evidence.

      (5) Lack of an appropriate comparison condition limits the interpretation of retrieval-practice mechanisms

      The present study did not include a re-exposure or restudy control condition. Therefore, the current design cannot determine whether the observed effect was specifically attributable to retrieval practice or could also be produced by re-exposure or restudy. We have added this limitation to the Discussion and noted that future studies should include a re-exposure or restudy control condition to clarify the specific contribution of retrieval practice.

      (6) Furthermore, it is unclear whether retrieval practice operates at the trial level or the participant level. Retrieval practice could enhance memory representations for specific practiced items, making those trials more resistant to stress, or it could induce a more global change in cognitive strategy or stress resilience across participants. One way to address this issue would be to analyze inference performance separately for trials that were successfully retrieved during the retrieval practice phase versus those that were not

      We agree with reviewer1 that additional analyses of retrieval performance during retrieval could help improve. However, in Experiment 2, retrieval practice was implemented using a free-recall procedure. Because participants' responses during this phase were not recorded, retrieval-practice performance could not be reliably coded for individual AB/BC associations. Consequently, the present data do not allow us to compare later A-C inference performance between associations that were successfully versus unsuccessfully retrieved during retrieval practice.

      As an indirect robustness check, we fitted a mixed-effects model to trial-level A-C inference accuracy, including fixed effects of stress, retrieval practice, and their interaction, as well as random intercepts for participants and ABC triads. The stress-by-retrieval-practice interaction showed a positive trend consistent with the participant-level analysis, although it did not reach the conventional significance threshold (b = 0.116, SE = 0.061, z = 1.90, p = .058). We have added this analysis to Section 3.2.3, “Retrieval practice enhanced direct memory retrieval but not baseline inference,” in the revised manuscript. Future studies should adopt a standardized retrieval-practice procedure and systematically record retrieval-practice performance for each association. This would allow researchers to determine whether the protective effect of retrieval practice is specific to successfully retrieved trials or reflects a broader participant-level effect.

      (7) Interpretation of EEG decoding as bridge-element reactivation may be overstated

      Yes, our decoding targeted at category classification, therefore, we cannot sure specific picture (i.e., the bridge-element was reactivated). We revised the terminology throughout the manuscript to use “bridge-related category information” (or equivalent category-level wording) and removed claims that the analysis decoded a specific bridging memory.

      Reviewer #2 (Public review):

      (1) The authors correctly timed the inference task to begin approximately 20 minutes after the onset of the stressor. While this window aligns with the expected peak of the glucocorticoid (HPA) response, it also represents a period where the rapid adrenergic (SAM) response, confirmed by heart rate elevation, is still highly influential. As the authors acknowledge, because they did not collect saliva samples due to safety protocols, they cannot definitively separate the influence of peak cortisol from the tail-end of the adrenergic surge on the observed memory impairments.

      The approximately 20-minute interval was selected on the basis of prior stress-and-retrieval studies and corresponds to the expected window of the delayed HPA response, while the heart-rate data also indicate that autonomic arousal remained relevant. Saliva collection was omitted because the study was conducted under COVID-19 safety protocols, and the present data therefore cannot dissociate glucocorticoid from adrenergic contributions. We revised the manuscript to avoid implying that cortisol was measured or that a cortisol peak was confirmed, and we now state explicitly that future studies should collect hormonal measures, when safe, to separate these mechanisms.

      (2) Figures 4 and 6: Without asterisks is really difficult to compare the significant group differences.

      Thank you for this suggestion, we added asterisks to Figures 4 and 6. At the same time, statistical significance was already conveyed in the original figures by whether the confidence intervals included zero.

      Reviewer #3 (Public review):

      (1) There are some key gaps in the reporting of the data. In particular, data is missing on how many trials were included in the inference phase and how many were retrieved in the direct memory task. This is important to know as the main conclusions are based on inference trials proportional to the direct retrieval trials. Considering that the direct retrieval performance differs significantly between the experiments, there could be issues with floor/ceiling effects (in the behaviour) and statistical power (in the EEG results) that confound the comparisons between experiments. Without the data, it is difficult to draw conclusions.

      We agree with Reviewer 3 and have added Table S1 to the Supplementary Material. The table reports group-level direct-memory correct counts, the number of triads for which both AB and BC were answered correctly, and conditional A-C accuracy. Importantly, the number of both-correct AB/BC triads did not differ significantly between stress and control groups in either Experiment 1 (t (66) = -1.65, p = .10) or Experiment 2 (t(66) = -0.28, p = .78). Moreover, the cross-experiment stress-by-retrieval-practice interaction remained significant after controlling for both-correct triad count (b = 0.051, SE = 0.024, t = 2.17, p = .031, 95% CI [0.005, 0.098]). We have added this analysis to Section 3.2.2, “Retrieval practice protects direct memory retrieval from stress without affecting premise pairs counts. These additions make the available trial numbers transparent and indicate that the primary behavioral pattern was not explained by unequal numbers of premise-supported trials.

      (2) Additionally, one-tailed t-tests have been used in follow-up tests, and, as I understand it, no multiple comparisons corrections have been applied to the post-hoc tests, suggesting that these findings should be interpreted with caution.

      The one-tailed follow-up tests were used because the relevant hypotheses were directional a priori. Based on previous findings and our theoretical framework, we specifically predicted that acute stress would impair inference-related performance and neural reactivation, whereas retrieval practice would mitigate these effects. These follow-up tests were therefore planned comparisons used to decompose the significant omnibus effects in the predicted directions, rather than exploratory post-hoc comparisons. For this reason, we considered one-tailed testing appropriate. Similarly, we did not apply an additional multiple-comparison correction to these planned follow-up tests because they were limited in number, theory-driven, and designed to evaluate specific directional predictions rather than to search broadly across multiple possible contrasts. Importantly, our conclusions do not depend on any single follow-up comparison, but on the consistent pattern observed across behavioral inference performance, neural decoding of bridge-related category information, and theta-band activity. We have revised the manuscript to clarify the rationale for these analyses.

      (3) In places, the structure is unclear, making the narrative difficult to follow, often making it necessary for the reader to go back and forth between the sections to understand the study and analyses.

      We thank Reviewer 3 for this helpful suggestion. We have thoroughly reorganized the manuscript based on the detailed recommendations to improve the overall narrative flow and readability, ensuring that the study and its analyses are easy to follow.

      Reviewer #3 (Recommendations for the authors):

      (1) There is no mention of why the delay between learning and test is important. The delay may relate to consolidation, but the rationale is unclear.

      We added the rationale for the using the 24-hour delay between learning and test to the Introduction. First, separating Day 1 learning/retrieval practice from Day 2 stress induction and testing minimizes direct effects of stress on encoding and aligns the design with prior work on stress-related impairment of delayed retrieval (Kuhlmann et al., 2005; Schönfeld et al., 2014; Smith et al., 2016). Second, the delay allows the longer-term advantage of retrieval practice to emerge; prior work showed that repeated study can be advantageous on an immediate test, whereas retrieval practice produces better retention after longer delays (Roediger and Karpicke, 2006). The interval therefore permits assessment of memory after offline processing, sleep, and natural forgetting. We also state explicitly that consolidation was neither manipulated nor measured here, so the design cannot establish that consolidation caused the stress-buffering effect.

      (2) Additionally, it is unclear what happened between Day 1 and Day 2 (did you ask the participants to do anything between the sessions, e.g., refrain from alcohol, sleep at a normal time, if so, was this recorded, etc?).

      Participants received no additional task, intervention, or behavioral restrictions between sessions, and alcohol use and sleep schedules were not recorded. They returned to the laboratory approximately 24 hours after Day 1 under otherwise naturalistic conditions. We added this information explicitly to the Experimental Procedure section. We agree that monitoring sleep and substance use would improve control over potential intersession variability in future studies.

      (3) Section 2.5 Time-frequency analyses: The rationale for investigating theta power is unclear. Did the authors only investigate theta, or were other frequency bands often associated with memory retrieval also explored (e.g., alpha or beta)? If so, these should be reported. If not, the rationale should be clearer

      We clarified that theta was selected a priori because theta oscillations have been linked to associative memory, retrieval, hippocampal-prefrontal communication, and memory integration in associative-inference paradigms (including Backus et al., 2016). The time-frequency analysis therefore focused on theta power (2-8 Hz) rather than conducting an exploratory search across frequency bands. Alpha and beta bands were not analyzed, and this is now stated explicitly in the Methods. In the Discussion, we now relate the theta-band findings to the behavioral and decoding results, noting that acute stress reduced theta power during the later stage of inference, whereas retrieval practice prevented this reduction and enhanced theta activity during the earlier stage of inference.

      (4) 2.6.2 Analysis of Memory Inference Performance: There seems to be a disconnect between the hypothesis, which predicts that Experiment 2 conditions will be the same (i.e., confirming the null) and the independent t-test, which would tell you if the alternative can be accepted (rather than if it's a true null). Bayes or Equivalence tests would instead link to the hypothesis

      Because a non-significant frequentist t-test cannot directly provide evidence for the null hypothesis, we additionally conducted a Bayesian independent-samples t-test. The analysis yielded BF10 = 0.361 (BF01 = 2.77), providing evidence in support of the null hypothesis that memory inference performance did not differ between the stress and control groups in Experiment 2. We have added this analysis to the Methods and Results.

      (5) Line 508: It is not clear where the 207 +/- 50 ms time window came from.

      Thank you for identifying this error. The value 207 ms was a typographical mistake and the correct value is 198 ms. We rewrote the procedure in detail 2.6.4 Optimal time window identification and validation). In short, participant-level peak latencies were first identified in the localizer training data; their group mean was 197.46 ms (SD = 245.22 ms), which was rounded to define the primary 198 +/- 50 ms training window. An independent cross-task time-generalization analysis yielded a peak latency of 246.01 ms (SD = 220.08 ms). This did not differ significantly from the localizer-derived latency, t(133) = 1.66, p = .10, supporting use of the fixed 198 +/- 50 ms window. The Methods now describe all three steps and the corrected value consistently.

      (6) Section 3.5: It is not quite clear to me why the choice phase is of interest for the decoder. As I understand it, the participants are asked to select the image during this 3-second time window, meaning that they will be moving (artifacts). Therefore, I am unsure what question this analysis is addressing and would recommend clarification

      We clarified that our primary theoretical interest was in the pre-choice inference period, during which participants considered and integrated the relevant information before making a response. We were also interested, secondarily, in the choice period to examine whether bridge-related category reactivation persisted into response selection. Thus, the inference period served as our primary neural window of interest, with the choice period providing a complementary analysis.

      We agree that button presses create a risk of movement-related contamination. EEG trials were visually inspected, and ICA was used to remove ocular and movement-related components; nevertheless, we now interpret the choice-period findings cautiously.

      (7) The title boldly suggests that the restoration of the impairment is due to memory reactivation. Although the evidence hints that this may be the case, there could be many other factors contributing to the results, and the title can be misleading. I would therefore recommend changing the title to suggest a link with memory reactivation.

      Thank you for this suggestion. We have revised the title to “Retrieval practice prevents stress-induced inference impairment and preserves rapid bridge-related memory reactivation” to avoid implying a causal role of memory reactivation.

      Figure 1A: illustrates the stimuli as words, whereas the stimuli were images. To avoid confusion, I would recommend replacing the words with images (or adding images alongside).

      We have replaced the words with images in Figure 1A to accurately reflect the stimuli used in the experiment.

      Line 654: I presume the authors meant to say "memory inference phase" instead of "memory reference phase".

      Sorry for that. We apologize for this typographical error. We have corrected “memory reference phase” to “memory inference phase.”

      Specific comments to the authors are listed below in the order of the manuscript:

      For the remaining minor comments, we have made the corresponding revisions throughout the manuscript. To keep the response letter focused on the major scientific issues and avoid an overly lengthy point-by-point description of minor editorial changes, we do not elaborate on each of these changes here. All corresponding revisions can be found in the revised manuscript.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Reviewer #1 (Public review):

      Summary:

      This manuscript investigates the interplay between spontaneous attention and melody formation during polyphonic music listening. The authors use EEG recordings during uninstructed listening to examine how attention bias influences melody processing, employing both behavioural measures and computational modelling with music transformers. The study introduces a very clever pitch-inversion manipulation design to dissociate high-voice superiority from melodic salience, and proposes a "weighted integration" model where attention dynamically modulates how multiple voices are combined into perceived melody.

      Strengths:

      (1) The attention bias findings (Figure 2) are compelling and methodologically sound, with convergent evidence from both behavioral and neural measures.

      (2) The pitch-inversion manipulation appears to super elegantly dissociate two competing factors (high-voice superiority vs melodic salience), moreover, the authors claim that the chosen music lends itself perfectly to his PolyInv condition. A claim I cannot really evaluate, but which would make it even more neat.

      (3) Nice bridge between hypotheses and operationalisations.

      Weaknesses:

      The results in Figure 3 are very striking, but I have a number of questions before I can consider myself convinced.

      (1) Conceptual questions about surprisal analysis:

      The pattern of results seems backwards to me. Since the music is inherently polyphonic in PolyOrig, I'd expect the polyphonic model to fit the brain data better - after all, that's what the music actually is. These voices were composed to interact harmonically, so modeling them as independent monophonic streams seems like a misspecification. Why would the brain match this misspecified model better?

      Conversely, it would seem to me the pitch inversion in PolyInv disrupts (at least to some extent) the harmonic coherence, so if anywhere, I'd a priori expect that in this condition, listeners would rather be processing streams separately - making the monophonic model fit better there (or less bad), not in PolyOrig. The current pattern is exactly opposite to what seems logical to me.

      The reviewer raised an important point that we have further clarified in the text (lines 503-516). We agree that a physiologically valid computational model of polyphonic music processing should match neural signals more closely than a monophonic model for all conditions. However, these transformer models are not built to be physiologically plausible. Their only objective is to minimise the next-event prediction error based on the prior context, which may also be achieved in ways that differ from human brain processing.

      Previous studies (Di Liberto et al., eLife, 2020; Marion et al., Journal of Neuroscience, 2021; Kern et al., eLife, 2022), combined with our results on the monophonic condition, makes us confident that the monophonic models are correlated with how our brains process melodies from monophonic streams. Our finding that monophonic models also correlate with neural activity during PolyOrig is quite exciting, and far from obvious. Finding that melodic surprises derived from a polyphonic model work outperform the monophonic model at all is also extremely interesting. In fact, that result suggests that, under certain conditions (in this case, corresponding to a change in attention bias), our brains build melodic surprises by integrating information from multiple streams. Indeed, it is important to thoroughly discuss the motivation, reasoning, and caveats of this result, and we have done our best to augment the manuscript in that regard.

      Our rationale was the following: In the PolyOrig condition, there is a strong attention bias, meaning that the melody corresponds primarily to one specific stream, and melodic expectations seem to be built on that stream exclusively (i.e., monophonic model). One caveat here is that our polyphonic model may simply be a “bad” model (i.e., non-physiologically plausible) for PolyOrig. Nonetheless, we find the result extremely promising, as the monophonic model is a good predictor of the EEG signal, and that its classification gain (AM-A) was comparable between PolyOrig and Monophonic condition.

      We think that more work is needed to identify a polyphonic model that is closest to brain neural activity. That this question should be investigated using multiple datasets with various stimuli and conditions, and we are doing our best to provide a wider range of data and conditions in our ongoing work (for example, we are currently collecting data with three-stream music).

      (2) Missing computational analyses:

      If the transformer is properly trained, it should "understand" (i.e., predict/compress) the polyphonic music better, right? Can the authors demonstrate this via perplexity scores, bitsper-byte, or other prediction metrics, comparing how well each model (polyphonic vs monophonic) handles the music in both conditions? Similarly, if PolyInv truly maintains musical integrity as claimed, the polyphonic model should handle it as well as PolyOrig. But if the inversion does disrupt the music, we should see this reflected in degraded prediction scores. These metrics would validate whether the experimental manipulation works as intended. Also, how strongly are the surprisal streams correlated? There are many non-trivial modelling steps that should be reported in more detail.

      The revised manuscript includes an assessment of the impact of the inversion on the model predictions. As expected, the inversion alters the ability of the model to predict the next note, producing a statistically significant increase in the surprise (KS test p = 9.7*10<sup>-130</sup>; D = 0.116), entropy (KS test p = 6.9*10<sup>-15</sup>; D = 0.0388), and perplexity (Wilcoxon signed-rank test p = 9.4*10<sup>-6</sup>, r = -0.783) for the polyphonic model. While our manipulation led to a reduced predictive ability of the model, it should be noted that these are very small effects (D<0.2).

      Next, we measured the Pearson’s correlations of the expectation values for corresponding notes before and after the inversion of the polyphonic tracks, finding relatively low correlation values for surprise (r = 0.150, p = 7*10<sup>-68</sup>) and entropy (r = 0.106, p = 3*10<sup>-34</sup>).

      To test whether the low correlations between the original and inverted expectation streams affected the neural results, we re-ran the CCA analysis used in Figure 3 on the PolyInv condition using expectation features extracted from PolyOrig. This control removes the inversion-induced change in the expectation features. The pattern of results was unchanged, indicating that the main findings are robust to these differences in model-derived expectation values. The revised manuscript includes this new data and a reflection on the implication of these results (lines 348-370; please see the new Figure 3 Supplement 1).

      (3) Methodological inconsistencies:

      Why are the two main questions (Figures 2 and 3) answered with completely different analytical approaches? The switch from TRF to CCA with match-vs-mismatch classification seems unmotivated. I think it's very important to provide a simpler model comparison - just TRF with acoustic features plus either polyphonic or monophonic surprisal - evaluated on relevant electrodes or the full scalp. This would make the results more comparable and interpretable.

      The revised manuscript includes an explanation on that choice (lines 309-315). TRFs are effective when studying selective attention, which has been widely documented in the speech selective attention literature. The TRF also leads to interpretable results (ERP-like), which is preferable. However, when the objective is to assess the neural encoding of a certain property, CCA returns stronger scores as it accounts for all stimulus features and all EEG channels simultaneously. This is preferable in this case, as the EEG signatures of melodic expectation typically have a small magnitude (r~0.005; see Figure 2C in Di Liberto et al., eLife, 2020). Interpretability (i.e., the ability to infer spatial and temporal patterns of the neural response) was also less important on this analysis, as the two models were expected to simply be better or worse representations of the same neural sources. As such, we opted for the method with the highest sensitivity in terms of explained variance (here operationalised as a classification metric - as explored in our previous study on phonotactics, Di Liberto et al., NeuroImage, 2019).

      (4) Presentation and methods:

      (a) Coming from outside music/music theory, I found the paper somewhat abstract and hard to parse initially. The experimental logic becomes clearer with reflection, but you're doing yourselves a disservice with the jargon-heavy presentation. It would be useful to include example stimuli.

      We have added an example sound file, with the corresponding PolyOrig, PolyInv versions (Figure 1 - supplement 1).

      With regard to the wording in the manuscript, we agree that it may sound heavy in some parts. Nonetheless, that was an inevitable consequence of avoiding confusion and ambiguity. We are referring, for example, to the PolyInv manipulation, where it was critical to use a consistent wording. For instance, high-pitch stream could be intended as the stream that has the higher pitch in PolyInv, or the stream that had originally the higher pitch in PolyOrig. This was an issue of an early version of the manuscript that was fixed, regrettable making the manuscript heavier to read. We remain open to suggestions and did our best to improve some of our wording in the revised version (especially in the Discussion section).

      (b) The methods section is extremely brief - no details whatsoever are provided regarding the modelling: What specific music transformer architecture? Which implementation of this "anticipatory music transformer"? Pre-trained on what corpus - monophonic, polyphonic, Western classical only? What constituted "technical issues" for the 9 excluded participants? What were the channel rejection criteria?

      The methods section has been substantially augmented to include all details necessary for replication of our analyses (see lines 578-580, 670-737).

      Reviewer #2 (Public review):

      Summary:

      The authors sought to understand the drivers of spontaneous attentional bias and melodic expectation generation during listening to short two-part classical pieces. They measured scalp EEG data in a monophonic condition and trained a model to reconstruct the audio envelope from the EEG. They then used this model to probe which of the two voices was best reflected in the neural signal during two polyphonic conditions. In one condition, the original piece was presented, in the other, the voices were switched in an attempt to distinguish between effects of (a) the pitch range of one voice compared to the other and (b) intrinsic melodic features. They also collected a behavioural measure of attentional bias for a subset of the stimuli in a separate study. Further modelling assessed whether expectations of how the melody would unfold were formed based on an integrated percept of melody across the two voices, or based on a single voice. The authors sought to relate the findings to different theories of how musical/auditory scene analysis occurs, based on divided attention, figure-ground perception, and stream integration.

      Strengths:

      (1) A clever but simple manipulation - transposing the voices such that the higher one became the lower one - allowed an assessment of different factors that might affect the allocation of attention.

      (2) State-of-the-art analytic techniques were applied to (a) build a music attention decoder (these are more commonly encountered for speech) and (b) relate the neural data to features of the stimulus at the level of acoustics and expectation.

      (3) The effects appeared robust across the group, not driven by a handful of participants.

      Weaknesses:

      (1) A key goal of the work is to establish the relative importance for the listener's attention of a voice's (a) mean pitch in the context of the two voices (high-voice superiority) and (b) intrinsic melodic statistics/motif attractiveness. The rationale of the experimental manipulation is that switching the relative height of the lines allows these to be dissociated by imparting the same high-voice benefit to the new high-voice and the same preferred intrinsic melodic statistics to the new low voice. However, previous work suggests that the high-voice superiority effect is not all-or-nothing. Electrophysiology supported by auditory nerve modelling found it to depend on the degree of voice separation in a non-monotonic way (see https://doi.org/10.1016/j.heares.2013.07.014 at p. 68). Although the authors keep the overall pitch of the lower (and upper) line fixed across conditions, systematically different contour patterns across the voices could give rise to a sub-optimal distribution of separations in the PolyInv versus PolyOrig condition. This could weaken the high-voice superiority effect in PolyInv and explain the pattern of results. One could argue that such contour differences are examples of the "intrinsic melodic statistics" put forward as the effect working in opposition to high-voice superiority, but it is their interaction across voices that matters here.

      We thank the reviewer for this thoughtful comment. We agree that high‑voice superiority can vary with between‑stream pitch separation and need not be all‑or‑nothing. To address this, we quantified the separation differences between PolyOrig and PolyInv. Separation was higher in PolyInv (paired t‑test: p = 3.6×10<sup>⁻⁶</sup>). If a larger separation weakened the high-voice superiority effect, this would threaten our interpretation of the result in Figure 2 B, D (where PolyOrig presented a stronger high-voice attention bias than PolyInv). However, pitch separation did not correlate with our EEG attention‑bias index when considering both conditions together (r = 0.005, p = 0.908) or PolyOrig alone (r = -0.101, p = 0.0693). Within PolyInv, the correlation was significant and positive (r = 0.154, p = 0.00561) i.e., greater separation was associated with a stronger, not weaker, high‑voice bias. Thus, the observed results are not explained by a sub‑optimal distribution of separations across conditions. While contour differences could be viewed as part of the “intrinsic melodic statistics,” the cross‑voice interaction via separation does not account for the pattern we report.

      (2) Although melody statistics are mentioned throughout, none have been calculated. It would be helpful to see the features that presumably lead to "motif attractiveness" quantified, as well as how they differ across lines. The work of David Huron, such as at https://dl.acm.org/doi/abs/10.1145/3469013.3469016, provides examples that could be calculated with ease and compared across the two lines: "the tendency for small over large pitch movements, for large leaps to ascend, for musical phrases to fall in pitch, and for phrases to begin with an initial pitch rise". The authors also mention differences in ornamentation. Such comparisons would make it more tangible for the reader as to what differs across the original "melody" and "support" line. In particular, as the authors themselves note, lines in double-counterpoint pieces can, to a degree, operate interchangeably. Bach's inventions in particular use a lot of direct repetition (up to octave invariance), which one would expect to minimise differences in the statistics mentioned. The references purporting to relate to melodic statistics (11-14 in original numbering) seem rather to relate to high-voice superiority.

      We agree that quantifying “motif attractiveness” will be useful to the readers. We computed four standard melodic-statistics measures (H: high-pitch; L: low-pitch): Pitch Proximity (mean interval size; H < L, p = 0.0747), Leap Ascension ratio (H > L, p = 0.00111), Pitch Declination (H < L, p = 0.73), and Initial Anacrusis (H > L, p = 0.422). We also note that the H line contains ~15.2% more notes than L. Taken together, we conclude that there are small albeit measurable differences between H and L streams that predict behaviour i.e., there was an attention bias toward the H voice (with behavioural and EEG metrics consistent with this interpretation). Indeed, it should be noted that these differences were relatively small, in contrast with the large contrasts that are typical of many contemporary Western pieces. This is consistent with the double-counterpoint repertoire, where lines are intentionally written to be highly interchangeable. Here, modest statistical asymmetries nonetheless track perceptual salience. To facilitate further work, we will release code, per-piece feature tables, and note-count summaries in the repository.

      (3) The exact nature of the transposition manipulation is obscured by a confusing Figure 1B, which shows an example in which the transposed line does not keep the same note-to-note interval structure as the original line.

      Thank you for pointing that out. We have corrected that panel.

      (4) The transformer model is barely described in the main text. Even readers who are familiar with the Hidden Markov Models (e.g., in IDyOM) previously used by some of the authors to model melodic surprise and entropy would benefit from a brief description in the main text at least of how transformer models are different. The Methods section goes a little further but does not mention what the training set was, nor the relative weight given to long- and short-term memory models.

      (5) The match-mismatch procedure should be explained in enough detail for readers to at least understand what value represents chance performance and why performance would be measured as an average over participants. Relatedly, there is no description at all of CCA or the match-mismatch procedure in the Methods.

      The revised manuscript includes substantial additions to the methodology description, including details on the Transformer model and the match-mismatch procedures (lines 670-716). Please also see our answer to Reviewer 1, Point 4.

      (6) Details of how the integration model was implemented will be critical to interpreting the results relating to melodic expectations. It is not clear how "a single melody combining the two streams" was modelled, given that at least some notes presumably overlapped in time.

      The revised manuscript includes details on the integration model (see lines 706-716, 722-737).

      The AMT treats the polyphonic input as a single event sequence, rather than as two separate streams, where simultaneous notes are encoded as distinct events with the same onset times. Thus, the model generated an expectation value for each note event in that sequence, including notes with identical onset times. For simultaneous notes, these expectation values are not equivalent: the first note at a given onset is evaluated without the other simultaneous note yet having been incorporated into the context, whereas the final note at that same onset is evaluated after the other simultaneous note has been processed. AMT is a pretrained model that was trained using the same representation. To ensure that the integrated expectation feature reflected the full polyphonic context present at that timepoint, we used the expectation value of the last note event at each onset time. By using this merged representation, the model captures the polyphonic context. The revised Methods now makes this explicit.

      (7) The authors propose a weighted integration model, referring in the Discussion to dynamics and an integration rate. They do show that in the PolyOrig case, the top stream bias is highest and the monophonic model gives the best prediction, while in the PolyInv case, the top stream bias is weaker and the polyphonic model provides the best prediction. However, that doesn't seem to say anything about the temporal rate of integration, just the degree, which could be fixed over the whole stimulus. Relatedly, the terms "strong attention bias" and "weak attention bias" in Highlight 4 might give the impression of different attention modes for a given listener, or perhaps different types of listeners, but this seems to be shorthand for how attention is allocated for different types of stimuli (namely those that have or have not had their voices reversed).

      Our wording was misleading and was improved in this revision (lines 500-516). Our use of “dynamic”, in that sentence, did not refer to temporal integration, but it was referring to the possibility that our integration strategy may adapt to the stimulus (as suggested by the different results in PolyOrig and PolyInv). The revised manuscript includes a clearer wording that we think solves the issue. With regard to temporal dynamics, the reviewer is absolutely correct in that our analyses have not explored the temporal rate of integration. We are currently looking into that with a more tailored experiment involving more varied stimuli, but that will be part of a separate future study.

      With regard to strong vs. weak attention bias in Highlight 4, our view is that the attention bias, in fact, leads to different “modes”, as suggested by the result in Figure 3C. Nonetheless, we appreciate that it would be useful to referring more closely to the facts (as opposed to our interpretations). As such, we have reworded Highlight 4.

      (8) Another aspect of the presentation relating to temporal dynamics is that in places (e.g., Highlight 1), the authors suggest they are tracking attention dynamically. However, as acknowledged in the Discussion, neither the behavioural nor neural measure of attentional bias are temporally resolved. The measures indicate that on average participants attend more to the higher line (less so when it formed the lower line in the original composition).

      The reviewer is correct. Our phrasing was referring to a previous version of the manuscript, as we had attempted time-resolved analyses that, however, showed quite a bit of variability, and were not necessary for the conclusions of the present study. As such, those results were excluded from our submission, as we aim to investigate the temporal dynamics aspect in a future study, including more data and more tailored denoising methodologies. We have revised the wording in the manuscript to solve this issue (please see lines 33, 39-43, 64, 262, 507).

      (9) It is not clear whether the sung-back data were analysed (and if not why participants were asked to sing the melody back rather than just listen to the two components and report which they thought was the melody). It is also not stated whether the order in which the high and low voices were played back was randomised. If not, response biases or memory capacity might have affected the behavioural attention data.

      We have added our explanation and motivations to the manuscript (lines 598-608).

      The procedure was the following: Participants were presented with a short segment of a polyphonic composition; they sung back the melody; they were presented with the two monophonic streams, one after the other; they selected which one they considered the melody.

      The numerical results from the last step of this process were analysed, while the “sung back” data was not analysed. The request of singing back before hearing the individual streams was to encourage them to answer the question based on their own melody extraction process, as opposed to perform a post hoc “reasoned” decision (possibly influenced by a presentation bias). Future research should explore whether this approach is more or less effective. Here, behavioural and EEG attention bias results are compatible, which is satisfactory for claims.

      Please note that the presentation order of the high and low-pitched melodies played was indeed randomised.

      Reviewer #3 (Public review):

      Summary:

      In this paper, Winchester and colleagues investigated melodic perception in natural music listening. They highlight the central role of attentional processes in identifying one particular stream in polyphonic material, and propose to compare several theoretical accounts, namely (1) divided attention, (2) figure-ground separation, and (3) stream integration. In parallel, the authors compare the relative strength of exogenous attentional effects (i.e., salience) produced by two common traits of melodies: high-pitch (compared to other voices), and attractive statistics. To ensure the generalisability of their results to real-life listening contexts, they developed a new uninstructed listening paradigm in which participants can freely attend to any part of a musical stimulus.

      Major strengths and weaknesses of the methods and results:

      (1) Winchester and colleagues capitalized on previous attention decoding techniques and proposed an uninstructed listening paradigm. This is an important innovation for the study of music perception in ecological settings, and it is used here to investigate the spontaneous attentional focus during listening. The EEG decoding results obtained are coherent with the behavioral data, suggesting that the paradigm is robust and relevant.

      (2) The authors first evaluate the relative importance of high-pitch and statistics in producing an attentional bias (Figure 2). Behavioral results show a clear pattern, in which both effects are present, with a dominance of the high-pitch one. The only weakness inherent to this protocol is that behavioral responses are measured based on a second presentation of short samples, which may induce a different attentional focus than in the first uninstructed listening.

      That’s a good point. That is an experimental limitation. Asking participants to repeat the melody during the first presentation (so, providing a task) could have altered the way they processed the music, so we preferred to avoid that. We instead opted for the presentation of a short snippet of each of the polyphonic pieces heard only after the initial uninstructed listening task. In principle, repeating the same identical stream may lead to different attentional patterns, we agree. We think that is less likely in our case, as we only presented very brief snippets from a random portion of each previous segment. We think that this minimises that risk, and the results are in line with that hypothesis. We have added some considerations on that risk. We actually think that the question on repetition, both from attention and melodic processing/surprise perspectives, is a very interesting one that should be investigated in dedicated studies. As such, we have added a suggestion for future work too (line 452-455).

      (3) Then, the analyses of EEG data compare the decoding results of each melody (the high or low voice, and with "richer" or "poorer" statistics), and show a similar pattern of results. However, this report leaves open the possibility of a confounding factor. In this analysis, a TRF decoding model is first trained based on the presentation of monophonic samples, and it is later used to decode the envelope of the corresponding melodies in the polyphonic scenario. The fitting scores of the training phase are not reported. If the high-pitch or richer melodies were to produce higher decoding scores during monophonic listening (due to properties of the physiological response, or to perceptual processes), a similar difference could be expected during polyphonic listening. To capture attentional biases specifically, the decoding scores in the polyphonic conditions should be compared to the scores in the monophonic conditions, and attention could be expected to increase the decoding of the attended stream or decrease the unattended one.

      We carried out additional analyses to confirm that the model was not biased toward any particular condition. The attention decoding model, which was trained on all monophonic pieces together, was evaluated on each of the four monophonic conditions (main stream high-pitch, support stream low-pitch, main stream low-pitch, support stream high-pitch). No statistically significant differences were detected when comparing the four conditions (Kruskal-Wallis = 0.377), nor when comparing high versus low pitch conditions (unpaired t-test, p= 0.567) and main versus support streams (unpaired t-test, p = 0.377).

      (4) Then, Winchester and colleagues investigate the processing of melodic information by evaluating the encoding of melodic surprise and uncertainty (Figure 3). They compare the surprise and uncertainty estimated from a monophonic or a polyphonic model (Anticipatory Music Transformer), and analyse the data with a CCA analysis. The results show a double dissociation, where the processing of melodies with a strong attentional bias (high-pitch, rich statistics) is better approximated with a monophonic model, while a polyphonic model better classifies the other melodies. While this global result is compelling, it remains a preliminary and intriguing finding, and the manuscript does not further investigate it. As it stands, the result appears more like a starting point for further exploration than a definitive finding that can support strong theoretical claims. First, it could be complemented by a comparison of the encoding of individual melodies (e.g., AMmono high-voice vs AMmono low-voice, in PolyOrig and PolyInv conditions) to highlight a more direct correspondence with the previous results (Figure 2) and allow a more precise interpretation. Second, additional analyses or experiments would be needed to unpack this result and provide greater explanatory power. Additionally, the CCA analysis is not described in the method. The statistical testing conducted on this analysis seems to be performed across the 250 repetitions of the evaluation rather than across the 40 participants, which may bias the resulting p-values. Moreover, the choice and working principle of the Anticipatory Music Transformer are not described in the method. Overall, these results seem at first glance solid, but the missing parts of the method do not allow for full evaluation or replication of them.

      For the missing methodological details please see our answer to Reviewer 1-Weakness 4, and Reviewer 2-Weakness 5, and the revised manuscript (lines 670-716, 734-737). We agree with the reviewer that our results should be taken as a stepping stone toward a better understanding of polyphonic music, and that additional work is required to draw stronger theoretical claims. We have expanded the future works section of the manuscript to reflect this consideration (lines 446-456, 500-516). The revised manuscript also clarifies that the statistical analyses on the CCA results are tests on the mean across participants, where distributions are derived by repeating the procedure 250 times for each participant (lines 324-326).

      An appraisal of whether the authors achieved their aims, and whether the results support their conclusions:

      (1) Winchester and colleagues aimed at identifying the melodic stream that attracts attention during the listening of natural polyphonic music, and the underlying attentional processes. Their behavioral results confirm that high-pitched and attractive statistics increase melodic salience with a greater effect size of the former, as stated in the discussion. The TRF analyses of EEG data seem to show a similar pattern, but could also be explained by confounding factors. Next, the authors interpret the CCA results as the results of stream segregation when there is a high melodic salience, and stream integration when there are weaker attentional biases. These interpretations seem to be supported by the data, but unfortunately, no additional analyses or experiments have been conducted to further evaluate this hypothesis. The authors also acknowledge that their results do not show whether stream segregation occurs via divided attention or figure-ground separation. However, the lack of information about the music model used (Anticipatory Music Model) and the way it was set up raises some questions about its relevance and limits as a model of cognition (e.g. Is this transformer a "better" model of the listeners' expectations than the wellestablished IDyOM model, and why?), and about the validity of those results.

      (2) Overall, the authors achieved most of the aims presented in the introduction, although they couldn't give a more precise account of the attentional processes at stake. The interpretations are sound and not overstated, with the exception of potential confounding factors that could compromise the conclusions on the neural tracking of salient melodies (EEG results, Figure 2).

      Impact of the work on the field, and the utility of the methods and data to the community: The new uninstructed listening paradigm introduced in this paper will likely have an important impact on psychologists and neuroscientists working on music perception and auditory attention, enabling them to conduct experiments in more ecological settings. While the attentional biases towards melodies with high-pitch and attractive statistics are already known, showing their relative effect is an important step in building precise models of auditory attention, and allows future paradigms to explore more fine-grained effects. Finally, the stream segregation and integration shown with this paradigm could be important for researchers working on music perception. Future work may be necessary to identify the models (Markov chains, deep learning) and setup (data analysis, stimuli, control variables) that do or do not replicate these results.

      We thank the reviewer for their work on this manuscript!

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      The authors examine the neural correlates of face recognition deficits in individuals with Developmental Prosopagnosia (DP; ’face blindness’). Contrary to theories that poor face recognition is driven by reduced spatial integration (via smaller receptive fields), here the authors find that the properties of receptive fields in face-selective brain regions are the same in typical individuals vs. those with DP. The main analysis technique is population Receptive Field (pRF) mapping, with a wide range of measures considered. The authors report that there are no differences in goodness-of-fit (R2), the properties of the pRFs (neither size, location, nor the gain and exponent of the Compressive Spatial Summation model), nor their coverage of the visual field. The relationship of these properties to the visual field (notably the increase in pRF size with eccentricity) is also similar between the groups. Eye movements do not differ between the groups.

      Strengths:

      Although this is a null result, the large number of null results gives confidence that there are unlikely to be differences between the two groups. Together, this makes a compelling case that DP is not driven by differences in the spatial selectivity of face-selective brain regions, an important finding that directly informs theories of face recognition. The paper is well written and enjoyable to read, the studies have clearly been carefully conducted with clear justification for design decisions, and the analyses are thorough.

      Weaknesses:

      One potential issue relates to the localisation of face-selective regions in the two groups. As in most studies of the neural basis of face recognition, localisers are used to find the face-selective Regions of Interest (ROIs) - OFA, mFus, and pFus, with comparison to the scene-selective PPA. To do so, faces are contrasted against other objects to find these regions (or scenes vs. others for the PPA). The one consistent difference that does emerge between groups in the paper is in the selectivity of these regions, which are less selective for faces in DP than in typical individuals (e.g., Figure 1B), as one might expect. 6/20 prosopagnosic individuals are also missing mFus, relative to only 2/20 typical individuals. This, to me, raises the question of whether the two groups are being compared fairly. If the localised regions were smaller and/or displaced in the DPs, this might select only a subset of the neural populations typically involved in face recognition. Perhaps the difference between groups lies outside this region. In other words, it could be that the differences in prosopagnosic face recognition lie in the neurons that are not able to be localised by this approach. The authors consider in the discussion whether their DPs may not have been ’true DPs’, which is convincing (p. 12). The question here is whether the regions selected are truly the’prosopagnosic brain areas’ or whether there is a kind of survivor bias (i.e., the regions selected are normal, but perhaps the difference lies in the nature/extent of the regions. At present, the only consideration given to explain the differences in prosopagnosia is that there may be ’qualitative’ differences between the two (which may be true), but I would give more thought to this.

      Thank you for the positive assessment of our study and for raising this important theoretical point regarding ROI definition. We agree that face-selective ROIs in DPs, relative to controls, may be smaller, less selective, or altogether missing when traditional methods of localization with fixed thresholds are used (Furl et al, 2011). For this reason - to circumvent potential survivor bias and ensure ROI voxel counts across participants are equated - we used a method of ROI definition whereby each subject’s individual statistical map from the localizer was intersected with a generously-sized group mask for each ROI and the top 20% most category-selective voxels were retained for the pRF analysis (Norman-Haignere et al., 2013; Jiahui et al., 2018). This means that the raw number of voxels per ROI was equal across all participants with respect to the common group space, thereby ensuring a fair comparison even in cases where one group shows diminished category-selectivity. The details of the ROI definition are provided in the Methods at the end of the manuscript. To ensure readers understand our approach, we have also updated the Results section manuscript to highlight this important methodological step.

      “To ensure a fair group comparison because individuals with DP often exhibit category selective responses below typically used thresholds, we adopted the “variable-window” method of ROI definition (Norman-Haignere et al., 2013; Jiahui et al., 2018). In this method, generously-sized group masks for each respective ROI (see Supplementary Figure 11) were intersected with each participant’s individual statistical map and the top 20% most category-selective voxels within the mask were retained for analysis. This method avoids the subjectivity of manually choosing thresholds and ensures that all participants have equally sized ROIs (i.e., identical voxel counts) prior to pRF fittings.”

      With regard to the question of whether face-selective ROIs may be displaced in DPs compared to controls, previous work from the senior author’s lab (Jiahui et al., 2018) shows that, despite exhibiting weaker activations, the peak coordinates of significant clusters in DPs occupy very similar locations to those of controls. And, even if there were indeed slight displacements of face-selective ROIs for some subjects, the group-defined masks used in the present analysis were large enough to capture the majority of the top voxels. In the Supplementary Figure 11, we have included a diagram of the group masks used in our study.

      The reviewer here also points out that more DPs than controls were missing the mFUS region (6/20 DPs vs 2/20 controls; Figure 1C). However, ‘missing’ in this context was not based on face-selectivity but rather a lack of retinotopic tuning. PRFs were fit to all voxels within each ROI - with all subjects starting out with equal voxel counts - and thereafter, voxels for which the variance explained by the pRF model was below 20% were excluded from subsequent analysis. We decided that any ROI with fewer than 10 voxels remaining after thresholding on the pRF fit should be deemed ‘missing’ since we considered the amount of data insufficient to reliably characterize the region’s retinotopic profile. Left mFUS was just one of six face-selective regions under study. The other five regions, many of which evinced strong fits to the pRF model, were represented comparably in DPs and controls and showed high similarity in the pRF parameters. Furthermore, across most participants, mFUS exhibited a low proportion of retinotopically modulated voxels (defined as voxels with pRF R squared greater than 20%, see Figure 1D). A follow-up analysis showed that the count of voxels surviving pRF R squared thresholding in left mFUS was not significantly correlated with mean pRF size (r(30) = 0.23,t = 1.28,p = 0.21) indicating that slightly more exclusion of DPs in this region is unlikely to have biased the group’s average pRF size.

      The discussion considers the differences between the current study and an unpublished preprint (Witthoft et al, 2016), where DPs were found to have smaller pRFs than typical individuals. The discussion presents the argument that the current results are likely more robust, given the use of images within the pRF mapping stimuli here (faces, objects, etc) as opposed to checkerboards in the prior work, and the use of the CSS model here as opposed to a linear Gaussian model previously. This is convincing, but fails to address why there is a lack of difference in the control vs. DP group here. If anything, I would have imagined that the use of faces in mapping stimuli would have promoted differences between the groups (given the apparent difference in selectivity in DPs vs. controls seen here), which adds to the reliability of the present result. Greater consideration of why this should have led to a lack of difference would be ideal. The latter point about pRF models (Gaussian vs. CSS) does seem pertinent, for instance - could the ’qualitative’ difference lead to changes in the shape of these pRFs in prosopagnosia that are better characterised by the CSS model, perhaps? Perhaps more straightforwardly, and related to the above, could differences in the localisation of face-selective regions have driven the difference in prior work compared to here?

      We agree that the use of high-level mapping stimuli (including faces) would be expected to add to the reliability of the present results for DPs and could have further emphasized differences between the groups if true differences did, in fact, exist. In the section of the Discussion titled “What factors may have contributed to the different results for the present study and Witthoft et al. (2016)”, we speculate on the extent to which the type of mapping stimuli and various other methodological factors (e.g. stimulus size, aperture design, pRF model) could have explained the divergent findings in our study versus that of Witthoft et al. (2016). In brief, our use of more colorful, naturalistic stimuli targeting higher-level visual areas elicited better model fits than the black and white checkerboard pattern used by Witthoft et al. (2016). The CSS model we used is better suited for higher-level regions and makes fewer assumptions than the linear pRF model. The field of view of our stimulus was smaller but still representative of the visual angle subtended by faces in the real world. Finally, our aperture design and longer run length likely also improved reliability.

      Regarding the type of pRF model deployed, our use of a non-linear exponent (versus a linear model as in Witthoft et al. (2016)) is unlikely to explain the similarity we observed between the groups in terms of pRF size. Specifically, the groups did not show substantial differences in the exponent across ROIs, as seen in Figure 1G, so the use of a linear model should, in theory, produce similar outcomes for the two groups. We have explicitly mentioned this in the Discussion as follows:

      “Both groups, however, evinced highly similar values for the compressive static nonlinearity parameter across the ROIs studied (Figure 1G). Because this nonlinear exponent parameter did not considerably differ between DPs and controls, the use of a linear model in prior work (Witthoft et al., 2016) is unlikely to explain the massive group differences they reported, as it would be expected to scale pRF estimates similarly for both groups.”

      Overall, these methodological improvements, along with our larger sample size, make us confident in our findings. These are our best attempts to make sense of the divergent findings, but it is not possible to come to a definitive explanation. Examples abound of exaggerated or spurious effects from small-scale studies that ultimately fail to replicate in the related field of dyslexia research (Jednorog et al., 2015; Ramus et al., 2018) and neuroimaging research more broadly (Turner et al., 2018; Poldrack et al., 2017). Sometimes there are clear explanations for a lack of replicability (e.g. software bugs, overly flexible preprocessing methods, etc.), but many times the real reason is difficult to determine.

      Perhaps more straightforwardly, and related to the above, could differences in the localisation of faceselective regions have driven the difference in prior work compared to here?

      The reviewer astutely points out that differences in ROI definition could have played a role in the differences between our work and that of Witthoft et al. (2016). While Witthoft et al. (2016) used a fixed statistical threshold for ROI definition, the authors reported no significant group differences in ROI volume; Nevertheless, it is problematic to confidently establish true equivalence with a sample size of only 7 DPs as they had. If a fixed threshold inadvertently captured slightly different sub-populations of voxels between the groups due to generally weaker face-selectivity among the DPs, it could have heavily skewed the pRF estimates in such a small sample. Our use of the variable-threshold analysis (top 20% of face selective voxels within bounds of a group-defined mask) effectively eliminates this potential spatial sampling artifact.

      Finally, the lack of variations in the spatial properties of these brain regions is interesting in light of the theories that spatial integration is a key aspect of effective face recognition. In this context, it is interesting to note the marked drop in R2 values in face-selective regions like mFus relative to earlier cortex. The authors note in some sense that this is related to the larger receptive field size, but is there a broader point here that perhaps the receptive field model (even with Compressive Spatial Summation) is simply a poor fit for the function of these areas? Could it be that these areas are simply not spatial at all? A broader link between the null results presented here and their implications for theories of face recognition would be ideal.

      The reviewer highlights an excellent point regarding the marked drop in R squared from the early visual cortex to anterior face-selective regions like mFUS. We believe this drop reflects two converging factors. First, it raises the methodological question of whether there is a more effective pRF stimulus for these more anterior regions. For example, it might be possible to obtain higher and more reliable responses there using single isolated faces (Cf. Kay, Weiner, Grill-Spector, 2015).

      Second, we agree that the pRF model might ultimately be an incomplete characterization of the neural function in these higher-level areas. While we would not go so far as to say that these areas are “not spatial at all" (given that they do exhibit reliable visual field coverage), their primary computational role may shift from strict spatial mapping toward position-invariant feature extraction and identity representation. As Reviewer 2 suggests, one possibility is that other brain processes (e.g. functional or structural connectivity between ROIs) may give rise to holistic face processing in ways that are not captured by pRF properties.

      Reviewer #1 (Recommendations for the authors):

      In addition to the points raised in the public review, please address the following issues:

      Related to the question about the localisation of face-selective regions in prosopagnosia (and whether the localised regions differ in the DP vs control analyses), one way to better consider this would be to report the location and size or surface area of the localised regions in typical vs. DP individuals. Perhaps analyses using an averaged or standardised ROI (e.g., averaging control ROIs and applying this to prosopagnosics) would also be of interest to consider how this factor might influence the results.

      As above, a greater discussion of potential reasons for the null results of the present study relative to prior work would be ideal, including consideration of differences in localization of the brain regions and predictions for the way the different pRF models (Gaussian vs. CSS) might have created this (lack of) difference, is my suggestion. Greater discussion of the implications of these findings for theories of face recognition more broadly would also be ideal (e.g., whether the drop in R2 values in face-selective regions suggests a general lack of spatial selectivity).

      As detailed in our responses to the Public Review above, we completely agree that ROI localization and model choices are critical factors when comparing our results to prior work.

      To briefly reiterate: our use of the variable-window analysis explicitly equates ROI sizes across participants, effectively eliminating the spatial sampling artifact that may have arisen had someone used a fixed threshold. We have now explicitly highlighted this methodological strength in both the Methods and Results sections. Furthermore, as shown in Figure 1G, the CSS exponent was highly similar between groups, meaning the model choice alone is unlikely to explain the divergent results (now noted in the Discussion).

      Relatedly, one issue with the interpretation of the null results in the present study is in the statement that ’our results provide strong empirical evidence that pRF properties are highly similar between DPs and controls’. This comes back to the old ’absence of evidence is not evidence of absence’ argument, and I would suggest this statement be more carefully worded - there is certainly a consistent lack of differences between the two groups, which allows one to make the argument that properties are likely similar. But I suggest the authors could be more careful in making this statement.

      We agree that “the absence of evidence is not evidence of absence”, and we appreciate the push to be more precise in our claims.

      To substantiate our claim that pRF properties are indeed similar between the two groups, we have incorporated complementary Bayesian analyses (as also requested by Reviewer 2). As detailed in our response to Reviewer 2 (Point 2) and reported in the new Supplementary Table 6, Bayes Factors using both default and ‘ultrawide’ priors provided consistent, moderate-to-strong evidence explicitly in favor of the null hypothesis across the visual hierarchy. Combined with our frequentist confidence intervals, this allows us to rigorously assert that these spatial properties are highly similar, rather than merely relying on a frequentist failure to reject the null.

      Finally, one typo is present at the bottom of p. 14, which should be ’differentially affected DPs and controls’

      Thank you for catching this typo - it has been corrected.

      Reviewer #2 (Public review):

      Summary:

      This is a well-conducted and clearly written manuscript addressing the link between population receptive fields (pRFs) and visual behavior. The authors test whether developmental prosopagnosia (DP) involves atypical pRFs in face-selective regions, a hypothesis suggested by prior work with a small DP sample. Using a larger cohort of DPs and controls, robust pRF mapping with appropriate stimuli and CSS modeling, and careful in-scanner eye tracking, the authors report no group differences in pRF properties across the visual processing hierarchy. These results suggest that reduced spatial integration is unlikely to account for holistic face processing deficits in DP.

      Strengths

      The dataset quality, sample size, and methodological rigor are notable strengths.

      Weaknesses

      The primary concern is the interpretation of the results.

      (1) Relationship between pRFs and spatial integration While atypical pRF properties could contribute to deficits in spatial integration, impairments in holistic processing in DPs are not necessarily caused by pRF abnormalities. The discussion could be strengthened by considering alternative explanations for reduced spatial integration, such as altered structural or functional connectivity in the face network, which has been reported to underlie DP’s difficulties in integrating facial features.

      We agree that intact pRF properties do not preclude the existence of holistic processing deficits, and that altered structural or functional connectivity within the broader face network is a plausible alternative mechanism for such deficits. To ensure this distinction is clear to the reader, we have updated the Discussion section to highlight these alternative explanations for holistic processing deficits, citing relevant literature.

      “However, intact pRF properties do not preclude impairments to holistic processing. Such behavioral deficits could instead arise from abnormalities in broader neural networks due to either altered functional connectivity (Avidan et al., 2014; Lohse et al., 2016; Rosenthal et al., 2017) or structural connectivity (Gomez et al., 2015; Song et al., 2015b).”

      (2) Beyond the null hypothesis testing framework

      The title claims "normal spatial integration," yet this conclusion is based on a failure to reject the null hypothesis, which does not justify accepting the alternative hypothesis. To substantiate a claim of "normal," the authors would need to provide analyses quantifying evidence for the absence of effects, e.g., using a Bayesian framework.

      To directly address the reviewer’s request to quantify evidence for the absence of an effect, we have added a Bayesian analysis of mean pRF size across all ROIs and hemispheres (Supplementary Table 5).

      Using a default Cauchy prior, the Bayes Factors favored the null hypothesis (BF<sub>01</sub> > 1) in 15 out of 16 regions. Only the right OFA showed moderate evidence for the alternative hypothesis. However, upon inspecting this difference, we found that pRFs in the right OFA were actually larger in our DP sample compared to controls (DPs: mean size ± SD = 2.42±0.82; Controls: 1.78±0.75). Because the existing literature explicitly claims that DP is associated with abnormally small pRFs leading to restricted spatial integration (Witthoft et al., 2016; Avidan & Behrmann, 2021), this specific deviation (in the opposite direction) contradicts the alternative hypothesis.

      Because Witthoft et al. (2016) reported that pRFs were approximately three times smaller in DPs, we computed Bayes Factors using an ‘ultrawide’ prior (rscale = 1.414 in function ttestBF from the BayesFactor R package). The ‘ultrawide’ prior, therefore, correctly models the huge effect size expected under this alternative hypothesis. Under these conditions, the evidence strongly favored the null hypothesis across the visual hierarchy. Combined with our frequentist confidence intervals, these Bayesian analyses substantiate our claim that DPs do not suffer from the restricted spatial integration previously theorized to underlie the disorder.

      (3) Face-specific or broader visual processing

      Prior work from the senior author’s lab (Jiahui et al., 2018) reported pronounced reductions in scene selectivity and marginal reductions in body selectivity in DPs, suggesting that visual processing deficits in DPs may extend beyond faces. While the manuscript includes PPA as a high-level control region for scene perception, scene selectivity was not directly reported. The authors could also consider individual differences and potential data-quality confounds (tSNR difference between and within groups, several obvious outliers in the figures, etc). For instance, examining whether reduced tSNR in DPs contributed to lower face selectivity in the DP group in this dataset.

      Thank you for raising these methodological checks. We have addressed each point below to ensure the robustness of our findings.

      (1) Scene Selectivity in PPA: We have now explicitly reported scene selectivity in PPA in Supplementary Table 5. Unlike prior work (Jiahui et al., 2018), we found no significant reduction in scene selectivity in DPs versus controls in our current sample. This finding suggests that the visual deficits in our DP sample are specific to faces rather than reflecting a more domain-general degradation of high-level visual cortex.

      (2) tSNR Between-groups: Independent samples t-tests revealed no significant differences in regional tSNR between DPs and controls across any of the six face-selective regions (all uncorrected, p > 0.085). Bayesian analyses further supported this, with Bayes Factors generally favoring the null hypothesis of equal regional tSNR between groups (bilateral pFUS and mFUS BF<sub>01</sub> range: 3.08 to 3.21; bilateral OFA evidence was inconclusive, BF<sub>01</sub> range: 0.95 to 1.43). There is therefore no evidence that the DP group suffered from systematically worse signal quality.

      (3) tSNR Within-groups (Correlation): Finally, to address whether variance in signal quality (tSNR) relates to our selectivity measures, we computed Pearson correlations between individual tSNR and face-selectivity magnitude (percent signal change) across the six face regions. Only the left OFA showed a weak, uncorrected correlation (r = 0.32,p = 0.046), which does not survive correction for multiple comparisons. No other regions approached significance. Crucially, for tSNR to act as a confound explaining the group difference in face selectivity, tSNR itself would need to be systematically lower in the DP group. Because our betweengroups analysis established that DPs and controls have equivalent tSNR, any shared variance between tSNR and percent signal change across the entire sample cannot explain the reduction in face selectivity within the DP group.

      (4) Individual Differences and Outliers: Regarding variance and potential outliers in the figures, we intentionally plotted individual data points to provide maximum transparency regarding individual differences. To ensure that extreme values did not unduly influence our group-level conclusions, we utilized Linear Mixed-Effects Models (LMMs) for our primary statistical analyses. LMMs are highly robust to individual variance and non-normality. Furthermore, all data points included in our analyses passed strict, objective quality-assurance thresholds (e.g., stable fixation verified by eye-tracking, and pRF model goodness-of-fit R<sup>2</sup> > 0.20). Because these points represent true, high-quality individual variance rather than noise artifacts, we retained them in our analyses.

      (4) Linking pRF properties to behaviour

      The manuscript aims to examine the relationship between pRF properties and behavior, but currently reports only one aspect of pRF (size) in relation to a single behavioral measure (CFMT), without full statistical reporting: "We found no significant association between participants’ CFMT scores and mean pRF size in OFA, pFUS, or mFUS." For comprehensive reporting, the authors could examine additional pRF properties (e.g., center, eccentricity, scaling between eccentricity and pRF size, shape of visual field coverage, etc), additional ROIs (early, intermediate, and category-selective areas), and relate them to multiple behavioral measures (e.g., HEVA, PI20, FFT). This would provide a full picture of how pRF characteristics relate to behavioral performance in DP.

      We agree that a comprehensive reporting of pRF-to-behavior is worthwhile. In our revised manuscript, we extracted participant-by-participant values for the metrics used in our main group comparisons: mean pRF size, mean pRF eccentricity, visual field coverage area at 95% probability contour, pRF center dispersion, and slope relating pRF size to pRF eccentricity. We then correlated these six metrics across all ROIs and hemispheres with scores from both the Cambridge Face Memory Test (CFMT) and Famous Faces Test (FFT). To control for the large number of exploratory correlations, we applied False Discovery Rate (FDR) correction. As shown in newly included Supplementary Table 5, no pRF metrics reliably correlated with behavioral face recognition ability, further cementing our conclusion that these spatial integration mechanisms are intact and decoupled from the recognition deficit in DP. We have reported these new findings in the main text and pointed readers to Supplementary Table 5 for full statistical reporting.

      Reviewer #2 (Recommendations for the authors):

      In addition to the points raised in the public review, please address the following issues:

      (1) Table 1 & Supplementary Table 4

      Caption: "intercept has been mapped to the control group in the left hemisphere".

      Main text: "intercept was mapped to the control group in the right hemisphere."

      These descriptions are directly contradictory. Please correct them and ensure consistency across the main text, tables, and supplementary materials. Supplementary Table 4.

      (2) Supplementary Table 4

      The reported results are identical for V2 and V3, which is highly unlikely. Please double-check and correct any copying errors.

      The caption indicates significance, but the table shows no asterisks.

      (3) Figure 2A

      Missing colorbar (color, units, and label).

      (1) This caption was correct but there was a typo in the main text. The main text has been updated to correctly state that the intercept in the LMM models was mapped to the control group in the left hemisphere.

      (2) The results for V3 had incorrectly been displayed twice. We have corrected the error and updated the table. Also, we have omitted the significance key from the caption since none of the models contain any significant effects.

      (3) A colorbar (with color, units, and label) has been added to Figure 2A. Thank you for your keen eye and attention to detail.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      This in situ cryo-ET workflow of selected plant structures provides several detailed strategies using plunge-freezing and the HPF waffle method and lift-out for notoriously difficult samples (compared to cell culture, yeast, and algae, which are far more prevalent in the literature).

      Strengths:

      A very difficult challenge whereby the authors demonstrate successful vitrification of selected plants/structures using waffle and lift-out approaches for cryoET. Because there are relatively few examples of multi-cellular plant cryo-ET in the literature, it is important for the scientific community to be motivated and have demonstrated strategies that it is achievable. This manuscript has a number of very helpful graphics and videos to help guide researchers who would be interested in undertaking that would help shorten the learning curve of admittedly tedious and complex workflows. This is a slow and tedious process, but you have to start somewhere, and I applaud the authors for sharing their experiences with others, and I expect will help other early adopters to come up to speed sooner.

      Weaknesses:

      While important, the specific specimen and cell-types selected that were successful (perhaps other plant specimen and tissues tried were unsuccessful and thus not reported) in this approach did not demonstrate success to broadly applicable to other much more prevalent and interesting and intensive areas plant biology and plant structures (some mentioned in more detail below).

      This manuscript is essentially a protocol paper and in its paragraph form, and even with great graphics, will definitely be difficult to follow and reproduce for a non-expert. Also considering the use of 3 different FIB-SEM platforms and 2 different cryo-FLM platforms, I wonder if a master graphic of the full workflow(s) could be prepared as a supplementary document that walks through the major steps and points to the individual figures at the critical steps to make it more accessible to the broader readership.

      We agree that this would help the reader to keep track of the different workflow steps. Therefore, we prepared two additional supplementary figures:

      Figure 1 – figure supplement 1: Overview of the critical workflow steps for P. patens protenemata.

      Figure 1 – figure supplement 2: Overview of the used lift-out procedures.

      Multiple times in the manuscript, important workflow details seemed to point to and be dependent on two "unpublished" manuscripts:

      (1) Line 583, 755, 790, 847-848, (Poge et al., will soon be published as a protocol).

      (2) Lines 140, 695, 716 (Capitanio et al., will soon be described in a manuscript).

      It is not clear if/when these would be publicly available. It may be important to wait until these papers can be included in published form.

      Reviewer #2 (Public review):

      Summary:

      Poge et al. present a workflow for studying plant tissue by combining high-pressure freezing, cryo-fluorescence microscopy, FIB milling, and cryo-electron tomography (cryo-ET). They tested various plant tissues, including Physcomitrium patens, Arabidopsis thaliana, and Limonium bicolor. The authors successfully produce thin lamellae suitable for cryo-ET studies. Using sub-tomogram averaging, they determined the Rubisco structure at subnanometer resolution, demonstrating the potential of this workflow for plant tissue studies.

      Strengths:

      This manuscript is likely the first to systematically apply FIB milling and cryo-ET to plant tissue samples. It provides a detailed methodological description, which is not only valuable for plant tissue studies but also adaptable to a broader range of biological tissue samples. The study compares the plunge freezing method with a high-pressure freezing method, demonstrating that high-pressure freezing can vitrify thick tissues while preserving their native state. Additionally, the authors explore two methods for plant tissue sample preparation, the "waffle" method and in-carrier high-pressure freezing combined with the "lift-out" approach. The "waffle" method is suitable for samples less than 25um, while the in-carrier high-pressure freezing method can process samples up to 100um.

      Weaknesses:

      The described workflow is very complicated and requires special expertise. The success rate of this workflow is not very high, particularly for high-pressure freezing and life-out technology. Further improvements are needed for automation and increasing throughput.

      We thank the reviewer for the fair and detailed assessment of our manuscript.

      Reviewer #3 (Public review):

      Summary:

      The authors aimed to improve cryo-TEM workflows for plant cells. The authors present details on high-pressure-freezing protocols to vitrify, ion-mill, and image certain plant cell types.

      Strengths:

      Clear step-by-step outline on how to preserve and image cryo samples derived from plants.

      Weaknesses:

      A general current weakness of cryo-TEM is the problem of vitrifying cells that are embedded in tissues. The vast majority of cells in the plant body are currently not accessible to this technology. This is not a weakness of this specific manuscript but a general problem.

      The manuscript is well organized and well written, and the discussion covers practically all questions I had while reading the results section. I only have a few comments, all of which I consider minor.

      We thank the reviewer for the fair and detailed assessment of our manuscript.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      (1) I would like to see more part numbers of reagents and supplies used. They were largely absent.

      (2) The authors seem to refer to two other unpublished manuscripts, which have important details for this workflow, and are unavailable at the time of this submission.

      In point (1) and (2), the reviewer addresses crucial points. By the time we submit the revised version, the manuscript describing the FIB-view method in more detail is still in preparation. The step-by-step protocol was accepted for publication in Bio-Protocol but cannot yet be cited. We stated this as placeholders for the citations in the text which will be added in the version of record of this manuscript.

      Here, we wanted to give the reader an outline of the concepts which are required to image plant tissues with cryo-ET. Therefore, we omitted the full description of chemicals and supplies which will be listed in the step-by-step protocol.

      (3) A number of figure legends lack the actual specimen in the figure. Please add.

      We thank the reviewer for this comment and added specimen names and tissue type to the caption of Figures 2-4 and the figure supplements.

      (4) There are a few mixed orientations and missing figure panel labeling. Sometimes, in the same figure, the reader must compare horizontal and vertical sequences in the same panel. This makes it more difficult to figure out, especially when many panels are unlabeled (one example, Extended Data Figure 6). Every panel in the figure should have a letter. Consider using C1, C2, C3, C4 if they are a related series.

      We agree that some of the figures are difficult to understand due to different directions of image sequences. Instead of labeling every image of an image sequence with a unique letter, we decided to frame images which belong to an image sequence. These adjustments were consistently implemented for all main figures, supplementary figures and figures in the supplementary material.

      (5) Line 22. Insert "in situ" cryo-ET since cryo-FIB is part of the workflow.

      (6) Line 31. Remove redundant second "tissue" in the same sentence.

      (7) Line 31-32. Specify for At "seed embryos and Lb "salt glands".

      The suggested changes in (5)-(7) were implemented.

      (8) Line 53; add. air spaces in leaves. Why do you suggest vacuoles often contain solute "depleted" vacuoles? See: https://doi.org/10.1016/S0065-2296(08)60152-4. It's variable for sure, but I see that as an exception rather than as written, it seems to imply this is more likely than not, which I disagree with. Please modify. The primary driver for poor freezing is the very large vacuole itself and air spaces (at least in leaves).

      We changed the first two sentences starting from line 51: The most critical step in cryo-ET is the vitrification. For plant tissues, this process is complicated by the cell size (diameter typically 10 – 100 µm) which is larger than for most yeast, algae or mammalian cells, often contain water-filled vacuoles occupying up to 90 % of their cellular volume and, in the case of leaves, the tissue comprises air-filled spaces.

      (9) Lines 66-68. This oversimplification should be modified. Many freeze-substitution protocols include a fixative (typically osmium tetroxide) and 1-5% water in solvent, so technically not dehydrated (at least until resin steps).

      This line was changed to “samples are metal-impregnated and dehydrated upon embedding in a resin”.

      (10) Lines 66-69. I suggest that more recent papers that actually include resin electron-tomography (and cryo-ET) in plants with HPF data should be cited: https://doi.org/10.1093/jmicro/dfy133. There are plenty of organellar/sub-organellar studies of merit with FS-HPF (albeit I agree, not appropriate for molecular structure). The value and importance of your cryo-ET work are good, but it is very difficult and has limited accessibility. The merits of an in situ cryo-ET of plants paper will have more credibility to plant scientists who do the prior when properly framed. Please adjust accordingly.

      (12) I would have at least expected a brief review (yes, it's very limited) of plant-based cryo-EM studies for readers. There is not a lot, but it would add value and demonstrate the work of others who did cryo-ET in photosynthetic organisms that preceded this effort.

      Following the suggestions in (10) and (12), we elaborated on certain points in the introduction.

      We briefly review pioneering cryo-ET work on plant and algal system in one sentence added in line 64:

      “Previous cryo-ET work focused on Protoplasts [24], i.e. isolated cells without cell wall, isolated organelles [25], cyanobacteria [26], red algae [27] and single celled green algae [28,29].” Citing:

      (24) Preparing Arabidopsis thaliana root protoplasts for cryo electron tomography., Sanchez Carrillo et al, 2023

      (25) Molecular architecture of thylakoid membranes within intact spinach chloroplasts, Wietrzynski et al, 2025

      (26) Structure and Function of a Bacterial Gap Junction Analog, Weiss et al, 2019

      (27) In situ cryo-ET structure of phycobilisome–photosystem II supercomplex from red alga, Li et al, 2021

      (28) Charting the native architecture of Chlamydomonas thylakoid membranes with single-molecule precision, Wietrzynski et al, 2020

      (29) Towards community-driven visual proteomics with large-scale cryo-electron tomography of Chlamydomonas reinhardtii, Kelley et al, 2024

      To highlight the importance HPF-FS for EM of plant tissues, we now cite the suggested review and added a sentence in line 68 referencing two more reviews for the interested reader :

      “Currently, this is the most accessible and reliable approach to image plant tissues by electron microscopy [7,31].”

      (7) Electron tomography of plant organelles and the outlook for correlative microscopic approaches, Wang et al, 2019

      (31) Electron microscopy for imaging organelles in plants and algae, Weiner et al, 2022

      (11) Lines 74-75. While I understand the temptation to use "one-dimensional" and "two-dimensional", the chains are not straight lines, and certainly they are 3D structures. I suggest chains and sheets is sufficient here.

      The terms "one-dimensional" and "two-dimensional" were removed.

      (13) The Intro is pretty minimalist and ends rather abruptly, only mentioning one plant species used in the study. While it was the primary system used, please include the other plant targets and rationale.... Indeed, the title "Making plant tissue accessible for cryo-electron tomography" felt a bit misleading. I was expecting cells from non-embryonic roots, stem, or leaf tissue,e which would be the dominant targets for most plant scientists. Yes, A. thaliana embryos and salt glands from L. bicolor are useful plant targets, but certainly don't represent typical types of structures and potential for biotic and abiotic stress and developmental studies of multicellular plants. They certainly would be low-hanging fruit, but limited use cases for the workflow.

      (14) Please consider a title more appropriate based on the realities/constraints and limitations of what you were able to demonstrate in broadly relevant plant tissues. For example, "Making select plant tissue accessible for cryo-electron tomography" would more accurately reflect the scope of the achieved project, at least what was included in the manuscript.

      Regarding (13) and (14), we are aware that most research is done on root tips or leaf epidermis. We had no success with leaves. The air-filled space in the spongy mesophyll is very problematic for HPF and we did not manage to dissect the tissue to fit into HPF carriers without severely damaging the cells. We can imagine that other labs with access to cryo-ET setups similar to ours but more expertise in high-pressure freezing plant tissues may still be successful. On the other hand, we have initial results, indicating that Arabidopsis thaliana root tips can be vitrified using the described methods. Furthermore, we discuss the limitations of the method extensively. Therefore, we think that the title is still appropriate.

      We specified the names of the tested tissues in line 78 of the introduction.

      (15) Lines 91 and 92. I am a bit surprised that such high concentrations of sucrose (and glycerol) were used as cryo-protectants. This certainly was a hypertonic solution and would have caused plasmolysis and cell collapse (not dehydration as characterized). Good results (or at least freezing quality improvement) in cells equilibrated in much lower concentrations of sucrose (closer to those used in proline). I'm not saying you need to address it in the manuscript, but I am not surprised. Those would not have worked well as tested.

      We thank the reviewer for this advice. It may be worth screening more cryo-protectants at various concentrations for plunge freezing. We still think that most plant cells will not vitrify with this method.

      (16) The first introduction of cryo "FLM" (Leica solution) was line 62, and "int-FLM" (Delmic solution) without reference to cryo was line 111. Thermo has an integrated system referred to as iFLM. Please consider that it may cause confusion to a novice, and they should probably be differentiated together at first introduction. I assume the use of int-FLM is meant to distinguish from Thermo iFLM.

      In order to clarify this and to name the different cryo-FLM modalities already in the introduction, we added a sentence in line 62:

      “For correlative light and electron microscopy (CLEM) approach it is possible to use FLMs equipped with cryo-compatible stages (e.g. Leica SP8/Stellaris or Linkam CMS196 stage) or FLMs integrated into the FIB chamber (int-FLM, e.g. Delmic METEOR or Thermo Fisher Scientific iFLM).”

      (17) Line 124-128. Figure 1 and the corresponding text. Sure, large/severe crystals in this low-resolution TEM image are visible, but this is insufficient to confirm that much smaller ice crystals (e.g., 5-10nm) that would not be visible from just this data. Please note that other evidence to confirm vitrification would require a closer inspection.

      We agree. That is an aspect we do not address. The tilt-series recorded on our HPF samples do not show the large patterns introduced by crystalline ice. Still, the best evidence for full vitrification would be a diffraction pattern without the characteristic diffraction spots of crystalline ice. Unfortunately, we did not record diffraction patterns. And because the pixel size of our raw tilt images is too large, there are no diffraction spots in the power spectra of tilt images even when they clearly contain crystalline ice. After cryo-ET imaging, we discarded the samples. Therefore, we cannot record diffraction patterns for the lamellae shown in this work.

      (18) Line 340. I think most cell types have sufficient contrast with certain platforms, such as Hydra Helios5 pFIB or ZEISS CrossBeam. This is likely a limitation of the platform used, Scios, Aquilos, and Aquilos 2 columns and detectors. In the alternative platforms, other cellular features can definitely be resolved and contrasted that are non-membranous. This is why I expect this valuable approach would have benefited this particular work and reduced the dependency and resolution challenges for cryo-FLM, as it was essentially not available/utilized in this workflow. This should be noted accordingly in discussion or elsewhere, as it is a limitation of the platforms used, not the potential for this kind of work in general, as implied.

      We present SEM imaging and integrated fluorescence light microscopy as possibilities for targeting. In line 340 where we discuss axial targeting. The point we want to make is that SEM and int-FLM imaging are complementary methods with different limitations. Irrespective of the SEM system, for example liquid-liquid phase-separated compartments may not generate high enough contrast in SEM images but can potentially be labelled with fluorophores and therefore reliably targeted with int-FLMs. During our work for this project we milled lamellae on protonema cell files that were oriented parallel to the surface of the trenches and no cellular material was exposed at the surface of the trench. In this case, SEM block face imaging could not be used for axial targeting and we had to rely on the int-FLM.

      (19) Line 621-622 and elsewhere. The fluorescence in the images from the Leica SP8 is of chlorophyll, which would dominate with an emission filter of 500-750nm. Chlorophyll is definitely not "green autofluorescence". It emits above 650nm quite strongly. However, in lines 644-645, using the Delmic platform, the text simply states an "emission wavelength = 525nm". First, while that may be the center point of this filter or the name in the software, the manuscript should include the full spectral bandwidth of this and any other filters reported in that platform. Based on the specific exclusion of chloroplast signals in the images (dark ovoid voids), I fully expect it blocks the chlorophyll signal. Thus, interpretability and relationship would simply show locations of cells, but not exactly match if using cryo-FLM and int-FLM at the same cell location in this use case. I interpret the green fluorescence signal in int-FLM to be most likely vacuole autofluorescence rather than general cytoplasmic autofluorescence. The readers should be informed of the importance of matching emission filters if this is critical for targeting their work and matching an integrated and non-integrated FLM image.

      We thank the reviewer for making us aware of this incomplete description. We included the spectral band widths of the emission filters and replaced the term “green-autofluorescence” with “cellular autofluorescence” as a more general term. Furthermore, we added a sentence to the caption of Figure 2 and Figure 2 - figure supplement 1 (previously Extended Data Fig 3):

      “Note that the excitation wavelengths and emission filters used for FLM imaging are different from those used for int-FLM imaging. Therefore, the fluorescence signals appear different. Ideally, for most reliable targeting, excitation and emission should be the same for all FLM imaging modalities.”

      And to methods section “Lateral targeting and trench milling” the following sentence:

      “If both FLM and int-FLM imaging are employed for targeting, the used excitation wavelengths and emission filters should ideally be the same for both imaging modalities. This assures most reliable targeting. That is not the case here. Therefore, the fluorescence signals of FLM and int-FLM images (Figure 2, Figure 2 - figure supplement 1) appear different.”

      (20) Please review the paper more closely, a number of typos and grammatical errors were noted.. such as but not limited to:

      - Line 319 swift

      - Line 725 patterns

      - Line 1002 autofluorescence

      - Line 1064 Luliia Lermak.

      We thank the reviewer for carefully reading our manuscript and uncovering these mistakes. The name “Iuliia Iermak”, however, both starting with capital “i” is spelled correctly. This is the official transliteration of Ukrainian names to Latin alphabet.

      Reviewer #2 (Recommendations for the authors):

      Minor comments:

      (1) The authors tested several cryoprotectants for the plunge freezing method, which were ineffective for thick samples. For high-pressure freezing, they used either 20% (m/v) Ficoll 400 or 40% (m/v) Ficoll 400. Did they test other cryoprotectants, and does the high concentration of Ficoll 400 affect the cells?

      We thank the reviewer for the overall positive assessment of our work. In fact, we only used 20% (m/V) Ficoll 400 for high-pressure freezing. The 40% (m/v) Ficoll 400 solution was our stock solution and mixed 1:1 with growth medium. For HPF, we only tested dextrans and in contrast to Ficoll 400 we often observed plasmolysis. This indicates that dextrans put P. patens under osmotic pressure. We did not test, however, what impact a high concentration of Ficoll 400 has on growth, development and physiology of P. Patens or the other tested samples. But we suspect the impact to be minimal because tissue samples were immersed in a Ficoll-containing buffer only for 10-60 s right before freezing.

      (2) Page 15, line 277. There is no Figure 6.

      (3) Page 27, line 550. Switched off?

      (4) Page 50, line 992, 4 ℃?

      All typos in (2)-(4) were corrected.

      Reviewer #3 (Recommendations for the authors):

      (1) I appreciate that the authors highlight some of the drawbacks of their methods in the discussion and mention potential improvements that need to be accomplished to make cryo-TEM a more standard method for plant cell biology. For tissues that are more deeply embedded in the plant body (practically all sub-epidermal layers in higher plants that are not embryonic or meristematic), there is no potential method on the horizon that would allow vitrification. This means that some 99% of the plant body can currently not be vitrified, and this will likely be the major hurdle in the coming years. I find the text line 326 "can still be a major challenge for some samples" an understatement. Most samples will show vitrification problems.

      This fact does not reduce the importance of their current study, but a sentence on this would inform non-experts that cryo- and classical TEM will have to run side by side for quite some time. Clarification may help, as reviewers constantly ask for the application of cryo-TEM to investigate samples that currently cannot be vitrified.

      We agree with the reviewer that the mentioned sentence is an understatement and changed it into “is still a mayor challenge.” Furthermore, we added a new sentence at the end of the paragraph starting in line 335 “Currently, most fully intact tissues remain only accessible by conventional electron microscopy employing chemical fixation, if the dissection to fit the sample into the small volume of HPF carriers is omitted.” to emphasize that conventional TEM is currently indispensable for many if not most projects.

      (2) As the authors correctly mention, the waffle method leads to injury of neighboring cells. Cell-walled plant cells often withstand pressures of 5-10 MPa and more. Squeezing to make them burst will likely lead to a significant pressure wave running through the tissue with potential artifact formation. I was wondering if the authors considered using young cultures where the protonema are just a few cells long and may completely fit into a grid hole?

      We specifically needed two-week-old protonemata for a project we are working on with collaborators. Otherwise, this is a great suggestion. Using tissue for HPF that is small enough to fit into the cavities formed by grid bars and support film is the best way to avoid tissue damage.

      (3) It would be helpful if the authors would briefly explain why the cryo pictures show open-ended membranes, e.g., in Figure 3, ER in e, Golgi in d, or relatively sharp corners (cristae in e). Are these reconstruction artifacts or potential preparation artifacts (e.g., by the described bending of lamellae or similar due to milling)?

      This is an important point to raise. The open-ended Golgi and ER membranes are caused by the missing wedge which is the most prominent but unavoidable imaging artifact in cryo-ET. To clarify this for readers, we added a sentence in line 198:

      “The seemingly discontinuous membranes in Fig. 3d, e are caused by the missing wedge, a known imaging artifact in cryo-ET.”. Citing the paper “On geometric artifacts in cryo-electron tomography” by Turoňová et al., 2016.

      Regarding the sharp membrane corners of cristae, that is hard to say for certain. It is not the missing wedge in this case. For all our P. Patens preparations, cristae always looked like that which is different from cristae in other organisms we investigated with cryo-ET. It could be a characteristic feature of cristae in P. patens. But it could also be an artifact of the preparation which we can never fully exclude. It is not ion beam damage, however, because it is confined to a few tens of nanometers from the surface of the lamella and cristae have this appearance throughout the whole thickness of the lamella (150 to 350 nm).

      (4) Please explain the nature of the dark spots in e.g., Figure 5e.

      We marked this ice contamination introduced during transfer between microscopes as we did it in Figure 1 and added the description to the figure caption.

      (5) Line 105 "recording the green cellular autofluorescence". The autofluorescence of chlorophyll is actually red. The software seems to render it green. I would suggest deleting "green".

      We followed the suggestion and removed “green” on multiple occasions in the methods section.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      This work explores the relationship between sexual conflict and species diversification in a clade of small water striders. They use multiple phylogenetic methods to establish a potential phylogenetic tree and explore incomplete lineage sorting and introgression. They then compare their calibrated species tree with phenotypic measures of many species to try to infer the relationship between species diversity and sexual conflict. They show evidence for both ILS and introgression within the broader clade. They also find evidence that male leg diversity is associated with speciation, potentially due to sexual conflict, and that male genital grasping structures as well as female anti-grasping traits have less evidence for an association with speciation. This paper seems like a generally rigorous and interesting addition to the literature on sexual conflict and speciation, and I believe the conclusions are well supported with only a few minor concerns with methodology.

      Strengths:

      This paper verifies results using multiple methodologies to ensure robustness to changes in software use, and presents convincing evidence for the hypotheses tested.

      We thank the reviewer for their valuable and constructive suggestions.

      Weaknesses:

      (1) Lines 299-304: For the categorization of sexual conflict traits, were categories chosen by a blinded participant or by a researcher who knew the species they were observing? If any of these traits are subtle, this could add bias to the categorisation of traits.

      The categorization of morphological traits was performed by researchers who are familiar with the taxonomy and morphology of this taxa. We acknowledge that this may introduce some degree of subjectivity, and raw specimen photographs are available from the corresponding authors upon request.

      (2) Lines 325-327: It is unclear to me if you control for phylogenetic relationships in this model. Diversification rate could be lineage-specific regardless of sexual conflict, so it seems like potentially including phylogenetic relationships in a model would control for that. And similarly, lines 331-333, I may be mistaken, but it sounds like you are using lm() to model a binary outcome (presence/absence), but lm() doesn't do logistic regression as far as I know, so it may be better to model this as a logistic regression (controlled for phylogeny) using glm().

      In our original analysis, we treated the PCAmix values derived from multiple discrete traits as continuous variables and used the lm () function to test the correlation between these values and net diversification fates (lines 352-357). We agree that a phylogenetic comparative approach would be more appropriate. We plan to re-analyze the data using either glm () or phylogenetic generalized least squares (PGLS) to properly account for phylogenetic relationships. In lines 331-333, we would clarify that this part refers to the HiSSE analysis based on discrete traits, which is independent of the linear regression analysis mentioned above. Nevertheless, we will ensure that both analyses are clearly distinguished and properly described in the revised Methods section. We will update the relevant sections accordingly.

      (3) There are a few areas where the reporting of inference or statistics could be improved, and throughout the manuscript there are often mentions of 'significant' without any measure of uncertainty such as confidence intervals (example on lines 449-451). In lines 385-390, because the intervals are so wide, I would suggest saying these clades diverged between X-mya and Y-mya, rather than giving an actual estimate. It seems to me like giving a specific date is a bit overconfident when the authors have such wide intervals. On line 436, I think the authors should report confidence intervals for their 5mya estimate. In lines 455-456, what is this correlation and what are the authors' uncertainties around the estimate?

      We will carefully re-examine the entire manuscript and add appropriate measures of uncertainty.

      (4) Lines 549-545: When the two possible explanations for this result are reported, it seems like the authors are saying that because they can't think of how to test this possibility, the other possibility is more likely. But I don't think that is an argument against the first possibility.

      We agree with the reviewer that two hypotheses are not mutually exclusive. In the revised manuscript, we will rephrase this paragraph to present both possibilities more neutrally.

      (5) Lines 591-602: This paragraph confuses me. I thought that much of the introduction and Figure 1 seemed to be putting forth that the terminal segment complexity was a conflict structure that we were interested in. However, here it is stated that it does not strongly influence mating success, so is it necessarily a conflict trait? Is it demonstrated that the leg structures influence mating success?

      We have observed mating behaviors in this group and found that ASE function occurs after the male has successfully grasped the female using its legs. However, we acknowledge that our study did not include direct experiments to quantitatively test the effect of ASE complexity on mating success. Therefore, our discussion in this section is indeed somewhat speculative.

      Reviewer #2 (Public review):

      Summary:

      This study uses comparative phylogenetic methods to examine the evolution of male and female antagonistic traits in a group of small water striders. Water striders have long been a model system for studies into the sexual conflict that arises through anisogamy, the differential investment in gametes by males and females. Here, the authors aimed to reveal the evolutionary rates and trajectories of male grasping and female anti-grasping traits across species of the minute water-strider subgenus Pseudovelia. This was done by combining multiple genomic techniques to generate phylogenies to test trait evolution, quantify rates of evolution, and identify instances of incomplete lineage sorting (a result of rapid diversification) and introgression (the result of interbreeding between genetically different populations/species).

      Strengths:

      The strengths of this study lie in its comparative macroevolutionary framework, in particular the generation of multiple phylogenetic hypotheses using different methods (mitochondrial genes, USCOs, and SNPs), and contrasting these to glean insights into evolutionary patterns across species.

      Weaknesses:

      The main weakness of the study is the lack of underlying experimental evidence to explicitly show the grasping and anti-grasping functions of the various male and female traits, relying instead on studies of similar structures in more distantly related taxa. Without explicitly showing the functional mechanisms and reproductive costs of these traits, the resulting interpretations are wholly speculative. However, I would argue that such macroevolutionary studies are still very useful, and provide the groundwork for future studies untangling the relative roles of sexual conflict, cryptic female choice, sperm competition and reproductive interference in trait evolution and ultimately in speciation.

      We thank the reviewer for their encouraging and constructive comments. We agree that our study lacks direct experimental evidence to explicitly demonstrate the grasping and anti-grasping functions of the various male and female traits in Pseudovelia, and that our interpretations currently rely on comparisons with functional studies in more distantly related taxa. In the revised manuscript, we will explicitly state this limitation and refer to these traits as “putative” grasping or anti-grasping traits throughout the text where appropriate.

      Recommendations for the authors:

      Reviewing Editor Comments:

      Two reviewers and I, all experts in the study of sexual conflict, have assessed the work presented in this manuscript. We find the study well-executed and compelling, but we believe it would benefit from greater rigor in statistical reporting, clearer presentation, and experimental validation of functional traits. Addressing these concerns will strengthen its contributions to sexual conflict and speciation research.

      Both reviewers acknowledge the study's rigorous and innovative approach to exploring the relationship between sexual conflict, morphological diversification, and speciation in water striders (Gerromorpha). The paper leverages multiple phylogenetic methods (mitochondrial genes, UCEs, SNPs) to construct a robust species tree while also investigating incomplete lineage sorting (ILS) and introgression. The findings suggest a strong association between male grasping traits and speciation, though the evidence for female anti-grasping traits is less conclusive.

      The reviewers provided valuable suggestions for the authors to improve the manuscript. The details are clearly listed by the reviewers, and I believe they provide ample opportunity for the authors to refine their work. These suggestions include:

      - Improving the categorization of traits.

      - Using logistic regression for binary outcomes.

      - Ensuring that statistics are properly supported and that uncertainty is stated where appropriate.

      One of the reviewers also rightly points out that the traits have not been functionally tested, and their categorization as sexually antagonistic traits remains uncertain. The authors may want to acknowledge this important aspect and perhaps label those with uncertainty as "putative"

      Other recommendations concern clarity and the definitions of acronyms and abbreviations, some of which can be confusing.

      Thank you for the comment and for coordinating the review process. We have carefully read the valuable suggestions provided by both reviewers and have addressed each point in a detailed response below. In the revised manuscript, we have added new PGLS regression analyses, strengthened the statistical reporting, and described traits whose sexually antagonistic function has not been experimentally validated as “putative” throughout the text.

      Reviewer #1 (Recommendations for the authors):

      (1) Line 75 - phrasing confusing, do you mean 'maybe' instead of 'may'?

      Thank you for the comment. We agree that the original phrasing was confusing because “may exhibiting” is incorrect. We have revised the sentence to “…with one sex may exhibit delayed or mosaic patterns…”.

      (2) Lines 133-140 - This sentence doesn't make sense to me, and it asks the reader to refer to the results, but I feel that if I need to jump forward to the results to understand the summary in the introduction, it is counterproductive for summarizing what was done and what was found.

      Thank you for the comment. We have revised it.

      (3) Line 143 - Maybe still give a brief summary and then refer to the figure?

      Thank you for the comment. We have considered adding a brief summary before referring to Figure 2. However, due to our analytical steps are described in detail in the Materials & Methods section, we prefer to keep the transition concise and use Figure 2 as a direct visual summary of the workflow, without repeating information that is covered elsewhere in the text.

      (4) Lines 201/208 - Why did the number of individuals decrease from 201 to 158

      Thank you for the comment. All the 201 individuals were used for mitochondrial dataset. However, the full SNP matrix was extremely large, including all individuals would have imposed prohibitively high computational costs. We retained only one or two high-coverage individuals per population. We have now clarified this in the revised Materials & Methods section to avoid confusion.

      (5) Line 250 - SC as an initialism for South China is very confusing in a paper that talks about sexual conflict.

      Thank you for the comment. We have changed the initialism “SC” into “South China” in our manuscript.

      (6) Lines 281-289 - I think you may be spelling the name of some software wrong.

      Thank you for the comment. We have revised it.

      (7) Lines 374, 386 - I'm unclear why you refer to Figure 1a here.

      Thank you for the comment. We have revised it.

      (8) I'm having a hard time following all of the initialisms used, and I think it may be beneficial to spell out some of the lesser-used ones

      Thank you for the comment. We have revised it.

      (9) Are the sexes modelled separately?

      Thank you for your comment. Male and female sexual traits were modelled separately in our analysis.

      Reviewer #2 (Recommendations for the authors):

      Wow, this is an impressive piece of work. Congratulations! I confess my area of expertise is not in genomics, so I cannot provide much useful commentary on your methodology. Instead, I can give some commentary on sexual conflict, as well as some minor edits/ suggestions.

      (1) L32: I don't think the term "semi-aquatic bug" is as widely recognised in the evolutionary biology community. I would rephrase as "The Gerromorpha (semi-aquatic bugs), which inhabit..." or "Semi-aquatic bugs (e.g. water striders)...".

      Thank you for the comment. We have revised it.

      (2) L33: delete "has".

      Thank you for the comment. We have revised it.

      (3) L91: change "bug" to "bugs".

      Thank you for the comment. We have revised it.

      (4) L100: You refer to the subgenus "Pseudovelia" - what is the genus? I assume also Pseudovelia, but I think it ought to be mentioned.

      Thank you for the comment. We have mentioned it in L101: “a lineage of small water striders belonging to the genus Pseudovelia, subfamily Microveliinae of the family Veliidae”.

      (5) L101: Change "compising" to "comprises".

      Thank you for the comment. We have revised it.

      (6) L116: You note ASE modifications are "widely considered adaptations to improve grasping efficiency". Is this published anywhere, and has this been demonstrated? If so, provide citations. I don't think it has been demonstrated in Pseudovelia.

      Thank you for the comment. The function to improve grasping efficiency has not been demonstrated in Pseudovelia. We have revised it.

      (7) L117: You say "similar to those observed in other Microveliinae taxa (Maroni et al 2023)." If this is the only evidence you have of the function of the ASE in Pseudovelia, then I think you should expand either here or in the discussion to explicitly describe its role in grasping and opening the proctiger (if that's what you think is happening) and that it comes from that study. Do Pseudovelia have enclosed genitalia as well? If so, you should mention that and perhaps also reference the work of Chang Han and colleagues, who first demonstrated concealed genitalia in Gerrids.

      Thank you for the comment. We have revised the sentence to explicitly state that in other Veliidae, male ASE modifications function to open the female proctiger, and we inferred a similar function in Pseudovelia. We also confirm that female Pseudovelia have concealed genitalia, and we have now included a citation to Han et al. (2009) on this point.

      (8) L118: You talk about additional male grasping traits - if these haven't been tested you ought to call them "putative" or "likely" grasping traits. It might also be worthwhile to at some point briefly summarise how all limbs and even parts of the abdomen in Gerrids have been shown to function in grasping females during mating. Likewise, I don't believe any of the female anti-grasping features in Pseudovelia (or any other microveliid) have been experimentally shown, such as the elongated tergites and gonocoxal setae. To cover this, you ought to refer to the comparable traits in Gerridae where these roles have been explicitly tested.

      Thank you for the comment. We have revised absolute statements with more cautious wording, and added references to comparable female traits in Gerridae.

      (9) L138: You say here that ASE modifications are associated with relatively low-intensity conflict. Why do you hypothesize this? I'm not sure how you could a priori say these are the result of low-intensity conflict. Later when you discuss this in the discussion, it might be worth mentioning/expanding on alternative interpretations.

      Thank you for the comment. We have revised this hypothesis. We now propose that the absence of highly modified leg structures may have resulted in lower conflict intensity, rather than ASE modifications being associated with low-intensity conflict.

      (10) L603: This is what I have suspected - that the further diversification of these traits, which may have initially arisen through conflict, may be driven by reproductive interference rather than by SC.

      Thank you for the comment. We agree that the later diversification of ASE may be driven primarily by prezygotic isolation rather than by sexual conflict. In the revised manuscript, we have restructured this section to explicitly separate two sequential process: the initial origin of ASE complexity through sexual conflict, and the subsequent diversification potentially driven by prezygotic isolation.

      (11) As a general comment, I think somewhere in the conclusions you should suggest that future studies should explicitly test some of the assumptions made herein - e.g. the functions of the traits, and the potential role of interspecies interactions in driving the diversification of traits.

      Thank you for the comment. We have added a paragraph in the Discussion section outlining future works.

      (12) L893: Figure 1. I think in the legend it might be good to restate what the clade names are, i.e. EA, MAL, etc.

      Thank you for the comment. We have revised it.

      (13) L903: Figure 2: "Traits" is misspelt in the bottom left panel.

      Thank you for the comment. We have revised it.

      (14) L913: Figure 3: Maybe add a line saying coloured bars represent the clades, as identified in Figure 1.

      Thank you for the comment. We have revised it.

    1. Author response:

      The following is the authors’ response to the original reviews.

      We would like to express our sincere gratitude for accepting our manuscript for public review. We are encouraged by the generally positive reception of our work and trust that the revisions we have made adequately address the concerns that were raised.

      The revised manuscript reflects this work. The complementation experiment, in which a silent mutation at the ATHB2miP start codon produces a constitutive shade-response phenotype despite an unchanged full-length ATHB2 sequence, provides direct genetic evidence for endogenous ATHB2miP function. Immunoprecipitation mass spectrometry from the same complementation lines further demonstrates that the TTG-to-CTC substitution redirects translation to alternative initiation sites, altering the repertoire of ATHB2 proteoforms. Together with the FRET-FLIM, EMSA, and transcriptomics data, we believe the revised manuscript makes a compelling and internally consistent case for the proposed regulatory mechanism.

      Reviewer #1 (Public review):

      Summary:

      The authors report evidence for a microprotein of AtHB2-miP. The authors came across HB2 in a screen for alternative transcription start sites in Arabidopsis in response to white light or a white light followed by a far-red light representative of shade. Out of 337 potential microproteins, authors selected AtHB2. At the beginning of the manuscript, it is investigated that an alternative transcription start site of HB2 gene can be used in response to far-red light. The resulting shorter protein form seems to interact with HB2 protein forms, altering the localization of HB2 in transient expression assays. The functionality of HB2-miP overexpression has been addressed in transgenic Arabidopsis lines using a 35S promoter. The responses and phenotypes were compared with either WT or various types of athb2 mutant lines with disrupted HB2 gene. Such mutants and the 35S promoter-driven AtHB2-miP line showed various types of phenotypes versus each other that can be classified as mild or none, e.g. small effects on root growth, iron homeostasis gene expression, and iron contents.

      Strengths:

      The authors performed an interesting screen for alternative transcription start sites which resulted in 337 candidates (Figure 1A). Principally, it can be interesting to find that plants may use alternative start sites for HB2 in response to shading light. The authors provide evidence that alternative transcription start sites of HB2 can be present and used in response to FR. The possibility that potentially resulting small protein may have effects under FR light, causing alteration of root growth and physiology, is an interesting idea.

      We thank Reviewer 1 for this summary and for the constructive criticisms that helped us improve the manuscript considerably.

      Weaknesses:

      (1) The transient expression experiments are not conducted with much detail to demonstrate that HB2miP is produced and can interact with the regular protein. The localization of HB2 was found to be linked with condensates, but perhaps not in the presence of HB2miP. Clearly, the lack of quantitative and qualitative analysis hampers a clear assessment of this point.

      We have addressed this concern at multiple levels. The revised manuscript includes quantified FRET-FLIM lifetime measurements from multiple nuclei, demonstrating a statistically significant reduction in eGFP-ATHB2 fluorescence lifetime when co-expressed with mCherry-ATHB2miP relative to the mCherry control (Fig. 2C, D). This reduction is diagnostic of direct protein-protein interaction and confirms physical interaction in planta. We have also added electrophoretic mobility shift assays (EMSA) using purified recombinant proteins (Fig. 2E). ATHB2 forms a clear retarded complex with a biotin-labeled ATHB2 binding site (CAATGATTG). Titrating increasing amounts of ATHB2miP progressively abolishes complex formation, directly demonstrating that ATHB2miP sequesters ATHB2 into a non-DNA-binding complex. The majority of nuclei expressing eGFP-ATHB2 show distinct photobody or speckle formation, while nuclei expressing eGFP-ATHB2miP show predominantly diffuse nuclear localization. Co-expression of both proteins results in disruption of the speckle pattern, indicating that heterodimer formation prevents ATHB2 from assembling into higher-order condensates.

      (2) The authors unfortunately did not provide the data of the screen to demonstrate which concrete candidates may have microProteins and whether there is enrichment of certain functions. There is no supplemental table accompanying Figure 1A.

      We apologize for the oversight. The full list of 377 microProtein candidates, including read counts per condition and functional annotation, is now provided in Supplementary Dataset 1.

      (3) One of the major unclear points that is also not addressed in the discussion is that the function of miR is studied in overexpression plants (35S promoter::miP). The effects are only compared to wild type and various lines of HB2 knockouts or knockdowns, partly with fairly uncharacterized phenotypes. It can now not be clearly determined whether the miP effects are due to a regular function of miP or due to overexpression of it. A needed control would be a 35S::AtHB2 line, or better at least two different lines (only a single miP overexpression line investigated). Since it has not been assessed by deletion mutant analysis to determine which protein parts of miP are involved in the protein regulation, it cannot be ruled out that the observed miP effects are not naturally occurring but the result of ectopic expression of a protein. Clearly, the effect of miP would be ideally studied in an environment where the levels can be controlled and the resulting phenotypes and protein levels quantified.

      This concern has been addressed by three complementary approaches. First, we included here two independent 35S::ATHB2miP lines, both showing elongated hypocotyls consistent with reduced ATHB2 activity, and two independent 35S::ATHB2 full-length lines, which show the opposite phenotype. This rules out T-DNA insertion artifacts and confirms that the direction of the overexpression effects is specific to the protein being overexpressed.

      Author response image 1.

      We acknowledge that both overexpression systems are subject to autoregulatory feedback: 35S::ATHB2miP plants sequester ATHB2, thereby relieving its autorepressive loop, which leads to increased endogenous ATHB2 transcription, as confirmed by our RNA-seq data showing elevated reads across ATHB2 exons 1 and 2 in these plants (Fig. S2). Conversely, excess ATHB2 protein in 35S::ATHB2 plants strengthens autorepression of the endogenous locus. We also recognize that overexpressed ATHB2miP can form ATHB2miP: ATHB2miP homodimers, reducing the fraction available to sequester ATHB2. These feedback loops complicate quantitative interpretation but do not alter the qualitative direction of the phenotypes: in both overexpression systems, the data are internally consistent with the proposed model.

      Most decisively, the complementation experiment resolves all of these concerns. The ATHB2 WT and ATHB2 alt constructs are driven by the endogenous ATHB2 promoter, produce full-length ATHB2 protein with an identical amino acid sequence, and differ only in the capacity to initiate translation of ATHB2miP from the TTG near-cognate start codon. There is no exogenous overexpression, no homodimerization artifact, and no perturbation of the autoregulatory circuit beyond what ATHB2miP itself normally exerts. Plants carrying ATHB2 alt display constitutively enhanced hypocotyl elongation under both white light and shade. This phenotype cannot be explained by overexpression artifacts or autoregulatory side effects, and directly demonstrates that endogenous ATHB2miP produced from the TTG codon is required to restrain ATHB2 activity in planta. The overexpression data and the complementation data thus converge on the same conclusion through independent and mechanistically distinct approaches.

      (4) It is not shown that the microprotein is generated in Arabidopsis in response to shade, e.g. through Western or fluorescence protein detection. The main idea that the authors want to claim has not been addressed in Arabidopsis. There are no localization experiments of HB2 protein data in the presence of miP in Arabidopsis.

      We provide three independent lines of evidence supporting in planta production of ATHB2miP. First, ribosome profiling (Ribo-seq) reveals significantly elevated translational activity across the second half of the ATHB2 locus specifically after 45 minutes of shade treatment (see Author response image 2), consistent with preferential translation of the ATHB2miP isoform under shade. This dataset is part of a separate study currently in preparation; however, given its direct relevance to the question of ATHB2miP translation, we include the ATHB2 locus data here.

      Author response image 2.

      Ribo-seq coverage across the ATHB2 locus. Coverage from seedlings grown under white light is shown in blue, after 45 min of shade in red, and after 90 min of shade in green. Notably, translation appears to increase under shade specifically in the second half of the gene.

      Secondly, the pATHB2miP::GUS reporter drives GUS expression in the shoot apical meristem and hypocotyl, demonstrating that sequences within the ATHB2 gene body are sufficient to promote transcription and translation in these tissues (Fig. 1E, G). Third, the ATHB2 alt complementation lines produce wild-type ATHB2 protein but cannot produce ATHB2miP, and they display constitutively enhanced elongation growth precisely as predicted by the model (Fig. 5D). Fourth, immunoprecipitation mass spectrometry from ATHB2 WT and ATHB2 alt complementation lines reveals distinct sets of ATHB2-related peptides in each genotype, demonstrating that the TTG-to-CTC substitution fundamentally alters ATHB2 proteoform composition (Fig. 5B). Collectively, these data provide robust genetic and biochemical support for endogenous ATHB2miP function even without direct protein visualization.

      (5) The plants with altered HB2 forms seem to grow well and the recorded phenotypes are rather minor. Photos are not shown. At some point, the authors discuss that there could be redundancy or that HB2miP might interact with other HB proteins. However, such protein interactions have not been experimentally investigated.

      The complementation experiment (ATHB2 alt lines) reveals a strong and reproducible phenotype: exaggerated hypocotyl elongation under both white light and deep shade, exceeding all other genotypes tested. This demonstrates that, when examined in the appropriate genetic context, loss of ATHB2miP has a clear consequence for growth. Regarding interactions with other HD-ZIPII proteins: the Arabidopsis Interactome Initiative (Science, 2011) provides experimental evidence that ATHB2 heterodimerizes with HAT2, HAT3, and HAT14. Since the leucine zipper domain mediates dimerization within the HD-ZIPII class and ATHB2miP retains this domain, heterodimer formation with additional family members is structurally expected. The stronger phenotype of 35S::miP plants relative to t-athb2 single mutants under certain conditions is consistent with this interpretation and is now discussed explicitly in the revised Discussion.

      Reviewer #1 (Recommendations for the authors):

      The authors unfortunately did not provide the data of the screen. There is no supplemental table accompanying Figure 1A.

      The full list of 377 microProtein candidates is now provided in Supplementary Dataset 1. We apologize for not making this available in the original submission.

      (1) Title: seems repetitive: "elongation growth and root development"

      The title has been shortened to remove redundancy.

      (2) Introduction: (a) It seems very long and does not always address the central open questions. There is also previously published work on AtHB protein involvement in relation to growth and iron homeostasis (e.g. Capella et al. 2015). Perhaps the authors will suggest in the discussion a certain model of action. That could be better introduced to understand the importance of the findings. Hence, it would appear necessary to provide the current state of knowledge on AtHB proteins, their functions, and open questions to allow readers to better understand the connection between plant growth and iron homeostasis. This point did not come across in the Discussion, either.

      (b) Line 134-135: is this a general definition of microproteins?

      (a) The Introduction has been revised for focus and concision. A paragraph on the known functions of HD-ZIPII proteins beyond shade avoidance has been added, including roles in seed germination (Tognacca et al., 2021) and leaf cell proliferation (Carabelli et al., 2018).

      (b) We amended the text.

      (3a) Line 171ff: Would be helpful to explain the procedure briefly and explain what has been expected, also with respect to the shade experiment.

      Shade avoidance is well characterized at the transcriptional level, but whether shade also reshapes the proteome through alternative transcription start site usage had not been explored. We reasoned that shade-induced changes in TSS selection could generate truncated protein isoforms lacking specific functional domains, which could modulate the activity of their full-length counterparts. The 5'PEAT-seq approach enriches for capped transcript 5' ends, allowing genome-wide identification of active TSSs at single-nucleotide resolution and direct comparison between white light and shade conditions. A brief explanation of the rationale has been added to the Results section.

      (3b) Line 176ff: Would be helpful to explain how the findings fit with expectations, e.g. in the context of shade experiments.

      Among the 377 microProtein candidates, ATHB2 stood out as the only well-characterized shade avoidance regulator, and the alternative protein it encodes retains the leucine zipper domain, suggesting it could interfere with the dimerisation-dependent DNA-binding activity of full-length ATHB2. This combination of biological relevance and a clear mechanistic hypothesis made ATHB2miP the natural choice for functional characterization. This context has been added to the Results.

      (3c) Line 190: 377 potential microProteins candidates were identified. However, this finding is not further explained. What kind of microProteins were there? Were enrichment studies conducted and what did they show? How related were proteins to the shade response? Was the approach successful? Finally, only a single candidate was picked and studied. What were the criteria? There is no list of 377 microproteins provided, although this is a result mentioned in Figure 1A.

      The full list of candidates with functional annotations is provided in Supplementary Dataset 1. Among the candidates, ATHB2 was selected based on its status as a well-characterized shade avoidance regulator and its structural similarity to the LITTLE ZIPPER microProteins, which regulate HD-ZIPIII factors through the same competitive dimerization mechanism. The rationale for candidate selection has been expanded in the Results section and directed readers to Supplementary Dataset 1.

      (3d) Line 220: Would be helpful to explain why this control is chosen, and what aspect of the experiment it should control.

      The pATHB2control::GUS construct is identical to pATHB2miP::GUS except that GUS is fused out of frame with the alternative protein sequence. Its lack of signal confirms that the expression observed in pATHB2miP::GUS requires the correct reading frame and cannot be explained by transcriptional read-through or leaky expression from the ATHB2 gene body. This explanation has been added to the Results.

      (3e) Line 228: Is this typical for a microprotein regulation?

      There is no established precedent for what is "typical" in this context, as genome-wide studies of alternative TSS-derived microProteins remain scarce. Our study is among the first to show systematically that environmental signals can induce alternative TSS usage to produce regulatory microProteins from within existing gene loci, which is itself a novel finding. This point has been made explicit in the text.

      (3f) Figure 1A-C: Would be helpful to explain abbreviations.

      All abbreviations in Figure 1 have been defined in the figure legend.

      (3g) Figure 1A-C: There is no quantification of miP formation in response to FR; hence the data is not yet convincing.

      The figure title has been revised to remove the implication that microProtein production has been directly quantified at the protein level. The 5'PEAT-seq data in Figure 1B are inherently quantitative, with read counts at the alternative TSS showing a clear peak at 45 minutes of shade. The pATHB2miP::GUS reporter requires both transcription from the alternative promoter region and translation in the correct reading frame, as demonstrated by the out-of-frame control (Fig. 1F), making it a functional readout of the capacity of this locus to produce protein from the alternative TSS.

      (3h) Figure 1E-G: GUS staining should be done with and without the FR treatments used in Figures 1A-C.

      All seedlings shown in Figures 1E-G were subjected to deep shade treatment prior to sampling, as now stated explicitly in the figure legend.

      (3i) Line 232/233: Would be helpful to explain why the authors expected that.

      The LITTLE ZIPPER proteins are short leucine zipper-containing proteins related to the HD-ZIPIII family. They inactivate HD-ZIPIII transcription factors by forming non-productive heterodimers through their shared leucine zipper domain. Since ATHB2miP likewise retains only the leucine zipper of ATHB2 while lacking the homeodomain, we predicted by direct analogy that it would inhibit ATHB2 through the same competitive dimerization mechanism. This reasoning has been made explicit in the text.

      (3j) Figure 2: A, The different localization patterns are not quantified. C, The images seem to indicate different localization. Real co-localization and its quantification between ATHB2 and AtHB2miP or AtHB2HD is lacking, especially pointing out in better detail whether there are changes over time of microprotein expression. Explanations of statistics are lacking.

      Localization patterns have been quantified and the counts added to Figure 2A. The majority of nuclei expressing eGFP-ATHB2 showed distinct photobody or speckle formation, consistent with ATHB2 homodimerization driving higher-order nuclear condensate assembly. Nuclei expressing eGFP-ATHB2miP showed predominantly diffuse nuclear localization. Co-expression of ATHB2 and ATHB2miP (Fig. 2C) disrupted the speckle pattern, indicating that heterodimers are incompetent to form or maintain condensates. The FRET-FLIM data in Figure 2D provide the most rigorous measure of spatial proximity, demonstrating physical interaction at the nanometer scale. Statistical details are now described in the figure legend.

      (3k) Are protein interactions affected by light treatments?

      This is a well-framed question. The FRET-FLIM experiments were performed under standard light conditions. Testing whether the interaction strength is light-dependent would require stable transgenic lines expressing both fusion proteins in Arabidopsis, which are beyond the scope of this revision. The genetic complementation data indicate that the functional consequence of the interaction is most pronounced under shade, even if the interaction itself may not be light-regulated. We note this as a direction for future work.

      (3l) Line 270: It would be helpful to explain whether it is structurally expected that the different proteins interact.

      Yes, interaction is structurally predicted. Both ATHB2 and ATHB2miP contain a leucine zipper domain, a well-characterized coiled-coil dimerization motif. It has been established that the leucine zipper is both necessary and sufficient for dimerization among HD-ZIP proteins (Sessa et al., 1993). Heterodimer formation between ATHB2 and ATHB2miP is therefore a direct structural prediction. This has been stated explicitly in the revised text.

      (3m) Line 292ff: The g, e gxe effects have not been studied nor the true effects of miP since the proper genetic effects cannot be compared in the setup. Is the background of 35S::miP wild type? If so, what is the effect of endogenous miP? In any case, a control of 35S::Full-length protein would be important for comparison, since it cannot be ruled out that effects are due to ectopic overexpression rather than miP. The proper controls are needed to not draw any misleading conclusions.

      The experimental design compares three genotypes (Col-0, t-athb2, and 35S::ATHB2miP) under three light conditions, allowing identification of genes whose expression depends on genotype, environment, and their interaction. A 35S::ATHB2 full-length line has now been included in the growth assays (see above). Its inclusion in the RNA-seq experiment would require an additional sequencing run beyond the scope of this revision; however, the convergence of the t-athb2 and 35S::ATHB2miP transcriptomes on the same set of differentially expressed genes, achieved through two mechanistically independent perturbations of ATHB2 activity, provides strong evidence that the observed transcriptional changes reflect genuine loss of ATHB2 function rather than overexpression artifacts.

      (3n) Line 310: "Having established" must be carefully rephrased. It has not been shown that ectopic miP expression perturbs AtHB2 function.

      We respectfully disagree. The convergence of the t-athb2 and 35S::ATHB2miP transcriptomes on the same set of differentially expressed genes, through two mechanistically independent perturbations of ATHB2 activity, demonstrates that ectopic ATHB2miP expression perturbs ATHB2 function. Furthermore, the ATHB2 alt complementation data provide direct genetic evidence that endogenous ATHB2miP restrains ATHB2 activity in planta. The phrase "having established" is therefore accurate in context and has been retained.

      (3o) Line 310ff: Would be helpful to explain the outcome of differential expression in response to light treatments. Were the responses expected? How did they compare to the experiment described in Figure 1?

      Differential gene expression under increasing shade duration revealed progressive induction of auxin biosynthetic genes and known shade-avoidance targets in wild-type plants, consistent with established shade transcriptomics. In t-athb2 and 35S::ATHB2miP plants, this response was amplified and accompanied by constitutive upregulation of iron homeostasis and root development genes, even in white light. These findings are consistent with ATHB2 acting as a transcriptional repressor of these programs, and with ATHB2miP relieving this repression at the onset of shade. A brief discussion of this interpretation has been added to the Results.

      (3p) Figure 3A-C: More information should be added to the figures or the data representation should be improved. What do these expression patterns mean? The relevant information cannot be grasped.

      Figure 3 presents the statistical output of the differential expression analysis and cluster analysis. The heatmap in panel A displays expression levels of the 95 genes whose expression shows a significant genotype-by-environment interaction, with the color scale indicating CPM values. Panel B shows the expression trajectories of genes within three selected clusters across genotypes and shade conditions; the y-axis reflects expression change and the x-axis the genotype-condition combinations. The biological interpretation of these patterns is provided in the Results section, where we discuss the gene ontology enrichments associated with each cluster. The complete gene lists for all 17 clusters, including annotations, are provided in Supplementary Dataset 3, which allows readers to examine the data in full detail. Given the number of genes involved, a figure of this type necessarily presents a statistical overview rather than a gene-by-gene interpretation, and we believe the combination of the figure and the accompanying text and supplementary data provides sufficient context for readers to evaluate the findings.

      (3q) The tables are not labeled and it is not written what is represented.

      Table legends have been added to both tables. Table 1 lists DEGs related to auxin biology and hypocotyl elongation that are upregulated in both 35S::ATHB2miP and t-athb2 plants relative to wild type, with columns for gene identifier, annotation, log2 fold change in 35S::ATHB2miP, and log2 fold change in t-athb2. Table 2 lists the equivalent information for DEGs related to root development.

      (3r) Figure 4: Same comment as above in comment l, it is hard to assign effects properly to miP if there is no control on full-length proteins expressed behind the 35S promoter. There should be a clear scheme, depicting which athb2 mutant has which exact genomic structure.

      A schematic depicting the genomic structure and predicted protein product of each allele is provided in Figure 4A. Regarding the 35S::ATHB2 full-length control: we include data from two independent 35S::ATHB2 lines in this response letter (see our response to Reviewer 1, point 3), but have not added them to the main figures as we feel the ATHB2 alt complementation experiment addresses this concern more directly and cleanly. In those lines, full-length ATHB2 protein is produced from the endogenous promoter with an identical amino acid sequence, but ATHB2miP cannot be translated. The resulting phenotype is unambiguous and cannot be attributed to overexpression artifacts.

      (3s) Line 366ff: Based on which comparisons did authors get to this conclusion? Perhaps it is overstated.

      We agree the original statement was overstated. The text has been revised to reflect only what the data support: ATHB2 acts as a growth repressor in deep shade and promotes elongation growth in canopy shade. Under proximity shade, no significant differences in hypocotyl elongation were detected between wild-type and athb2 mutant plants, and this is now stated accordingly.

      (3t) Line 372: Do the authors mean really "complemented"?

      The reviewer is correct. The 35S::miP construct is not a complementation but an ectopic overexpression in the t-athb2 background. The wording has been changed to "we expressed ATHB2miP in the t-athb2 mutant background."

      (3u) Line 405ff: This section should be moved to the Discussion. It is highly speculative and not experimentally addressed.

      The speculative passage at lines 405ff has been rewritten.

      (3v) Supplementary Figure 2 and line 417: Can you please point out what are the relevant data to look at in Supplementary Figure 2?

      We apologize for the confusion. The data referenced at this point in the text are presented in Supplementary Dataset 2, not Supplementary Figure 2. The text has been corrected accordingly.

      (3w) Line 445: Why should HB2 be a negative regulator for iron uptake?

      The evidence for ATHB2 as a negative regulator of iron uptake comes from two independent loss-of-function contexts: iron levels are elevated in t-athb2 mutants and significantly so in 35S::ATHB2miP plants, where inhibition extends to additional HD-ZIPII family members. The stronger effect in 35S::ATHB2miP suggests that ATHB2 and related HD-ZIPII factors act collectively as repressors of iron uptake gene expression.

      (3x) The authors did not show photos of any of the plants. What about shoot growth?

      The phenotypes described in this study are quantitative in nature, specifically differences in hypocotyl and root length across multiple genotypes and shade conditions. We believe the quantifications presented in Figures 4 and 6 capture these differences more accurately and informatively than photographs would. Showing representative images for all genotype-condition combinations would add considerable length to the manuscript without providing additional insight beyond what the measurements already convey.

      (4a) Line 492: Is the result shown somewhere?

      The results are presented in Supplementary Dataset 1. A reference to this dataset has been added to the text at line 492.

      (4b) Line 509: Considering that quantitative analysis has not yet been performed, please formulate this carefully.

      Quantification has been added to the figure and the statement at line 509 is now supported by the data shown.

      (4c) Line 520ff: It is not discussed how to interpret the comparison of HB knockout and miP lines, especially considering that 35S::HB2 is missing.

      As described in our response to Reviewer 1 (point 3), the ATHB2 alt complementation experiment addresses this concern more directly than a full-length overexpressor. The distinct phenotype of ATHB2 alt plants, which produce wild-type ATHB2 but no ATHB2miP, provides a clean genetic separation of the two isoforms' functions. This is now discussed in the revised manuscript.

      (4d) Line 566/567: "might have stopped growing because of better nutrient supply." Is there any evidence for such assumptions?

      This statement appears in the Discussion and is clearly framed as speculative with the use of "might." We consider this appropriate for a discussion section where alternative interpretations are explored, and have retained the wording accordingly.

      (4e) Line 572ff: Very far-fetched hypotheses to link immunity, shade, and iron, without showing any precise data on the regulation under such circumstances.

      We respectfully disagree that this passage is far-fetched. The connection between shade, iron homeostasis, and immune signaling is grounded in two published findings: shade weakens pathogen defense through hormone homeostasis changes (de Wit et al., 2013), and IRONMAN peptides, which we show are regulated by ATHB2, respond to flagellin perception (Cao et al., 2024). The passage raises this as an open question rather than making a mechanistic claim, which we consider appropriate for a Discussion section. We have therefore retained the text as written.

      Reviewer #2 (Public review):

      The first portion of the manuscript centered on identifying and confirming the ATHB2 microprotein (ATHB2miP), which constitutes the core message of this study. Overall, I find no issue with the selection criteria employed for identifying alternative microprotein mRNA transcripts. However, I do have some queries that I hope the authors can address for clarity.

      We thank Reviewer 2 for the thorough and constructive assessment.

      (1) Upon reviewing the supplemental dataset where the authors listed the 377 unique novel miPs, along with those specifically in WL or shade treatments, I sought to comprehend the rationale behind focusing on ATHB2. Have the authors examined the shade response of all 377 potential microprotein candidates? Readers may be intrigued to learn how many of these candidates exhibit induction or repression under shade conditions, and whether such changes correlate positively or negatively with alterations in the full-length TSSs in response to shade. Essentially, I aim to discern the prevalence of microprotein production during shade responses and any shared characteristics among these microprotein transcripts. This inquiry also aims to uncover the existence of a common mechanism regulating microprotein transcription.

      Supplementary Dataset 1 provides the full list of 377 microProtein candidates, including read counts, which allows readers to inspect the data themselves. We did not perform a systematic analysis of shade responsiveness across all 377 candidates, nor did we examine correlations between alternative and full-length TSS changes genome-wide. We agree this would be informative and note it as a direction for future work.

      ATHB2 was selected from the candidate list on the basis of two criteria. First, the alternative protein it encodes retains a leucine zipper domain and thereby resembles the LITTLE ZIPPER microProteins, which regulate HD-ZIPIII transcription factors through competitive dimerization, providing a clear mechanistic hypothesis. Second, ATHB2 is one of the best-characterized shade avoidance regulators in Arabidopsis, making it possible to evaluate the biological consequences of ATHB2miP production in a well-defined molecular framework.

      (2) To confirm that ATHB2miP stems from an independent transcription event, the authors sequenced full-length cDNAs using PacBio IsoSeq. However, I find the information regarding isoseq missing from the manuscript. My assumption is that the full-length cDNAs were reverse transcribed from mRNAs isolated from whole seedlings, where mature mRNAs in the cytoplasm predominate, making it challenging to evaluate whether a specific mRNA undergoes post-transcriptional processing. One approach to confirming ATHB2miP as a product of independent transcription involves examining nascent mRNA produced in the nucleus. The authors may need to isolate nascent mRNAs associated with RNA Polymerase II in the nucleus from seedlings treated with shade for 45 min, and then perform reverse transcription and PacBio Iso-Seq.

      We acknowledge this limitation. The full PacBio Iso-Seq dataset has been deposited to GEO. We have avoided placing the main weight of the argument on transcript origin. Instead, we focus on independent functional evidence. The pATHB2miP::GUS reporter demonstrates that the region upstream of the TTG near-cognate start codon within the ATHB2 gene body contains promoter activity sufficient to drive expression in the shoot apical meristem and hypocotyl. The absence of signal in the out-of-frame control (pATHB2control::GUS) confirms that this expression requires translation initiation at the correct reading frame, consistent with the predicted Kozak context of the TTG codon identified by TISpredictor. Together with the ATHB2 alt complementation data, which demonstrate that mutating this TTG codon abolishes the microProtein's regulatory function in vivo, these results establish that the TTG codon serves as a functional translation initiation site regardless of whether the shorter transcript arises from independent transcription or post-transcriptional processing.

      (3) The authors noted the identification of two potential start codons, TTG and CTG, in the alternative TSS of ATHB2 using TISpredictor. Yet, it's imperative to identify the actual translation initiation site and the full-length sequence of ATHB2miP. I suggest the authors fuse an epitope tag (e.g., 3xFLAG) to the C-terminus of ATHB2 (utilizing the genomic sequence of ATHB2) and generate transgenic lines to be treated with shade to induce ATHB2miP-3xFLAG production. Affinity purification (anti-FLAG beads) and mass spectrometry can then identify the actual start site of ATHB2miP. This step is crucial, as the current ATHB2miP used may not be the exact sequence, and any observed phenotype could be artifacts arising from these lines.

      We carried out exactly this approach. Transgenic lines expressing a C-terminal triple FLAG tag from the genomic ATHB2 locus were generated, subjected to shade treatment, and used for nuclear enrichment, anti-FLAG immunoprecipitation, and mass spectrometry analysis. We detected ATHB2-derived peptides by IP-MS (Fig. 5B), confirming that the FLAG-tagged protein was successfully enriched. However, we did not recover a peptide spanning the ATHB2miP N-terminus that would directly identify the translation initiation site, most likely because ATHB2miP is expressed transiently and at low abundance. We therefore cannot assign the functional start site by mass spectrometry alone. The functional evidence, however, points unambiguously to TTG. The ATHB2 alt construct carries a TTG-to-CTC substitution at this position. Because both codons encode leucine, the full-length ATHB2 protein sequence is unchanged. Yet plants carrying ATHB2 alt display constitutively enhanced hypocotyl elongation under both white light and shade, while ATHB2 WT-complemented plants restore wild-type growth. The only functional difference between these constructs is the capacity to initiate translation from TTG, providing a direct in vivo assignment of this codon as the physiologically relevant start site. Consistent with this, IP-MS revealed distinct peptide profiles between ATHB2 WT and ATHB2 alt plants (peptides I-IV detected exclusively in ATHB2 WT; peptide V exclusively in ATHB2 alt; Fig. 5B), demonstrating that the TTG-to-CTC substitution fundamentally alters which ATHB2 proteoforms are produced. Anti-FLAG immunoblotting detected full-length ATHB2 and ATHB2miP in ATHB2 WT plants; in ATHB2 alt plants, ATHB2miP was replaced by two alternative bands: one slightly larger and one smaller. These findings are consistent with translation initiating from alternative start sites when TTG is mutated (Fig. 5C).

      (4) My confusion arose when analyzing the results in Figures 1E - G. The authors didn't specify whether these plants were subjected to shade treatment. What are the sequences within the second intron and third exon excluded from pATHB2control::GUS that promote transcription and translation? Have the authors examined the sequence features? This information is pivotal and related to the above question #1 because it may tell us whether the sequence feature is shared by other miP candidates.

      All seedlings shown in Figures 1E-G were subjected to deep shade treatment prior to sampling. This is now clearly stated in the figure legend. The pATHB2miP::GUS construct contains the genomic sequence immediately upstream of the TTG near-cognate start codon, encompassing elements within the second intron and third exon absent from the control construct. The activity of this sequence in the shoot apical meristem and hypocotyl indicates the presence of a functional promoter. Characterization of the specific sequence features responsible is an interesting question we note as a direction for future work.

      The latter part of the manuscript focused on the functional characterization of ATHB2miP. The approaches adopted by the authors resemble those used in studying antimorphic (dominant negative) alleles. However, I have several concerns regarding the approaches and conclusions.

      (5) Firstly, as mentioned in question #3, the authors did not map the actual translation initiation site of ATHB2miP. Therefore, all constructs involving ATHB2miP, such as eGFP-ATHB2miP, BD-ATHB2miP, and mCherry-ATHB2miP in Figure 2, and 35S::miP in Figures 3-5, may contain extra amino acids in the N-terminus, given that epitope tags were all added to the N-terminus. These additional amino acids could potentially impact the behavior of ATHB2miP and lead to artifacts. Identifying the translation initiation site in ATHB2miP would facilitate the development of tools to disrupt ATHB2miP expression without affecting full-length ATHB2 expression. For instance, if the "CTG" before the leucine zipper domain is confirmed as the translation initiation site, mutating it to another Leu codon (e.g., TTA) could generate transgenic lines using the genomic sequence of ATHB2, including this mutation, to evaluate the impact of losing ATHB2miP on shade responses.

      We acknowledge that all constructs used, including the eGFP/mCherry fusions, GAL4 domain fusions, the recombinant GST protein for EMSA, and the 35S::ATHB2miP overexpression line, carry N-terminal additions. To resolve this, we carried out precisely the experiment proposed: a genomic ATHB2 transgene in which the alternative near-cognate start codon TTG was mutated to CTC, a synonymous substitution that preserves the full-length ATHB2 protein sequence while preventing ATHB2miP translation. Plants carrying this construct display strongly enhanced hypocotyl elongation under both white light and deep shade. This genetic result directly maps TTG as the functional initiation site and demonstrates that ATHB2miP production from this codon has measurable physiological consequences in planta, independent of any N-terminal addition artifact.

      (6) Another concern pertains to the 35S::miP line utilized in Figures 3-5. The authors only presented results from one 35S::miP line, raising the possibility of T-DNA insertion disrupting an endogenous gene in the transgenic plant genome. It is essential to clarify how many individual T1 plants were generated and how many of them showed the same phenotype as the line used in the manuscript. Additionally, the use of the constitutive CaMV35S promoter could generate artifacts akin to neomorphic mutations. For example, the authors identified Cluster 1 genes that were only induced in 35S::miP, but not in t-athb2 or WT plants (Figure 3B); moreover, they found an overrepresentation of genes involved in root development in this cluster. This observation correlated well with the root phenotype of 35S::miP under the proximity shade (Figure 4D), in which the short-root phenotype was only observed in lines expressing 35S::miP. These data could be artifacts due to the constitutive expression of ATHB2miP in roots but didn't necessarily reflect the natural function of ATHB2miP.

      To address the concern about a single overexpression line, we present data from an additional independent 35S::ATHB2miP line earlier in this letter (see our response to Reviewer 1, point 3), alongside two independent 35S::ATHB2 full-length overexpression lines as controls. All 35S::ATHB2miP lines show elongated hypocotyls in white light and shade, consistent with reduced ATHB2 activity. The 35S::ATHB2 full-length lines show the opposite phenotype, confirming that the direction of the effect is specific to the protein being overexpressed and not an insertion artifact. Regarding the concern that constitutive ATHB2miP expression in roots may produce neomorphic effects: we acknowledge that ectopic 35S-driven expression cannot fully replicate the endogenous spatial and temporal pattern of ATHB2miP. The genes in Cluster 1, which are induced exclusively in 35S::miP plants, may partly reflect inhibition of additional HD-ZIPII family members by the overexpressed leucine zipper domain, beyond ATHB2 itself. This interpretation is discussed in the revised manuscript. Critically, however, the ATHB2 alt complementation experiment addresses this concern directly. In these lines, ATHB2miP is absent under the control of the endogenous promoter in the correct spatial context, with no ectopic expression involved. The constitutively enhanced hypocotyl elongation in ATHB2 alt plants relative to ATHB2 WT plants demonstrates that ATHB2miP has a genuine endogenous function that cannot be attributed to 35S overexpression artifacts.

      (7) Furthermore, I seek clarification regarding the rationale behind employing different shade conditions, including deep shade, canopy shade, and proximity shade, and the significance of treating plants with these conditions. The results were challenging to interpret, and I have reservations about some statements made. The authors claimed that ATHB2 acts as a growth repressor in deep shade but a growth promoter in the canopy and proximity shade (Lines 366-368). However, it appears that regardless of the shade conditions, most mutant and transgenic lines were not significantly different from WT (Figure 4C). Additionally, the definition of proximity shade in this manuscript (R:FR = 0.06) differs from that in Roig-Villanova & Martinez-Garcia (Front. Plant Sci., 2016; R: FR, 0.5-0.3). Clarity on this disparity would be appreciated.

      We employed three shade regimes to capture the spectrum of natural shading encountered by plants. Deep shade (PAR 13 µmol m-2 s-1, R: FR 0.13) simulates dense canopy where both light quantity and quality are strongly reduced. The two intermediate conditions both use PAR 45 µmol m-2 s-1 but differ in R: FR ratio (0.15 and 0.06), simulating conditions of neighboring plant competition where light quantity is less limiting but spectral quality changes. We acknowledge that the terminology "canopy shade" and "proximity shade" as used here does not match the definitions of Roig-Villanova and Martinez-Garcia (2016) and have revised the nomenclature in the manuscript to avoid confusion.

      (8) In Figure 5, no statistical analyses were presented in Figure 5C. It remains unclear whether the differences observed are statistically significant. Moreover, the values appear quite similar among all three genotypes. Even if statistically significant, do these minor differences in Fe concentrations significantly impact plant physiology? Additionally, some statements related to Figure 5 do not align with the data presented. For instance, claims about longer hypocotyls in t-athb2, athb2∆, and atbh2∆LZ mutants compared to wild type under shade conditions on high iron media (lines 453-455) were not supported by the data in Figure 5D. Similarly, statements about the differences between mutants (lines 458-460) were not substantiated by the data.

      The statistical analysis of the iron concentration data has been redone using a two-way ANOVA with tissue (root vs. shoot) and genotype as factors, followed by Tukey post-hoc comparisons. Statistical group labels are now shown directly on Figure 6C. All statements in the text making claims about genotype differences in hypocotyl or root length under iron conditions have been re-checked against the underlying statistical groupings. Unsupported claims have been corrected or removed.

      Reviewer #2 (Recommendations for the authors):

      (1) Figure 2A: The domain structure was not explained here, but instead in Figure 4A. Please incorporate that information into Figure 2A.

      The domain structure of each ATHB2 variant has been incorporated into Figure 2A.

      (2) Figure 3A: The transgenic line 35S::miP was used here but not introduced until Figure 4A.

      A brief introductory sentence for the 35S::ATHB2miP (35S::miP) transgenic line has been added to the Results section prior to its first appearance in Figure 3.

      (3) Line 283: Does logFC mean log2FC, and should logFC<1 be log2FC<-1?

      Yes, logFC refers to log2 fold change. The threshold for downregulated genes should read logFC < −1, and this has been corrected in the revised manuscript.

      (4) Figure 3B: Have the authors examined Cluster 16 genes, expressed at low levels only in 35S::miP but not the other two genotypes? Are they also related to root development?

      We examined Cluster 16 and found it is enriched for genes involved in responses to light stimuli, not root development.

      (5) Line 354-356: Please make sure "-2" and "-1" are in superscripts.

      Units have been corrected.

      (6) Line 391: "geneotypes" should be "genotypes."

      The typo has been corrected.

      (7) Line 393: Remove one instance of "all."

      The repeated word has been removed.

      (8) Figure 5A&B: I suggest the authors combine the data in A and B so readers can easily observe the change in gene expression between WL and shade 45 min.

      Thank you for the suggestion. The two heatmaps are presented sequentially in Figure 6A and B. We believe this layout allows clear comparison between white light and shade conditions and have retained the current arrangement.

      Reviewer #3 (Public review):

      Summary and Strengths:

      In this interesting manuscript, the authors identify a large number of alternative transcription start sites (TSS) and focus their functional analysis on an alternative TSS that is expected to produce a micro-protein (miP) encoding the C-terminus of ATHB2 (ATHB2miP). ATHB2miP is expected to comprise the leucine zipper part of ATHB2 and hence interact with the full-length protein through this dimerization motif. Such interactions are shown using yeast two-hybrid and FRET-FLIM assays. ATHB2 is a well-known shade-induced gene that has been implicated in shade-regulated growth responses. The authors then test the potential role for ATHB2miP genetically by comparing several athb2 loss-of-function (LOF) alleles: one does not express either full-length ATHB2 or the short ATHB2miP (t-ATHB2), two CRISPR alleles give rise to frameshift mutations in the full-length transcript but still express a potentially functional short ATHB2miP (athb2deltaLZ and athb2delta). The authors also use plants that over and ectopically express ATHB2miP (35S:miP). Overall, the results are consistent with the hypothesis that ATHB2miP inhibits the function of ATHB2, which constitutes a novel negative feedback loop. Potentially ATHB2miP may also inhibit the activity of other related HD ZIP proteins (based on 35S:miP). The effects of these genetic alterations on shade-regulated hypocotyl growth are relatively modest. Effects on root growth are also investigated and in one intriguing case, the negative feedback model does not appear to explain the data (Figure 4D, effect on lateral roots, because for this phenotype 35S:miP is very different from the lof alleles). The authors also identify a potentially interesting link between shade-regulated hypocotyl growth and iron uptake. A number of text changes and corrections to the figures would be important for clarity. They primarily concern three issues: names of the alleles, names of the studied shade conditions, and statements about significant differences between genotypes. Also, it would be interesting to know whether the effects of ATHB2 on iron uptake are due to local effects of ATHB2. Is ATHB2 expressed in roots?

      We thank Reviewer 3 for the thorough reading and for identifying specific inconsistencies.

      Weaknesses:

      (1) The naming of the different shade conditions is difficult to follow and not consistent with the way most authors in the field call such conditions. Deep shade is ok (low PAR and low R/FR, WL, PAR 13microE, R/FR 0.13). This condition is clearly defined for experiments in Figure 4. However, data in Figure 1 also use Deep shade (line 174) but PAR is not defined there. I suggest that all light conditions are clearly defined in the figure legends and in the M&M (not the case in this ms). Regarding Canopy shade (WL, PAR 45microE, R/FR 0.15) and proximity shade (WL, PAR 45microE, R/FR 0.06), see lines 355-357, this nomenclature is unclear. First proximity shade has a higher R/FR ratio than canopy shade. Second for canopy shade (compared to the WL control) PAR should decrease which is not what is done here. What is called proximity shade and canopy shade are 2 WL conditions with different R/FR ratios, which are compared to WL controls with the same PAR. It would make more sense to call them proximity shade and indicate the different R/FR ratios. Finally, extensive literature from many plant species and numerous labs has shown that hypocotyl elongation increases with R/FR decreasing. In the data shown in Figure 4, it is the opposite. Hypocotyls in Canopy shade (WL, PAR 45microE, R/FR 0.15) are longer than those in proximity shade (WL, PAR 45microE, R/FR 0.06), while with these R/FR ratios the opposite is expected. Could this be a mistake in the text? Please check.

      We agree that the terminology was confusing and have revised the nomenclature throughout the manuscript. All light conditions are now clearly defined in both the figure legends and the Materials and Methods section. Deep shade (PAR 13 µmol m-2 s-1, WL+FR; R: FR 0.13 in WL+FR) is consistently defined wherever it appears, including in the context of the 5'PEAT-seq experiment in Figure 1. The two intermediate conditions, which both use PAR 45 µmol m-2 s-1 but differ in R:FR, have been renamed to reflect their R: FR ratio rather than implying a specific natural shading scenario.

      (2) In several instances (in particular regarding data from Figures 4 and 5), the authors write that 2 genotypes are significantly different while the statistical analysis of the data does not support such statements. For example lines 392-395, the authors write that in WL the t-DNA mutant, both CRISPR mutants and 35S:miP lines all had significantly lower number of lateral roots than the WT. This is true for the t-DNA mutant (group bc, while the WT is in group a), however, all other genotypes are in group ab, hence not significantly different from the WT. Please carefully check all such statements about significant differences.

      We apologize for these inaccuracies. All statistical comparisons have been re-checked against the underlying statistical groupings, and the text has been corrected to reflect only differences supported by pairwise significance. Specifically, the statement about lateral root numbers in white light has been revised to note that only the t-athb2 mutant shows significantly fewer lateral roots than wild type; the CRISPR alleles and 35S::miP lines occupy intermediate groupings and are not significantly different from wild type in that condition.

      (3) The naming of the CRISPR mutants is problematic. In particular athb2delta, such a name suggests that the gene is deleted (also suggested by Figure 4A), which is not the case in this CRISPR allele leading to a frameshift early in the coding sequence. This is particularly problematic because in this allele ATHB2miP is still expressed, while based on such a name one would expect that in this mutant both the full-length and the miP are lost. Both CRISPR alleles lead to a frameshift and this should be clarified in Figure 4A and in the text.

      We agree that the naming was misleading. We have renamed the two CRISPR alleles throughout the manuscript. The allele carrying a frameshift in the first exon is now referred to as athb2cr2, and the allele carrying a frameshift in the third exon is now referred to as athb2cr1. Figure 4A and the text have been revised accordingly, with a clear description of the frameshift nature of each allele.

      (4) Overall hypocotyl growth phenotypes of athb2 lof mutants and 35S::miP are similar and consistent with the model. However, this is not the case for the root phenotype described in 4D. It would be interesting to discuss this.

      We thank the reviewer for flagging this apparent discrepancy. It is now explicitly discussed in the revised Discussion. The stronger root phenotype of 35S::miP plants relative to loss-of-function alleles in proximity shade conditions is consistent with ATHB2miP, when overexpressed, inhibiting not only ATHB2 but also other HD-ZIPII family members with which it can form leucine zipper-mediated heterodimers. Published interaction data (Arabidopsis Interactome Mapping Consortium, Science 2011) show that ATHB2 heterodimerizes with HAT2, HAT3, and HAT14. Since ATHB2miP retains the leucine zipper, it could form non-productive heterodimers with these proteins as well. Single athb2 loss-of-function alleles affect only ATHB2, which explains the milder root phenotype relative to 35S::miP. The partial suppression in t-athb2 35S::ATHB2miP is consistent with removing ATHB2 while retaining other HD-ZIPII substrates for ATHB2miP sequestration.

      (5) The authors propose a role for ATHB2 in the root, in particular linked to iron uptake. Is this due to a local effect of ATHB2 in the roots? Is ATHB2 expressed in roots? It would be very informative if the authors would show such data, e.g. using the reporter lines used in Figure 1. Are both the FL and the miP expressed in roots?

      Based on published expression data, ATHB2 transcript levels in roots are low relative to shoot tissues. The pATHB2::GUS reporter shows strongest expression in the hypocotyl and shoot apical meristem. This is consistent with the effects on iron uptake and root development being at least partly systemic, mediated by shoot-derived signals such as auxin. Steindler et al. (1999) showed that ATHB2-related root phenotypes depend on auxin transport, and He et al. (2020) demonstrated that ATHB2 overexpression reduces expression of PIN auxin efflux carriers and YUCCA biosynthetic enzymes, which would alter auxin distribution throughout the plant. A systemic model is also consistent with the established role of auxin as a long-distance messenger connecting shoot shade perception to root architecture adjustments (van Gelderen et al., 2018). We therefore propose that ATHB2 regulates root development and iron uptake primarily through its activity in the shoot, with downstream consequences for auxin distribution. Formally testing this through tissue-specific complementation is noted as a direction for future work.

      (6) From the description regarding 5'PEAT.seq data presented in Figure 1 (see lines 174-177) it is not clear in which light conditions the seedlings were grown. It appears that samples were collected in 3 conditions. WL and after 45 and 90 minutes of low R/FR treatment. However, then the data is discussed collectively. Does the 12398 TSS correspond to what was found in all three conditions together? Are the authors showing shade regulation of TSS? This is clearly the case for ATHB2miP. This needs to be clarified.

      We apologize for the lack of clarity. The 12,398 TSSs were identified from all three conditions combined (white light, 45 minutes of supplemental FR, and 90 minutes of supplemental FR). This is now stated explicitly in the Results. The shade condition for the 5'PEAT-seq experiment was deep shade (PAR 13 µmol m-2 s-1), and this is now stated in the figure legend and in the Materials and Methods. Shade-specific regulation of individual alternative TSS candidates, including ATHB2, is described in Supplementary Dataset 1.

      (7) The way gene expression of low F/FR effects is done might conflate circadian effects and low R/FR effects because the samples from different light conditions are not collected at the same ZT. This is how I understood the text. If I'm wrong please clarify the text. If I am right, this potential problem should be mentioned in the text.

      The reviewer's concern is valid in principle but does not apply to our experimental design. All samples were harvested at the same zeitgeber time (ZT). Plants assigned to the 90-minute shade condition were transferred to supplemental FR 90 minutes before the common harvest time; those assigned to 45-minute shade were transferred 45 minutes before; and control plants remained in white light until the same harvest point. Because all harvests were simultaneous, any differences in gene expression reflect the shade treatment rather than circadian phase. This information has been added to the Materials and Methods section.

      (8) Could the authors envisage a way to genetically test the role of ATHB2miP by using an allele that makes the full-length but not the miP? Currently, the authors use lof alleles that either make none of the transcripts (t-DNA) or potentially only the miP (CRISPR alleles). Overall, these alleles do not appear to differ in their phenotypes, suggesting that most of the effect of ATHB2miP is through ATHB2 FL. Having an allele only producing the FL would be nice (but technically I'm not sure how one could do that).

      We are pleased to report that we have done exactly this. The ATHB2 alt complementation construct carries a TTG-to-CTC substitution at the alternative near-cognate start codon. Because TTG and CTC both encode leucine, the full-length ATHB2 protein is unchanged in sequence, but translation of ATHB2miP is abolished. Independent homozygous lines carrying ATHB2 alt in the t-athb2 background display constitutively enhanced hypocotyl elongation under both white light and deep shade, while lines carrying the wild-type ATHB2 genomic transgene restore near-wild-type growth. This experiment provides precisely the allele the reviewer proposed and validates the model: endogenous ATHB2miP restrains ATHB2 activity, and its loss leads to exaggerated elongation growth.

    1. Author response:

      The following is the authors’ response to the previous reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Sensory hair cells of the inner ear convert mechanical sound vibrations into electrical signals through mechano-electrical transduction (MET). While the protein components of the MET machinery have been studied extensively, much less is known about how the surrounding membrane lipid environment contributes to hair cell function. The recent discovery that TMC1 and TMC2 also function as lipid scramblases has brought renewed attention to the importance of membrane lipid asymmetry and the mechanisms that maintain it in sensory hair cells.

      In this study, the authors identify the P4-ATPase ATP8B1 and its partner TMEM30B as key regulators of membrane lipid asymmetry in outer hair cells. Using complementary genetic models, HA-tagged knock-in mice, localization analyses, and functional experiments, they show that ATP8B1-TMEM30B is enriched in stereocilia and the apical membrane of outer hair cells and is required to maintain phosphatidylserine asymmetry, support hair cell survival, and preserve normal hearing. The parallels between the ATP8B1/TMEM30B loss-of-function phenotypes and TMC1 deafness-associated mutants with constitutive scrambling support a model in which ATP8B1-TMEM30B flippase activity maintains membrane lipid asymmetry and homeostasis, whereas constitutive TMC1-mediated phospholipid scrambling disrupts this balance and contributes to membrane instability.

      The authors have addressed the points raised during the initial review thoroughly. The revised manuscript includes clearer methodological details, additional physiological characterization, improved presentation and quantification of several datasets, and a more balanced interpretation of the localization and mechanistic findings. These changes improve both the clarity and rigor of the study while leaving its main conclusions unchanged.

      As with any study that opens a new area of investigation, important mechanistic questions remain. In particular, it will be interesting to determine how disruption of membrane lipid asymmetry ultimately impairs MET function and triggers hair cell degeneration, how flippase and scramblase activities are coordinated in vivo, and how these pathways are integrated with the broader molecular machinery underlying mechanotransduction. These questions highlight the exciting directions that this study opens for the field.

      Overall, this work provides evidence that ATP8B1-TMEM30B is a critical regulator of stereocilia membrane lipid asymmetry and represents an important contribution to our understanding of membrane homeostasis in auditory hair cells. I have no further major concerns and support publication.

      Reviewer #2 (Public review):

      Summary:

      Prior work identified TMEM30B (knockout mice) as well as ATP8B1 (human genetics and mouse model), ATP8A2 (knockout mice), and ATP811A (human genetics) as relevant for hearing. The authors also reasoned that given the recent discovery of TMC1 and TMC2's dual function as mechanotransduction channels of the inner ear and as lipid scramblases, a counterpart flippase should be in the sensory hair-cell stereocilia bundle where mechanotransduction happens. They use CRISPR/CAS to modify the endogenous mouse genes and add an HA tag at the N-terminus of the ATP8B1, ATP8A1, ATP8A2, and ATP11A proteins. Their experiments with these mice unambiguously localized ATP8B1 at the base of outer hair cell stereocilia bundles. Knockout of ATP8B1 results in loss of outer hair cells, deficient auditory function (ABR), and degeneration of outer hair cell stereocilia bundles. Similarly, hair cells from genetically modified mice with endogenous HA-tagged TMEM30B proteins show localization of this protein to outer hair cell stereocilia bundles. TMEM30B knock out mice phenocopy the ATP8B1 knock out model. Interestingly, the authors show that annexing V staining precedes hair cell loss in ATP8B1 and TMEM30B knockout mice and that proper localization of these proteins is lost in mice that lack CIB2, a protein essential for hair cell mechanotransduction.

      Strengths:

      (1) Use of knock-in HA-tagged proteins to unambiguously localize ATP8B1 and TMEM30B

      (2) Systematic characterization of auditory function (ABR), hair cell loss, and hair-cell stereocilia bundle morphology.

      (3) Advances our understanding of the role played by lipid homeostasis in auditory function.

      (4) Reports on mouse models that will be helpful to further understand the mechanistic role played by ATP8B1 and TMEM30B in normal hearing and hereditary deafness.

      Weaknesses:

      (1) Are the HA tags causing any functional issues? Function and localization of tagged proteins can sometimes be compromised. This is checked for TMEM30B and ATP8B1, but not for ATP8A1, ATP8A2, and ATP11A.

      (2) Following on the point above, is it possible that ATP8B1-HA is well localized, but localization for the other three flippases (ATP8A1-HA, ATP8A2-HA, and ATP11A-HA) is compromised by the tag? Is this potential miss-localization causing any functional phenotypes? I find surprising that there are flippases only in outer hair cells and only formed by ATP8B1. A possible explanation is that the tag is interfering with trafficking. If so, there should be a phenotype (ABRs), although this might be masked by redundancy among these flippases or caused by systemic issues (admittedly difficult to sort out).

      We would like to apologize for the oversight on our end that caused the delay and repeat consultation with you, and would like to thank you for your patience.

      As a reminder, after our manuscript underwent the full review, we discovered an issue with the final figure of the paper. This experiment is ancillary to the main story, and its removal does not alter the paper’s central findings or conclusions. This Figure 7 asked whether genetic loss of mechanotransduction (MET) alters ATP8B1/TMEM30B distribution in hair cells. After we discovered a problem with the MET-negative mouse model, we agreed with the reviewers to instead test whether pharmacological MET block has the same effect. We found that a 30-minute incubation with benzamil (MET blocker) did not alter ATP8B1 distribution (see uploaded PDF named “ATP8B1-HA_Benzamil”).

      Because this experiment was limited in scope and is difficult to compare directly with genetic deletion of MET, we think it is best to proceed with the manuscript version that removes this line of inquiry.

      We have made the following changes (compared to the most recent submission):

      - Removed Figure 7

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      In this manuscript, the authors aim to elucidate the mechanisms by which grid cells in the medial entorhinal cortex generate predictive representations of spatial location. To address this, they built a computational model integrating intrinsic neuronal dynamics with structured network connectivity. Specifically, they combine a conductance-based single-cell model incorporating biologically realistic HCN channels with a continuous attractor network that reflects known properties of grid cell circuitry. Their simulations show that HCN conductance can shift grid fields forward by approximately 5% of their diameter, consistent with experimental observations in layer II grid cells. Additionally, by introducing asymmetry in the connectivity of interneurons, the model produces larger forward shifts, which parallel properties observed in layer III grid cells. Together, these two mechanisms provide a unified framework for explaining layer-specific predictive coding in the entorhinal cortex.

      Strengths:

      A major strength of the study lies in its conceptual contribution. The authors propose two distinct mechanisms to generate forward-shifted grid fields for predictive coding. One mechanism is intrinsic and depends on the time constants associated with HCN channels. The other is network-based and results from asymmetries in interneuron connectivity. These two mechanisms correspond to different observed properties of grid cells in layer II and layer III, respectively. The modeling is based on previously validated frameworks of continuous attractor network models (e.g., Burak & Fiete; Kang & DeWeese), but it incorporates several novel features, including the incorporation of biophysically realistic HCN channels, a network architecture that excludes stellate-stellate connections and relies on interneurons, and asymmetric interneuron connectivity.

      Weaknesses:

      One of the proposed mechanisms for predictive coding, namely asymmetric interneuron connectivity, is a novel idea. However, this type of connectivity has not yet been demonstrated experimentally in the medial entorhinal cortex. Therefore, the biological plausibility of this mechanism remains uncertain and will need to be evaluated in future empirical studies.

      We agree that asymmetric interneuron-to-stellate connectivity has not yet been directly demonstrated, and we have revised the Discussion (page 15, lines 436–449) to state this limitation explicitly. As we note there, and as in most continuous attractor network models of grid cells, several elements of our network's connectivity, including the offset excitatory projections from stellate cells to interneurons that set the direction of attractor propagation, and the asymmetric interneuron-to-stellate connectivity that generates the layer III-like predictive bias, are constraints that are not derived from a fully specified, data-driven wiring diagram of the MEC. There are marked differences between the predictive coding of layer II and layer III grid cells, with the predictive bias in layer III roughly five-fold larger than in layer II. Our model predicts that these differences arise from an asymmetric directional skew in the synaptic weights between interneurons and stellate cells, present in layer III and absent, or much weaker, in layer II. Such a difference in synaptic weight or connection probability should become evident in paired recordings or connectomic reconstruction of interneuron-stellate synapses. This asymmetry has not yet been demonstrated directly, though recent anatomical work showing that stellate cell-interneuron synapses are organized at the spatial scale of individual grid-cell clusters [1] is at least consistent with the kind of spatially patterned connectivity our model requires (schematic figure 8 in Huang et. al. [1]).

      Manuscript change: Discussion (page 15, lines 436–449): added a new paragraph explicitly framing the asymmetric interneuron-stellate connectivity as an untested, falsifiable prediction, citing supporting anatomical evidence (Huang et al., 2024).

      Reviewer #2 (Public review):

      Summary:

      This study proposes that predictive spatial representations in medial entorhinal cortex (MEC) grid cells arise through two distinct biophysical mechanisms: (1) HCN conductance-dependent temporal dynamics, which generate modest forward shifts (~5% of grid field diameter) in Layer II cells, and (2) network asymmetry, enabling larger predictive shifts (~25% of grid field diameter) in Layer III cells. The model further predicts a dorsoventral gradient in predictive coding magnitude, correlating with observed HCN conductance variations. These results provide a mechanistic framework for understanding how intrinsic cellular properties and circuit architecture collectively enable prospective spatial coding in the MEC. This is an important study.

      Strengths:

      These findings reveal how cellular properties and circuit design enable prospective spatial coding. This novel, impactful study will be of interest to the field.

      Weaknesses:

      Some of the models are too mathematical and do not fit with the biological observation.

      We understand the concern that the manuscript may read as too mathematical. We have used a conductance-based formalism to describe the neurons, and much of this mathematical complexity is itself inherited from earlier models that were built directly from detailed voltage- and current-clamp experiments. The stellate cell model we use is a simplified version, due to Acker et al. (2003) [2], of the more detailed biophysical model of Fransén et al. (2004) [3]. We have added this lineage to the Methods section (“Neuron and Synaptic Models,” page 15, lines 466–467), where the stellate cell model is first introduced.

      The exact synaptic connectivity of the MEC network has also not been completely established. Guided by the anatomical work of Gu et al. (2018) [4], we speculate a local connectivity pattern consistent with that used in other continuous attractor network models of grid cells. As shown by Couey et al. (2013) [5], stellate cells are not connected to each other directly, but interact only through inhibitory interneurons, a motif we adopt in the model. The network motif and connectivity reported by Huang et al. (2024) [1] provide further support for the type of connectivity pattern used in our model. This anatomical grounding is already described in the Results section (“Biophysically detailed conductance-based grid cell attractor model,” page 3, lines 110–117).

      As stated in our response to Reviewer 1's comments, the exact connectivity of the network is not completely established. However, based on these anatomical observations, we make a testable prediction regarding the skew of the interneuron-stellate synaptic weight distribution. This skew should be present in layer III, where the predictive bias is large, and weak or absent in layer II. This prediction is already presented in the Discussion (page 15, lines 436–449), in the paragraph before the summary.

      Manuscript change: Methods and Materials, “Neuron and Synaptic Models” (page 15, lines 466–467): added a clause tracing the conductance-based stellate cell model to Fransén et al. (2004), as simplified by Acker et al. (2003). The related connectivity grounding (Gu et al., 2018; Couey et al., 2013; Huang et al., 2024) is already covered by Discussion (page 15, lines 436–449), and the testable, skew-based connectivity prediction is already covered by item 18; these points are not repeated in the Discussion. “Biophysically detailed conductance-based grid cell attractor model” (page 3, lines 110–117): added two sentences grounding the network topology (stellate-interneuron-only connectivity, exclusion of pyramidal cells) in anatomical data, and the testable, skew-based prediction was already present in the Discussion paragraph preceding the summary (page 15, lines 436–449): added a new paragraph explicitly framing the asymmetric interneuron-stellate connectivity as an untested, falsifiable prediction, citing supporting anatomical evidence (Huang et al., 2024).

      Reviewer #3 (Public review):

      Summary:

      The manuscript by Shaikh and Assisi addresses a timely and important question related to the neural circuit mechanisms underlying spatial representations during navigation. Concretely, they present a model of the medial entorhinal cortex (MEC) with biophysically detailed conductance-based stellate cells that can perform path integration and reveal two potential mechanisms underlying two forms of predictive coding by grid cells in the MEC. One mechanism uses HCN channels to explain predictive coding in MEC layer II grid cells equivalent to ~5% of the diameter of a grid field, and the other uses asymmetric connections between interneurons and stellate cells, resulting in a ~25% predictive bias of layer III grid cells. The methods and model are technically sound, and the model is expected to be useful for computational neuroscientists studying the neural mechanisms of spatial navigation.

      Strengths:

      One strength of the model is its use of conductance-based neuron models of stellate cells and interneurons, adding important biophysical constraints and details to existing continuous attractor network models of grid cells. The model fills a gap in the literature by providing mechanisms for predictive coding constrained by biophysical properties of stellate cells and simplified network topology.

      Weaknesses:

      A weakness of the model is that the neural network is relatively small (five sheets with 71 × 71 neurons each), and the 2-D toroidal topology is further simplified to a 1-D ring attractor consisting of three rings with 192 neurons each.

      The neurons were connected using periodic boundary conditions to minimize edge effects, and the connectivity was radially symmetric to limit the influence of topographic irregularities on the collective dynamics of grid cells. Therefore, we believe that increasing the network size would not have significantly altered the simulation outcomes.

      We were constrained by the number of biophysically realistic neurons that could be simulated within a reasonable time frame—approximately 25,000 for the 2-D attractor network and 576 for the ring network. There were two main reasons for this limitation. (i) The simulations had to run over time scales ranging from several seconds to minutes to ensure that the trajectory repeatedly passed through the same local neighbourhood and that the spike density was sufficient to delineate the grid fields. This process was especially time-consuming for the 2-D environment, though we managed to achieve it in a smaller network representing a 1-D environment. Additionally, the trajectories needed to extend over time to allow us to estimate any drift between the simulated animal’s actual position and its inferred position from neuronal activity. (ii) The simulations required extensive multi-parameter sweeps within the bounds of experimentally observed values, further increasing the total simulation time. Given these computational constraints, we had to limit our model to smaller neuron populations. While using simpler neuron models could have allowed larger networks, we considered it essential to retain a degree of biophysical realism. This level of detail enabled us to explore how specific conductances influenced the overall dynamics of the network. We have also added a sentence to the Methods section (“2D model,” page 16, lines 488–494) stating these computational constraints explicitly and noting that periodic boundary conditions and radially symmetric connectivity were used throughout to minimize edge and finite-size effects.

      Manuscript change: Methods and Materials, “2D model” (page 16, lines 488–494): added a sentence explaining the computational constraints that determined network size and the use of periodic, radially symmetric connectivity to limit edge effects.

      The model incorporates biophysical detail at the single-neuron level, but not at the network level. For example, it includes only stellate cells and a generic interneuron type and does not implement data-driven connectivity patterns. The restricted network size and the limited experimental knowledge about connectivity among stellate cells, principal cells, and different interneuron types in the MEC could be addressed in more detail.

      Because the network connectivity of the medial entorhinal cortex (MEC) is not yet fully understood, our model incorporates prior findings showing that stellate cells interact only through inhibitory interneurons [5–8]. In layer II, stellate cells that function as grid cells also show a topographic organization. They form clusters located between patches of pyramidal neurons. Each grid cell module consists of stellate cells that are physically contiguous, although cells from neighboring modules intermingle at their borders. Within a module, stellate cells tend to form a noisy two-dimensional lattice organized according to the phases of their grid fields [4]. In addition, axonal projections in layer II of the MEC create spatially organized connections between stellate cells and parvalbumin interneurons. Nearby neurons often, but not always, share direct connections, whereas neurons that are farther apart are linked primarily through multisynaptic pathways [5]. Together, these observations suggest that stellate cells interact via inhibitory intermediaries and are locally arranged in a network topology that closely resembles standard Continuous Attractor Network (CAN) models. We have added two sentences to the Results section (“Biophysically detailed conductance-based grid cell attractor model,” page 3, lines 110–117) making this anatomical justification explicit, and stating that layer II pyramidal cells, which form a separate microcircuit, are correspondingly excluded from the model.

      Manuscript change: Results, “Biophysically detailed conductance-based grid cell attractor model” (page 3, lines 110–117): added two sentences grounding the network topology (stellate-interneuron-only connectivity, exclusion of pyramidal cells) in anatomical data.;See Discussion (page 15, lines 436–449): added a new paragraph explicitly framing the asymmetric interneuron-stellate connectivity as an untested, falsifiable prediction, citing supporting anatomical evidence (Huang et al., 2024).

      Moreover, the manuscript lacks a thorough discussion of assumptions common to most continuous attractor network (CAN) models of grid cells, such as the use of "hand-crafted" connections between direction-sensitive conjunctive grid cells and network cells to drive attractor shifts. Including such a discussion would strengthen the manuscript. This is especially relevant given the authors' explicit claim that they have revealed two mechanisms underlying the emergence of a predictive code in the MEC. In this reviewer's view, the work demonstrates a potential mechanism, but one that requires experimental verification. The significance of the model would thus be increased by providing more experimentally testable predictions of the model.

      The exact connectivity of stellate cells and interneurons is yet unknown. But several lines of evidence point to an attractor-like connection topology. We have now included a more detailed discussion of the connectivity used in CAN models.

      Manuscript change: Discussion (page 15, lines 436–449): added a new paragraph explicitly framing the asymmetric interneuron-stellate connectivity as an untested, falsifiable prediction, citing supporting anatomical evidence (Huang et al., 2024).

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      (1) In the abstract, the authors write:

      "Our model revealed two mechanisms underlying the emergence of a predictive code in the MEC. The first relied on a time scale associated with the HCN conductance. The other depended on the degree of asymmetry in the topology of the MEC network."

      Given the central importance of these two mechanisms, the description here may be overly brief. Even in an abstract, a slightly more detailed explanation of each mechanism would enhance clarity and accessibility.

      We have modified the abstract (page 1, lines 7–21) which now includes a brief explanation of how the timing of stellate cell spikes are advanced

      Manuscript change: Abstract (page 1, lines 7–21): modified the abstract to include a detailed description of the mechanism.

      (2) In both experimental (e.g., Hafting et al., 2008; Chaudhuri-Vayalambrone et al., 2023; Ouchi & Fujisawa, 2024) and theoretical studies (e.g., Kang & DeWeese, 2019), predictive coding in grid cells has been closely associated with the phase profile of theta oscillations, including phenomena such as phase precession and phase locking. The authors' model successfully reproduces theta-range membrane potential oscillations, consistent with physiological observations. Given this, it would be valuable to know whether the model allows for an integrated analysis of the relationship between predictive coding and spike timing relative to theta phase. If such a simulation could be included in the present study, it would likely strengthen the contribution of the manuscript. However, if this is beyond the scope of the current work, a brief discussion of the potential relevance of theta-phase dynamics to predictive coding, and how this might be addressed in future studies, would still help broaden the perspective and impact of the paper.

      The predictive grid cells [9,10] are phase-locked to theta oscillations. In line with this observation, our model demonstrates that for sufficiently high theta amplitude stellate cells can be entrained to the input oscillations. We have added a paragraph to the Discussion (page 12, lines 365–370) describing this entrainment finding in the text. However, we have not included the analysis figure (see Author response image 1) itself in the manuscript.

      Manuscript change: Discussion (page 12, lines 365–370): added a new paragraph noting that the model reproduces theta-entrainment of stellate cell spiking consistent with phase-locked predictive grid cells, without including the underlying analysis figure in the manuscript.

      Author response image 1.

      (3) The Discussion section currently ends somewhat abruptly. Adding a concluding paragraph that summarizes the key findings and their broader implications would help reinforce the significance of the work for readers.

      We have now modified the discussion section (page 15, lines 450–463) to summarize key findings and the broader implications of the study.

      Manuscript change: Discussion (page 15, lines 450–463): a concluding paragraph has been added at the end of the Discussion section.

      (4) "These properties are due to the presence of a hyperpolarization-activated depolarizing current (Ih) and a persistent sodium current (INaP) in addition to leak and spiking currents (IL, IK, INa). An interplay between Ih and INaP is needed to generate the membrane potential oscillations observed here. In addition, these oscillations fall squarely within the range of theta oscillations (4-12 Hz)." (Page 3, Line 97)

      Please provide supporting evidence for these claims, such as simulation results or relevant literature references.

      We have added references supporting our claims.

      Manuscript change: Results, “Biophysically detailed conductance-based grid cell attractor model” (page 3, lines 97–100): added reference to "An interplay between I_h and I_NaP is needed to generate the membrane potential oscillations observed here. In addition, these oscillations fall squarely within the range of theta oscillations (4–12 Hz)."

      (5) "How does HCN give rise to a predictive bias? The HCN channel depolarizes the cell and is activated by inhibitory input from interneurons in the model network. Since HCN increases the cell's excitability, it speeds up the onset of spiking, translating grid fields that are farther away to locations closer to the animal." (Page 7, Line 285).

      Is this explanation derived directly from simulation data? If so, please indicate the relevant figures or results that support this interpretation.

      Reference to support the effect of HCN on the cell’s excitability has been added (page 10, lines 296–299). A paragraph in the manuscript explains how this change in excitability can cause the grid field to be translated closer to the animal (page 10, lines 300-305).

      Manuscript change: Results, “Cellular and network-based mechanisms for predictive and retrospective coding” (page 10, lines 296–299): added reference to "How does HCN give rise to a predictive bias? The HCN channel depolarizes the cell and is activated by inhibitory input from interneurons in the model Network. Since HCN increases the cell's excitability, it speeds up the onset of spiking, translating grid fields that are farther away to locations closer to the animal."

      (6) Some elements in the main figures are not clearly explained or referenced in the main text. For example, Figures 1E and F, and Figure 3B appear to lack corresponding descriptions or interpretation. Please ensure that all figure panels are explicitly discussed in the results.

      Missing explanations for Figure 1E and F have been added to the result section. Figure 3b is mentioned in the article (Page 8, line 235)

      Manuscript change: Results, “Biophysically detailed conductance-based grid cell attractor model” (page 4, lines 153–154): added missing references to Figure 1e and Figure 1f in the manuscript.

      (7) Typos

      (a) Page 4, Line 140: "as shown in Figure 1A". It seems "Figure 1D" is intended.

      (b) Figure 2A (color legend): "m.p. eamp (mV)" should be "m.p. ramp (mV)".

      These typos have been fixed.

      Manuscript change: fixed the Figure 1 panel-letter typo (Results, “Biophysically detailed conductance-based grid cell attractor model,” page 4, lines 146–147): fixed figure reference from Figure 1A (bottom) to Figure 1d (bottom) and the Figure 3 colour-legend typo (Figure 3a, page 9): fixed colour label typo from "m.p. eamp (mV)" to "m.p. ramp (mV)". and standardized all figure panel references to lowercase throughout the manuscript: Figure panel references were changed to lowercase throughout the manuscript.

      Reviewer #2 (Recommendations for the authors):

      (1) The model is based on five interconnected neuronal sheets organized in a toroidal topology, with four layers of stellate cells (71×71 neurons each) and one inhibitory interneuron layer. Key architectural features included: Stellate cells interacted exclusively via feedforward inhibition through interneurons, consistent with experimental observations (Couey et al., 2013). Interneurons projected symmetrically to other interneurons within their sheet, and each interneuron inhibited a concentric ring of stellate cells. This spatially structured inhibition, combined with toroidal boundary conditions, generated stable hexagonal activity patterns in both stellate and interneuron populations. In this model, it will be very likely that the interneurons also exhibited perspective coding, but this is not consistent with the physiology data. Can the authors comment on this?

      As stated in materials and methods, we used the interneuron activity as the “true” position of the animal. This was done because the errors accumulated during path integration were far greater than the predictive bias shown by the grid network. Therefore, it would not have been possible to discern the predictive bias from the path integration error. The interneuron field does show a skew in the opposite direction to the direction of travel. However, unlike stellate cells, this is not translation of the grid field, See Author response image 2. This is due to asymmetry in the firing rates of interneurons along its field. We have added a sentence to the Methods section (“Predictive and retrospective coding,” page 17, lines 521–525) making this distinction, between a firing-rate asymmetry and an actual translation of positional tuning, explicit.

      Manuscript change: Methods and Materials, “Predictive and retrospective coding” (page 17, lines 521–525): added a sentence clarifying that interneuron firing-rate asymmetry does not reflect a translation of positional tuning, justifying its use as the position reference.

      Author response image 2.

      (2) In the original study (Ouchi et al., 2024), it reported predictive grid cells; it has been shown that theta-rhythmic population activity in the MEC supports dynamic spatial representation, with phase-organized firing patterns enabling continuous trajectory prediction. The current model did not examine this in much detail. Could the authors discuss this or test this in their model?

      Our simulations have shown that the impact of theta oscillations on the temporal organisation of grid fields is more intricate than we initially anticipated, and further work is underway to elucidate these mechanisms. However, in line with experimental observations [9], our model demonstrates that stellate cells can be entrained to the input oscillations by increasing the amplitude of theta. See Author response image 1. As above, we have added a Discussion paragraph describing this entrainment result in the text, without including the corresponding figure in the manuscript.

      Manuscript change: Discussion (page 12, lines 365–370): added a new paragraph noting that the model reproduces theta-entrainment of stellate cell spiking consistent with phase-locked predictive grid cells, without including the underlying analysis figure in the manuscript.

      (3) In the data, the shift of the predictive grid is in a range of distribution from 22.5 {plus minus} 10.2 cm; the model did not clearly show the shift distance of the grid in the current model. It would be helpful to examine why the grid cells with different spacing could show a range of their shift in the current model.

      The expansion of grid spacing is accompanied by a lengthening of HCN conductance time scales. As demonstrated in Figure 5e, the extent of predictive coding can be enhanced by increasing these intrinsic temporal constants. We have added a sentence to the Results section (“Cellular and network-based mechanisms for predictive and retrospective coding”, page 10, lines 315–320) relating this range of model-predicted shift distances explicitly to experiments.

      Manuscript change: Results, “Cellular and network-based mechanisms for predictive and retrospective coding” (page 10, lines 315–320): added a sentence relating the range of model-predicted shift distances across grid scales to the experimentally reported range.

      (4) In the non-linearity and ensure accurate path integration, the author mapped each value of speed𝑠 measured in (𝑟𝑎𝑑∕𝑠) to its corresponding depolarising drive 𝐼 = 𝑓(𝑠) (Figure 2a). It is necessary to discuss the biological meaning of the depolarizing drive. Is the value reasonable in the biological range?

      The depolarizing drive I = f(s) is used to represent the population speed signal that is delivered to stellate cells as a somatic current, and across the simulated range of speeds its magnitude remains within the sub-nanoampere range used for current-clamp characterization of stellate cell and interneuron excitability in the original single-cell studies from which our conductance parameters were taken [2,3,11,12] We have added a sentence to the Results section (“Grid cell network can accurately path integrate 1D trajectories,” page 6, lines 184–188) stating this explicitly, so that the biological plausibility of the depolarizing drive is clear to the reader.

      Manuscript change: Results, “Grid cell network can accurately path integrate 1D trajectories” (page 6, lines 184–188): added a sentence clarifying that the depolarizing drive I=f(s) remains within the sub-nanoampere range used experimentally to characterize stellate cell and interneuron excitability.

      (5) In the study after HCN knockout, the spacing change of grid cells exhibited a linear drift to higher spacing (Giocomo et al., 2011a). This also shows grid cells with discrete modules (Stensola et al., 2012, Nature). Regarding this, how does the current model represent the discretized modules and their predictive coding?

      In our model, all stellate cells share the same grid scale and can therefore be treated as belonging to a single module. Experimentally, however, grid scale varies along the dorsoventral axis of the MEC, in parallel with systematic changes in inhibitory connectivity and HCN channel conductance [13–15]. In the model, we can reproduce different grid spacings (as seen across modules) by increasing the range of lateral inhibition, and the grid expansion observed after HCN knockout would similarly apply to modules with different grid scales. Our current implementation does not include a mechanism for generating discrete modules, which would require a network with a graded change in lateral inhibition across its spatial extent. In networks with such graded organization, several mechanisms have been proposed for how modules emerge [16,17] and these would likely apply to our model as well. We have added a paragraph to the Discussion (page 15, lines 428–435) stating this limitation and the proposed extension explicitly, with supporting citations.

      Manuscript change: Discussion (page 15, lines 428–435): added a new paragraph on the model's single-module limitation and possible extensions to discrete, dorsoventrally organized modules.

      (6) The grid cells have been shown in both the Stella cells and the pyramidal cell group? Will the current model bias their conclusion toward different cell groups? Or can it not represent these cell groups? It could be necessary to discuss this.

      Within Layer II of the MEC, stellate cells and pyramidal cells form separate, largely non-overlapping microcircuits. Pyramidal cells are commonly connected via 5− HT3a positive interneurons, while stellate cells are primarily connected via fast-spiking parvalbumin (PV<sup>+</sup>) cells and slower-spiking somatostatin-positive cells [5–7]. Further, stellate cells show a topographic organization with stellate cell clusters being separated by pyramidal neurons [1].

      Given these observations we chose a model stellate cell and fast-spiking interneuron.

      Based on our work it would be hard to say what, if any, the effect of pyramidal neurons would be to the stellate grid cell network. We have added a sentence to the Results section

      (“Biophysically detailed conductance-based grid cell attractor model,” page 3, lines 110–117) stating explicitly that the model does not include pyramidal cells and that our conclusions are specific to the stellate-cell grid-cell population.

      Manuscript change: Results, “Biophysically detailed conductance-based grid cell attractor model” (page 3, lines 110–117): added two sentences grounding the network topology (stellate-interneuron-only connectivity, exclusion of pyramidal cells) in anatomical data, which states the exclusion of pyramidal cells explicitly.

      (7) In Kropff et al., 2015 Nature, speed cells have been shown also represent predictive shift in their coding, the author achieved accurate path integration with a linear relationship between the speed of the animal and the movement of attractor is necessary and for this by introducing an invertible mapping between speed and the amplitude of the depolarizing input used to drive the stellate cells. The current model did not address the possible contribution of speed coding to the retrospective coding in grid cells. Will the authors discuss this?

      This is an interesting point. Kropff et al. (2015) [18] showed that a subset of speed-tuned cells in the MEC represent running speed with a temporal offset, effectively encoding a predictive or retrospective estimate of speed itself. Our model currently represents the population speed signal as a single, instantaneous depolarizing drive I = f(s) and does not incorporate this heterogeneity. We have added a passage to the Discussion (page 14, lines 393–402) noting that if even a fraction of the depolarizing drive to stellate cells were itself temporally offset in the way Kropff et al. describe, this could shift the magnitude, or potentially the sign, of the retrospective bias that we attribute to network asymmetry, providing an additional, speed-coding-dependent route to retrospective coding that could act alongside the intrinsic and network mechanisms we describe. Disentangling the relative contributions of speed-signal timing and network asymmetry to retrospective coding is a promising direction for future modeling work.

      Manuscript change: Discussion (page 14, lines 393–402): added a discussion of how heterogeneity in speed-cell timing (Kropff et al., 2015) could interact with network-asymmetry-based retrospective coding.

      References

      (1) Huang, L.-W., Garden, D. L., McClure, C. & Nolan, M. F. Synaptic interactions between stellate cells and parvalbumin interneurons in layer 2 of the medial entorhinal cortex are organized at the scale of grid cell clusters. eLife 12, RP92854 (2024).

      (2) Acker, C. D., Kopell, N. & White, J. A. Synchronization of Strongly Coupled Excitatory Neurons: Relating Network Behavior to Biophysics. J. Comput. Neurosci. 15, 71–90 (2003).

      (3) Fransén, E., Alonso, A. A., Dickson, C. T., Magistretti, J. & Hasselmo, M. E. Ionic mechanisms in the generation of subthreshold oscillations and action potential clustering in entorhinal layer II stellate neurons. Hippocampus 14, 368–384 (2004).

      (4) Gu, Y. et al. A Map-like Micro-Organization of Grid Cells in the Medial Entorhinal Cortex. Cell 175, 736-750.e30 (2018).

      (5) Couey, J. J. et al. Recurrent inhibitory circuitry as a mechanism for grid formation. Nature neuroscience 16, 318–324 (2013).

      (6) Nilssen, E. S., Doan, T. P., Ohara, S. & Witter, M. P. A reappraisal of the lateral and medial entorhinal subdivisions mediating parallel cortical pathways. Hippocampus in press, 1–17 (2019).

      (7) Witter, M. P., Doan, T. P., Jacobsen, B., Nilssen, E. S. & Ohara, S. Architecture of the entorhinal cortex: a review of entorhinal anatomy in rodents with some comparative notes. Frontiers in systems neuroscience 11, 1–12 (2017).

      (8) Nilssen, X. E. S. et al. Inhibitory Connectivity Dominates the Fan Cell Network in Layer II of Lateral Entorhinal Cortex. The Journal of neuroscience: the official journal of the Society for Neuroscience 38, 9712–9727 (2018).

      (9) Ouchi, A. & Fujisawa, S. Predictive grid coding in the medial entorhinal cortex. Science 385, 776–784 (2024).

      (10) Ouchi, A. Predictive grid cells: Future spatial representations in the hippocampal-entorhinal circuit. Neurosci. Res. 227, 105053 (2026).

      (11) Dickson, C. T. et al. Properties and role of I(h) in the pacing of subthreshold oscillations in entorhinal cortex layer II neurons. Journal of neurophysiology 83, 2562–2579 (2000).

      (12) Alonso, A. & Klink, R. Differential electroresponsiveness of stellate and pyramidal-like cells of medial entorhinal cortex layer II. J. Neurophysiol. 70, 128–143 (1993).

      (13) Garden, D. L. F., Dodson, P. D., O’Donnell, C., White, M. D. & Nolan, M. F. Tuning of Synaptic Integration in the Medial Entorhinal Cortex to the Organization of Grid Cell Firing Fields. Neuron 60, 875–889 (2008).

      (14) Giocomo, L. M. et al. Grid Cells Use HCN1 Channels for Spatial Scaling. Cell 147, 1159–1170 (2011).

      (15) Yoshida, M., Giocomo, L. M., Boardman, I. & Hasselmo, M. E. Frequency of subthreshold oscillations at different membrane potential voltages in neurons at different anatomical positions on the dorsoventral axis in the rat medial entorhinal cortex. The Journal of neuroscience: the official journal of the Society for Neuroscience 31, 12683–12694 (2011).

      (16) Kang, L. & Balasubramanian, V. A geometric attractor mechanism for self-organization of entorhinal grid modules. eLife 8, e46687 (2019).

      (17) Khona, M., Chandra, S. & Fiete, I. Global modules robustly emerge from local interactions and smooth gradients. Nature 640, 155–164 (2025).

      (18) Kropff, E., Carmichael, J. E., Moser, M.-B. & Moser, E. I. Speed cells in the medial entorhinal cortex. Nature 523, 419–424 (2015).

    1. Author response:

      The following is the authors’ response to the previous reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      This study uses optogenetics to activate CA3 while recordings from CA1 neurons and characterizing the excitation/inhibition (E/I) balance. They observe use-dependent alterations in the E/I balance as a result of STP and they develop a model to describe these observations. This is a very ambitious paper that deals with many issues using both experimental and modeling approaches.

      Strengths:

      This paper examines important principles regarding the manner in which synaptic circuitry and use-dependent synaptic plasticity can transform inputs and perform computations.

      Weaknesses:

      (1) I am pleased that the authors revised their section on external calcium. They now approach this issue by calculating the effect of low external calcium on plasticity. These calculations are based on studies of numerous types of synapses, which are unlikely to be directly comparable to hippocampal synapses.

      We have clarified how we use published studies and our own model to estimate the effect of lower (more physiological) levels of external calcium. Among these we do have data from hippocampus. From the text:

      “Specifically, in hippocampal CA3->CA1 glutamatergic synapses at 1.5 mM extCa the paired-pulse ratio is 15% larger than at 2mM (Blatow et al. 2003). In primary hippocampal neuronal culture, inhibitory synapses also undergo a 50% increase in paired-pulse ratio at 0.5 mM compared to 2 mM extCa (Kravchenko et al. 2006).”

      They focus on PPR rather than the overall response during more sustained activation that is likely to produce more complex responses. Obviously, it would have been preferable to simply measure the responses in the appropriate external calcium.

      The reviewer correctly says that we focus on the PPR when referring to previous work which looks at how external calcium affects short-term plasticity. This was because this was the common denominator of such studies, in particular those of Blatow et al. 2003, whose work was on hippocampal CA3-CA1 synapses. Blatow et al. did have one figure panel with a 5-pulse burst but this was at 2mM and 3mM calcium, so it did not pertain to the more physiological 1.5mM case that we would need to infer what happens for bursts at physiological calcium.

      We agree that direct measurements with reduced calcium in our own preparation would have been ideal, but it was not feasible to redo the technically demanding experiments.

      (2) The illumination intensity and the effect on fiber stimulation is a limitation that will alter apparent plasticity.

      We agree that these are among the factors that affect apparent plasticity. As we state in the text, we chose settings that have previously been reported to minimize desensitization, Regarding illumination intensity, we refer to a careful calibration study by Mattis et al 2012. Based on this, we used the highest optical power available in our setup with brief pulses of 2ms or 5 ms. From the text:

      “Each presentation of a pattern was either for 2 ms (Poisson spike train experiments, Figure 6 and frequency sweeps, Figure 1-3) or 5 ms (Mismatch experiments, Figure 7 and frequency sweeps, Figure 1-3). We chose short light pulses for two reasons. First, to decrease jitter in the light-triggered CA3 neuron spike timings. Second, if one is below saturating light intensities, short pulses at higher power give more consistent spiking over multi-pulse trains (Mattis et al. 2012), Figure 2A, using a 2ms pulse width). …For all experiments, unless mentioned, the intensity of light was kept at 100%.”

      Additionally, we monitored fiber activation through field potential recordings in the CA3, and estimated the extent of its reduction over the course of a burst or train of inputs. From the text:

      “To estimate this reduction, we measured the field EPSP in the CA3 during the optical stimulation, and fitted an exponential decay function to the peaks (Figure 7-figure supplement 2). We find that the largest decay was ~30% of the initial fEPSP. The fEPSP decayed over a wide range of time-courses, with median around 800ms. We estimate that the recovery time from ChR2 desensitization was around 150ms, again highly different between slices (Figure 7-figure supplement 2). Thus the mismatch detection was largely robust to ChR2 desensitization effects over the pulse train.”

      Reviewer #3 (Public review):

      Summary:

      This work shows experimentally and computationally that single CA1 neurons can perform mismatch detection on patterned CA3 inputs and that STP and EI balance underlie this detection.

      Strengths:

      It has been known that STP can enhance the EPSP when the corresponding presynaptic input exhibits abrupt changes in firing rate. This work provides experimental evidence and further computational support for the hypothesis that the basic computation through STP is useful for detecting abrupt changes in the spatial pattern of synaptic inputs at the Schaffer collaterals. Further, their results indicate the novel view that mismatch detection is most efficient when gamma-frequency bursting inputs exhibit mismatches between theta cycles. The authors included novel results in the revised manuscript to show that the effective frequency range of gamma oscillation is broad, including both slow and fast gamma bands.

      In the initial submission, the dependence of mismatch detection performance on model parameters and experimental settings, such as pattern overlaps and other network parameters, was not sufficiently explored. In the revised manuscript, the authors extensively studied these points and summarized the novel results in Fig. 9. Furthermore, the authors clarified that jitters in input spikes can improve detection performance in some cases. These results show the robustness of their results against variations in external and internal conditions.

      Weaknesses:

      While this study shows an intriguing example of combined experimental and computational studies, the results of experiments and those of the computational model display relatively large deviations in some conditions. The cause of this discrepancy needs further clarification.

      The reviewer correctly points out that our model deviates from the experiments in some conditions. We have added a new paragraph in the discussion section to address the main points of difference:

      “As expected for a reduced model, our predictions differed quantitatively from experiments in a few respects. The strongest of these is the difference in mismatch selectivity at 50 Hz in Figure 7Fi vs 7Fiii. We speculate that this is due to one of the major simplifications in our model, the use of a single class of inhibitory interneurons. An additional point of difference is the decay time-course of EPSP vs ISI from Figure 6F. Here again we implicate the simplification with respect to interneurons. An additional likely cause is our limited use of the diversity of STP profiles in the model compared to experiment. Specifically, we used STP profiles from Figure 4-figure Supplement 1, but the population is quite diverse (Figure 4-figure supplements 1 to 4). Finally, despite our efforts to model the CA3 cell population with ChR2 desensitization constrained by experiment, we have clearly simplified the recurrence and optical illumination profiles of the CA3. Thus, at the spiking level, our stimulus patterns can only approximate physiological activity.”

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      Both external calcium and light activation are important limitations. Although I might take a different approach if it were my own paper, at this point I favor allowing the paper to proceed as long as they clearly point out these limitations.

      We have pointed out these limitations. From the text:

      “Our bath solution had 2mM Ca2+, which is above the physiological 1.2 to 1.5 mM range and hence is likely to exhibit ~20% lower STP both for inhibitory and excitatory synapses (Kravchenko et al. 2006; Blatow et al. 2003).”

      Also, from the discussion:

      “Finally, despite our efforts to model the CA3 cell population with ChR2 desensitization constrained by experiment, we have clearly simplified the recurrence and optical illumination profiles of the CA3. Thus, at the spiking level, our stimulus patterns can only approximate experiments.”

      Reviewer #3 (Recommendations for the authors):

      This reviewer has no further comments except a minor comment. The authors use the word "squares" to specify the stimulus patterns tested. On reading the revised manuscript, I could not quickly find what the " square" means. The shape of the stimuli will not be particularly important in this study. The authors may use a different word.

      We thank the reviewer for pointing out this inconsistency. At the outset we explain why we use the term ‘square’ and we have gone through the text and where necessary we have replaced the term ‘spot’ with ‘square’ or ‘illumination square’ to resolve ambiguity. At the point where we define the illumination patterns, we have added this line:

      “Due to the grid pattern of illumination and the rectangular profile of the illumination spots, we refer to them as ‘squares’ in subsequent analysis, though the exact shape is unlikely to affect the activation of CA3 neurons.”

    1. Author response:

      The following is the authors’ response to the original reviews.

      eLife Assessment

      This useful study identifies knowledge of letter shape as a distinct component of letter knowledge and shows that children acquire it even before formal reading instruction and without knowing the corresponding letter sounds. However, the evidence supporting the main conclusions is incomplete at the current stage. With additional analyses examining the relationships among the underlying variables and/or revising interpretations, the work would be of broad interest to researchers studying language and vision.

      We have now done our best to include additional analyses and interpretation to address the Reviewers’ concerns, and look forward to a more positive assessment.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      This study examines letter-shape knowledge in a large cohort of children with minimal formal reading instruction. The authors report that these children can reliably distinguish upright from inverted letters despite limited letter naming abilities. They also show a visual-search advantage for upright over inverted letters, and this advantage correlates with letter-shape familiarity. These findings suggest that specialized letter-shape representations can emerge with very limited letter-sound mapping practice.

      Thank you for your positive assessment and concise summary of our work.

      Strengths:

      This study investigates whether children can develop letter-shape knowledge independently of letter-sound mapping abilities. This question is theoretically important, especially in light of functional subdivisions within the visual word form area (VWFA), with posterior regions associated with letter/orthographic shape and anterior regions with linguistic features of orthography (Caffarra et al., 2021; Lerma-Usabiaga et al., 2018). The study also includes a large sample of children at the very beginning of formal reading instruction, thereby minimizing the influence of explicit instruction on the formation of letter-shape knowledge.

      Thank you for acknowledging the importance of this work. We agree with you that this issue is important also because letter familiarity and letter-sound association learning could drive the development of the VWFA. We now acknowledge this in the Introduction (p. 7).

      Weakness:

      A central concern is that a production task (naming) is used to index letter-name knowledge, whereas letter-shape knowledge is assessed with recognition. Production tasks impose additional demands (motor planning, articulation) and typically yield lower performance than recognition tasks (e.g., letter-sound verification). Thus, comparisons between letter-shape and letter-name knowledge are confounded by task type. The authors' partial-correlation and multiple-regression analyses linking familiarity (but not production) to the upright-search advantage are informative; however, they do not resolve the recognition-versus-production mismatch. Consequently, the current data cannot unambiguously support the claim that letter-shape representations are independent of letter-name knowledge.

      Thank you for raising this very important point. We agree with you that letter naming is not the only way to measure letter-sound knowledge, and that naming could involve production demands that are absent in other measures such as recognition. However, there is extensive literature showing that recall and recognition depend on shared mechanisms, and that performance on recall and recognition tasks is often correlated. Thus, it is unlikely that children with low naming accuracy would have high recognition accuracy. Of course, we cannot conclusively rule out the absence of letter name or recognition knowledge, and it would certainly be interesting to include additional tests of letter name knowledge in future studies. However, we do feel that our observations are important and intriguing, and will spur further research in this direction. We now acknowledge this issue in the Discussion (p. 29-30).

      Reviewer #2 (Public review):

      Summary:

      In this study, the authors propose that there are two types of letter knowledge: knowledge about letter sound and knowledge about letter shape. Based on previous studies on implicit statistical learning in adults and babies, the authors hypothesized that passive exposure to letters in the environment allows early readers to acquire knowledge of letter shapes even before knowledge of letter-sound association. Children performed a set of experiments that measures letter shape familiarity, letter-sound association performance, visual processing of letters, and a reading-related cognitive skill. The results show that even the children who have little to no knowledge of letter names are familiar with letter shapes, and that this letter shape familiarity is predictive of performance in visual processing of letters.

      Thank you for your positive assessment and concise summary of our work.

      Strengths:

      The authors' hypothesis is based on widely accepted findings in vision science that repeated exposure to certain stimuli promotes implicit learning of, for example, statistical properties of the stimuli. They used simple and well-established tasks in large-scale experiments with a special population (i.e., children). The data analysis is quite comprehensive, accounting for any alternative explanations when needed. The data support at least a part of their hypothesis that the knowledge of letter shapes is distinct from, and precedes, the knowledge of letter-sound association, and is associated with performance in visual processing of the letters. This study shed light on a rather overlooked aspect of letter knowledge, i.e., letter shapes, challenging the idea that letters are learned only through formal instruction and calling for future research on the role of passive exposure to letters in reading acquisition.

      We are happy to note that you found our study interesting.

      Weaknesses:

      Although the authors have successfully identified the knowledge of letter shapes as another type of letter knowledge other than the knowledge of letter-sound association, the question of whether it drives the subsequent reading acquisition remains largely unanswered, despite it being strongly implied in the Introduction. The authors collected a RAN score, which is known to robustly predict future reading fluency, but it did not show a significant partial correlation with familiarity accuracy (i.e., familiarity accuracy is not necessary to predict RAN score). The authors discussed that the performance in visual processing of letters might capture unique variance in reading fluency unexplained by RAN scores, but currently, this claim seems speculative.

      We totally agree with you and we have carefully reviewed our manuscript throughout to clarify that this is a speculation that follows from our findings, but remains to be proved.

      Since, even children without formal literacy instruction were highly familiar with letter shapes, it would be reasonable to assume that they had obtained the knowledge through passive exposure. However, the role of passive exposure was not directly tested in the study.

      We agree that letter shape knowledge must have come from passive print exposure. Understanding passive exposure in detail will require characterizing it in conjunction with several other important home related variables (parental educational status, parental involvement, literacy artefacts in the home, scripts in the home, adult literacy practices in the home, home tutoring, home-school linkages), and is beyond the scope of the present study. We now acknowledge these issues in the Discussion (p 32: Limitations and Future Directions).

      Given the superimposed straight lines in Figure 2, I assume the authors computed Pearson correlation coefficients. Testing the statistical significance of the Pearson correlation coefficient requires the assumption of bivariate normality (and therefore constant variance of a variable across the range of the other). According to Figure 2, this doesn't seem to be met, as the familiarity accuracy is hitting the ceiling. The ceiling effect might not be critical in Figure 2, since it tends to attenuate correlation, not inflate it. But in Figures 3 and 4, the authors' conclusion depends on the non-significant partial correlation. In fact, the authors themselves wrote that the ceiling effect might lead to a non-significant correlation even if there is an actual effect (line 404).

      Thank you for your careful reading! We have now clarified how the straight-line fit in Figure 2A was generated (line 261-263, p. 13) and now report the non-parametric Spearman correlation which is also statistically significant.

      Regarding Figures 3 and 4, the reviewer raised an important concern about whether ceiling effects might obscure meaningful relationships in the reported partial correlations. Such an issue would arise only if the relevant parameter pairs (e.g., other parameters versus upright search advantage in Figure 3, or versus RAN score in Figure 4) exhibited comparable ceiling effects. To directly address this concern and demonstrate the robustness of our findings, we have undertaken the following additional analyses:

      (1) Parameter distributions. We now include the distribution of each parameter (Supplementary Figure S1.2). This analysis shows that only two relevant measures: motor accuracy and familiarity accuracy, exhibit ceiling effects. Although upright and inverted search accuracy do approach the ceiling, our analyses use the accuracy difference, which follows an approximately normal distribution.

      (2) Scatter plot visualization. We have added scatter plots for the relevant parameter pairs (Supplementary Figure S2.1 for Figure 3 and Supplementary Figure S3.1 for Figure 4). These plots demonstrate that the data are sufficiently well distributed across the measurement range, indicating that meaningful associations would be detectable if present.

      (3) Multiple regression and mixed-effects modelling. Previously, we used multiple linear regression analyses to validate the robustness of the partial correlation results in Figure 3 (now reported in detailed under Supplementary Section S2.2). We have now extended this approach by replicating the linear regression analysis for modelling RAN scores (Supplementary Section S3.2) and by conducting mixed-effects modelling to assess the contribution of different parameters to search reaction time (Supplementary Section 2.3).

      Together, these additional analyses provide converging evidence that our results are not driven by ceiling effects or other statistical artifacts, and they reinforce the robustness of the conclusions drawn from Figures 3 and 4.

      Reviewer #3 (Public review):

      Summary:

      This study examined how young children with minimal reading instruction process letters, focusing on their familiarity with letter shapes, knowledge of letter names, and visual discrimination of upright versus inverted letters. Across four experiments, kindergarten and Grade 1 children could identify the correct orientation of letters even without knowing their names.

      Thank you for your positive assessment and concise summary of our work.

      Strengths:

      This study addresses an important research gap by examining whether children develop letter familiarity prior to formal literacy instruction and how this skill relates to reading-related cognitive abilities. By emphasizing letter familiarity alongside letter recognition, the study highlights a potentially overlooked yet important component of emergent literacy development.

      We are happy to note that you found our study to be addressing an important research gap.

      Weaknesses:

      The study's methods and results do not effectively test its stated research goals. Reading ability was not directly measured; instead, the authors inferred its relationship with reading from correlations between letter familiarity and reading-related cognitive measures, which limits the validity of their conclusions. Furthermore, the analytical approach was rather limited, relying primarily on simple and partial correlations without employing more advanced statistical methods that could better capture the underlying relationships.

      We respectfully disagree for the following reasons.

      (1) We strategically targeted early readers because it is only in early readers that we could hope to disentangle letter familiarity from letter recognition. Once a child is reading fluently, his/her letter familiarity could come from knowing the names of letters, rather than from shape familiarity alone. We could not measure reading ability directly since these children were in the early stages of learning to read, and so we have measured their RAN score instead which is a precursor for fluent reading.

      (2) We have claimed that letter familiarity could potentially boost early reading, because we have shown that it already leads to a visual processing advantage. We have acknowledged throughout that our observations are important as such, and imply (but do not prove) a potential role for letter shape familiarity in early reading.

      (3) We have now replicated all our analyses using advanced statistical techniques, which are now reported in the Supplementary Material. In general, partial correlation analyses are mathematically equivalent to multiple linear regression and generalized linear modelling, so it is unsurprising that all these analyses yield similar conclusions.

      Major Comments:

      (1) Limited Novelty and Unclear Theoretical Contribution:

      The authors aim to challenge the view that children acquire letter shape knowledge only through formal literacy instruction, but similar questions regarding letter familiarity have already been explored in previous research. The manuscript does not clearly articulate how the present study advances beyond existing findings or why examining letter familiarity specifically before formal instruction provides new theoretical insight. Moreover, if letter familiarity and letter recognition are treated as distinct constructs, the authors should better justify their differentiation and clarify the theoretical significance of focusing on familiarity as an independent component of emergent literacy.

      We respectfully disagree with this reading of the current study. We have searched through the literature on this topic once again and most studies have compared frequent versus infrequent letters or strings but have not directly tested letter familiarity as we have done. In other words, there is little in the literature on the distinction between letter familiarity and letter recognition. We have now reworked the Introduction section to highlight this conceptual distinction, drawing attention to components within the term letter knowledge: letter shape familiarity, and letter recognition, (p. 3-5). We would, however, be happy to review and contrast with prior work if you can point us to it.

      (2) Overgeneralization to Reading Ability:

      Although the study measured several literacy-related cognitive skills and examined correlations with letter familiarity, it did not directly assess children's reading ability, as participants had not yet received formal literacy instruction. Therefore, the conclusion that letter familiarity influences reading skills (e.g., Line 519: "Our results are broadly consistent with previous work that has highlighted print letter knowledge as a strong predictor of future reading skills") is not fully supported and should be clarified or revised.

      We agree that the line was ambiguous, which led this confusion. By letter knowledge, we were referring to letter recognition ability (not letter shape familiarity), which is a well-established predictor of reading ability and is also partially correlated with the RAN score in our study (Figure 4B). We have now clarified this ambiguity by changing “letter knowledge”, to “letter naming knowledge” (line 667-669 now, and other places) in the manuscript.

      To draw conclusions about the impact on reading ability, a longitudinal study would be more appropriate, assessing the relationship between letter familiarity and reading skills after children have received formal literacy instruction. If a longitudinal study is not feasible, measuring familial risk for dyslexia could provide an alternative approach to infer the potential influence of letter familiarity on later reading development.

      While assessing the impact of letter familiarity on later reading ability using a longitudinal design or familial risk is indeed valuable, this is beyond the scope of the current study. We have acknowledged this in the 'Limitations and Future Directions' section (p. 32).

      (3) Confusing and Limited Analytical Approach with Potential for More Sophisticated Modelling: The study employs a confusing analytical approach, alternating between simple correlational analyses and group-based comparisons, which may introduce circularity - for example, defining high vs. low familiarity groups partly based on performance differences in upright versus inverted letters and then observing a visual search advantage for upright letters within these groups.

      We respectfully disagree that analytical approach related to subgrouping introduces circularity. Subgroups were defined exclusively using Experiments 1 and 2, which measured letter shape familiarity and letter naming based on accuracy. Experiment 3, in contrast, is a visual search task that does not require letter shape or naming knowledge, and its primary outcome measure is search time, not accuracy. Group assignment is therefore independent of the dependent variable in Experiment 3.

      Our analyses simply test whether children who differ in letter knowledge also differ in visual search performance. This is not reported before, rather, represent the hypothesis being tested here, making the approach non-circular.

      Furthermore, we have analysed our data without dividing participants into groups (Figures 3-4) and obtained similar results.

      Moreover, the analyses are relatively simple: although multiple linear regression is mentioned, the results are not fully reported.

      We now report the result of multiple linear regression in the supplementary material (Supplementary Section S2.2, and Section S3.2), where we obtained similar results.

      These approaches may not fully capture the complex relationships among letter familiarity, recognition, visual search performance, RAN, and other covariates. More sophisticated modeling, such as mixed-effects models to account for repeated measures, structural equation modeling to examine latent constructs, or multivariate approaches jointly modeling familiarity and recognition effects, could provide a clearer understanding of the unique contribution of letter shape familiarity to early literacy outcomes.

      We thank the reviewer for this suggestion. We have now conducted mixed-effects modelling to assess the contribution of different parameters to search reaction time. These additional analyses are described in detail in “Supplementary Sections S2.3: Contributions of various factors to letter search advantage: Generalized Linear Mixed-Effects Modelling (GLME)”, and yield results fully consistent with the original partial correlation findings.

      In addition, a large number of correlations were conducted without correction for multiple comparisons, which may increase the risk of false positives and raise concerns about the reliability of some significant findings.

      We thank the reviewer for this suggestion. We now have reported the correction for multiple comparisons wherever applicable, and all our key findings remain significant.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      (1) Introduction: The authors divide print knowledge into two components: letter shape (visual familiarity) and letter name (visual-sound associations). While letter-name knowledge is widely considered important for reading acquisition, it remains unclear whether letter-shape knowledge, independent of letter name, is important for reading development (Q1) and capable of inducing a visual-processing advantage (Q2).

      While the question is worthwhile, the motivation needs tightening. The three lines of literature cited - (1) print knowledge in kindergarteners, (2) associations between reading and basic visual skills, and (3) early sensitivity to repetition/statistical regularities - do not, as currently framed, present a strong reason to study letter-shape knowledge per se.

      First, evidence from kindergarten print knowledge (Lochy et al., 2016; Maurer et al., 2005) likely includes children with at least some letter-name exposure. Indeed, the neural measures reported there were associated with letter name knowledge measured in their child participants. Likewise, the claim that children from rich home-literacy environments can distinguish words/sentences from scribbles or inverted forms (Levy et al., 2006) does not preclude informal letter-name learning at home and thus does not show that shape familiarity precedes name learning. Please also define "global print features" (L43), explain how they differ from letter-shape features, and clarify why the global features are less relevant.

      Thank you for this suggestion. We have now reworked the relevant paragraph of the Introduction to make this clearer.

      Second, the work linking reading to basic visual functions is relevant, but the manuscript should connect those findings to letter-shape familiarity specifically-i.e., make explicit why any observed visual advantage should track familiarity with letter forms (controlling for name knowledge).

      Third, the repetition/statistical-learning literature cited does not specify representational grain. Such learning may preferentially build whole-word familiarity rather than letter-level representations; many early readers know a small set of high-frequency sight words in their environment (e.g., "McDonald's") without abstracting letter shapes.

      Thank you for these suggestions. We have now revised the Introduction (p. 6) to make these points clearer.

      (2) Methods and Results:

      The Methods and Results sections are difficult to follow. The motivation and procedures for several analyses are not described explicitly or clearly, and some analyses do not address the stated questions. My detailed comments follow.

      (a) Experiments 1 & 2:

      The analyses of the "top-line" effect (corresponding to /a/) are confusing (L194-200). After computing accuracies for letters with vs. without a top line, why are correlations performed? Correlations highlight similarity, not group differences. To test whether the top line contributes to or influences performance-that is, whether it differentiates the two stimulus groups-paired comparisons or mixed-effects models should be used.

      We thank the reviewer for highlighting this. We agree that correlation indicates similarity, and it does not address the specific contribution of the top-line (matraa). We now present a detailed analysis in Supplementary Section 2.4, and also now show that the top line does not have any effect on the upright letter search advantage.

      L201: Why do the authors assume some letters are more recognizable than others? Which letters are these? The appropriate test is to compute letter-wise accuracies for the proposed subset and compare them against the remaining letters. Split-half correlations cannot answer this question. As above, correlations between letter sets do not test whether the top line influences recognition accuracy.

      Our assumption that some letters are more recognizable than others is grounded in the structure of the school curriculum, in which certain letters are introduced earlier than others. From the 18 letters used in the study, we selected 9 letters introduced early in the curriculum (ಅ, ಆ, ದ, ಗ, ಇ, ಈ, ಖ, ಒ, ರ) and 9 letters introduced later (ದು, ಜ, ಳಿ, ಲ್ಲಿ, ನ, ನಾ, ಣ, ನ್ನು, ವ).

      To directly address the reviewer’s concern, we computed recognition accuracy separately for the early- and late-introduced letter sets for each child and compared these measures. Children were significantly more accurate for early-introduced letters than for late-introduced letters (“mean ± SEM accuracy: early taught: 70.1% ± 1.9%; late taught: 38.5% ± 1.9%; p < 0.00005, rank-sum test across 285 children, who did the recognition task”, L250-258, p. 12-13). We have now included this analysis in the Results section.

      However, as multiple analyses show that recognition accuracy does not uniquely predict the upright search advantage (Main Text Figure 3B; Supplementary section S2.2, S2.3, S2.4), we did not further pursue analyses examining the differential contributions of early versus late letter recognition accuracy or included early vs late accuracy comparison result in the article.

      L218-219: How is the fitted line in Figure 2A determined? Please specify the model.

      This was done using standard linear least squares fitting. We have now updated the manuscript with these details (L261-263, p. 13).

      L221-234: It is unclear why correlations between familiarity accuracies for unrecognized letters and overall recognition accuracy rule out the alternative explanations the authors propose. Moreover, the fact that some children who can name only a few letters nevertheless achieve high letter-shape recognition does not exclude the possibility that they can generalize shape statistics from those few known letters. Please provide the full argument and supporting evidence (citations) or include analyses that directly test this generalization account.

      We thank the reviewer for this comment and agree that the logic was not sufficiently explicit in the manuscript. Our argument has two components.

      First, if letter familiarity were merely a byproduct of letter recognition, then any effect of familiarity should be subsumed by recognition. In that case, removing recognition-related variance should eliminate familiarity effects. Contrary to this prediction, across multiple analyses we find that familiarity independently predicts the search advantage, whereas recognition does not, demonstrating that familiarity cannot be reduced to recognition.

      Second, to directly test the alternative possibility that children generalize shape statistics from the few letters they recognize, we used a computational similarity analysis. Specifically, we wondered whether letter familiarity for unrecognized letters depended on their similarity to recognized letters. To this end, for each child, we identified the unrecognized letters and calculated their average dissimilarity to recognized letters using a computational model (a neural network pretrained for object categorization, VGG-16), and asked whether the familiarity accuracy varied with the average dissimilarity between the recognized and unrecognized letters. If, familiarity accuracy on unrecognized letters is coming from shape generalization from recognized ones, then the familiarity accuracy will be more, as the dissimilarity decreases, i.e. we will see a negative correlation, but we in fact obtained a weak positive correlation (Section S1.6).

      We have included the above text in the Results (L. 299-309, p. 14-15) and in the Supplementary Material (Section S1.6).

      (b) Experiment 3:

      L280-281: "Thus, the visual processing advantage for upright letters is associated more strongly with visual familiarity for letter shape than with letter recognition." This claim requires an interaction test. For example, quantify the upright advantage as the upright-minus-inverted difference and run a 2×2 analysis (Orientation: upright/inverted × Knowledge type: familiarity/recognition), or an equivalent mixed-effects model, to test main and interaction effects. To their credit, the authors already analyze the difference score and examine unique associations via partial correlations and regression; an explicit interaction/contrast would complete the argument.

      We thank the reviewer for this suggestion. We address this directly using a mixed-effects model on raw search reaction times (Supplementary section “S2.3: Contributions of various factors to letter search advantage: Generalized Linear Mixed-Effects Modelling (GLME)”). This analysis shows that familiarity significantly facilitates faster responses in the upright relative to the inverted condition, whereas recognition does not. This supports our claim that the upright advantage is more strongly linked to visual familiarity than to letter recognition.

      (c) Effects of grade and language of instruction across experiments:

      These sections largely repeat the main analyses on different subsamples/methods and confirm robustness without adding new information. Consider condensing to one sentence, noting consistency across subsamples and moving details to the Supplement. Please also provide a concise summary table of key statistics for readability. Interpretive statements should be moved to the Discussion.

      We appreciate the reviewer’s suggestion and understand the concern about redundancy. However, grade and language of instruction are primary variables in this study, as they are directly linked to instructional exposure and the testing context. For this reason, we prefer to keep these analyses in the main text rather than moving them to the Supplement, which is often accessed only by interested readers. Although these analyses confirm robustness across subsamples, we consider this evidence central to our conclusions.

      Which factors are associated with rapid automatized naming (RAN) scores?

      Please state the motivation for including the RAN analysis and explain how its results inform the central question about letter-shape knowledge and the visual advantage.

      We have now added a few lines to address this before discussing the results of the RAN task, under the heading “Which factors are associated with rapid automatized naming (RAN) scores?” (L.550-559, p. 25)

      (d) Correlations among all factors across experiments:

      The purpose of these correlations is unclear. As presented, they primarily show strong associations between familiarity and recognition (both RT and accuracy), highlighting the close relationship between letter shape and letter name. Reaction time (RT) is also introduced for the first time here; please explain why RTs are not analyzed earlier and how they complement the accuracy-based results.

      We focus on accuracy for the letter familiarity and recognition tasks because these measures assess knowledge: whether a child knows the letter, rather than speed of response. In contrast, reaction time (RT) is more informative in visual search tasks, where it reflects the efficiency with which a child can locate the target. Figure 4C is included to illustrate the relationships among all measured parameters, including RT, providing additional context for interested readers. These correlations are not central to our main hypotheses but are reported for completeness.

      (5) Discussion:

      The Discussion should center on interpreting the core findings - high letter-shape familiarity and the upright-letter advantage in minimally instructed children - by situating them within prior work, outlining plausible formation mechanisms, and identifying contributing factors. Current sections on emergent reading skills (e.g., Understanding emergent literacy; Role of additional factors in reading acquisition) extend beyond what is tested here and should be substantially reduced or reframed. Speculation is acceptable but should not dominate the interpretation; please anchor claims in the present data and prior evidence.

      We have reframed the Discussion more closely on our core findings and have reduced the section on the role of additional factors in reading acquisition, as suggested. We believe, the revised version is more firmly grounded in the present results, and we hope it will be more accessible and acceptable to readers and reviewers.

      Letter knowledge as a predictor of early reading skills:

      The discussion opens by linking letter knowledge to early reading, but this relationship is not tested in the paper. If anything, the null relation with RAN-a well-known precursor of reading-cautions against strong claims. I therefore do not agree with the statement that "Our results are broadly consistent with previous work that has highlighted print letter knowledge as a strong predictor of future reading skills,".

      This is a phrasing problem from our side, as we thank you for your careful reading of this point. By ‘letter knowledge,’ we specifically meant letter name knowledge, or letter recognition, not letter shape familiarity. We agree that the original wording was confusing, and we have clarified it accordingly: “Our finding that letter naming in RAN is predicted by letter naming knowledge is broadly consistent with previous work that has highlighted letter naming as a strong predictor of future reading skills….” (L. 668)”.

      Minor comment:

      L52-54: "For example, children with low RAN scores (an early cognitive skill related to reading, as discussed earlier), showed slower performance in basic visual tasks, such as simple reaction time and same/different decision tasks (Stainthorp et al., 2010)." RT and decision tasks are outcomes or paradigms, not visual mechanisms per se.

      We acknowledge the mistake in wording, and now have revised the text to clarify this distinction: (L.69-72) “For example, children with low RAN scores (an early cognitive skill related to reading, as discussed earlier), showed slower performance in basic visual tasks, as measured by simple reaction time and same/different decision tasks (Stainthorp et al., 2010).”

      Reviewer #2 (Recommendations for the authors):

      (1) The authors wrote that they selected 18 letters with a range of letter frequencies. Would it be possible for the authors to correlate familiarity accuracy for each letter and the frequency of each letter in Kannada? According to the authors' hypothesis of implicit learning through passive exposure, one might expect that readers are more familiar with frequent letters than the infrequent ones. It would be particularly great if the authors could measure the letter frequency in the readers' learning environments (e.g., school, children's book).

      We have now included additional analyses of letter frequencies from a children’s book corpus {Citation} in Supplementary Section S1.3. The frequency data come from The Promise Foundation Corpus of Child-Directed Print drawn from 402 books for children between 3 and 10. We find no clear association between letter familiarity and letter frequency, at least for this corpus.

      (2) Regarding the question of whether the letter shape familiarity drives the subsequent reading acquisition, can the authors perform a mediation analysis on IV: familiarity accuracy, mediator: recognition accuracy, and DV: RAN scores? The correlations between three variables (i.e., the significant correlation between familiarity accuracy and recognition accuracy, the significant partial correlation between recognition accuracy and RAN scores, and the non-significant partial correlation between familiarity accuracy and RAN scores) jointly suggest a full mediation. However, they do not guarantee a significant indirect effect of familiarity accuracy on RAN scores. The authors might even want to consider other variables, such as age or grade, as a moderator. Please note, though, I'm not suggesting that the authors should make claims about causal directions with the mediation analysis on their observation data.

      We thank the reviewer for this insightful suggestion. We performed the mediation analysis as recommended, and the results indicated full mediation: letter shape familiarity predicted recognition accuracy, which in turn predicted RAN scores, while the direct effect of familiarity on RAN was non-significant. We have now included these in the Results (p. 28: Letter-RAN associations: Could letter familiarity affect RAN score through letter recognition?).

      (3) Regarding the ceiling effect and the significance testing of correlation coefficients, at the very least, I recommend including scatter plots for key factors in Figures 3 and 4.

      We have now added distributions of all relevant parameters (Supplementary Figure S1.2), which indicate that only motor accuracy and familiarity accuracy exhibit ceiling effects. In addition, we have included scatter plots for the key parameter pairs underlying Figures 3 and 4 (Supplementary Figures S2.1, and S3.1). Finally, we report both linear regression and generalized linear mixed-effects (GLME) analyses for Figures 3 and 4 to demonstrate the robustness of our claims (Sections 2 and 3, Supplementary Material).

      (4) The letter familiarity task results are shown as either averages across readers or across letters, but not as reader-letter pairs. In the letter familiarity task, each of the 18 letters was repeated four times. Is correctness consistent across four repeats of each letter for each reader? That is, if a dot in Figure 2A says a reader has the familiarity accuracy of 75%, is that number mainly driven by the reader 1) being correct in all four repeats for 75% of 18 letters and incorrect in all four repeats for the remaining 25%, or 2) being correct in three out of four repeats for all 18 letters?

      This is an interesting question, thank you for this suggestion. To address this, we computed letter-wise accuracy values (0, 0.25, 0.5, 0.75, or 1, as there were 4 repeats/letter) for each child. We focused this analysis on 41 children whose overall familiarity accuracy did not exceed 90%, as ceiling performance precludes meaningful assessment of variability (Supplementary Section S1.1).

      This analysis shows that children with lower overall familiarity accuracy exhibit substantial variability across repetitions of the same letter, indicating inconsistent responding, whereas children with higher overall familiarity accuracy show strong internal consistency, with most letters reaching 100% accuracy across repeats (Supplementary Figure S1.1A). We now report this analysis in the Supplementary Material (supplementary section “S1.1: Internal consistency of familiarity accuracy for each child.”).

      (5) Figure 4C: Since the conclusions from Figures 3 and 4 are based on partial correlations, something similar to Figure 4C but with partial correlations might be helpful.

      We thank the reviewer for the suggestion. However, we did not have a specific hypothesis motivating a partial correlation for Figure 4C. The correlations presented here are across all parameters measured in our study, and are included primarily for completeness and to allow inquisitive readers to explore potential relationships.

      (6) Figures 2D-G are bar plots, but the y-axis starts at 2. I suggest the authors break both the y-axis and the bars to more explicitly prevent readers from misinterpreting the relative differences among the four plots, or alternatively use violin plots.

      While we appreciate the point, we consider it a minor issue and believe that the current presentation of Figures 2D–G conveys the data clearly. Therefore, we prefer to keep the plots as they are.

      (7) Figures 2 and S1: By eyeballing, there seem to be ~120 data points in Figure 2A, suggesting that some data points are overlapping, probably because there are only 19 levels of recognition accuracy, and familiarity accuracy is hitting the ceiling. Figure S1 suffers even more from the same visualization issue. I think the authors can try using the size or transparency of markers to indicate overlapping data points in Figure S1, but I'm not sure whether it would work for Figure 2 as well.

      We have now added transparency to the markers in Figure S1 (now Supplementary S1.5) to better indicate overlapping data points. For Figure 2, however, applying transparency did not improve the visualization, so we have retained the original presentation.

      (8) Figure 2 caption: "high/low familiarity (cyan/blue) x high/low recognition (orange/red)" is not an accurate description of the color coding.

      Apologies for this confusion. We have now clarified in the revised text (p. 17, L355-359).

      Reviewer #3 (Recommendations for the authors):

      (1) Line 35: The statement 'a tacit assumption made by most studies is that letter knowledge is taken as the ability to explicitly name or recognize letters' requires supporting references.

      We thank the reviewer for this suggestion. We have now included relevant references: L.48-50: “A tacit assumption made by most studies is that letter knowledge is the ability to explicitly name or recognize letters (Muter et al., 2004; Noel Foulin, 2005; Sigmundsson et al., 2020; Stephenson et al., 2008)”.

      (2) Line 39: Similarly, the claim 'children only become familiar with letter shapes once they start learning letter names' should be supported by prior literature.

      We would like to respectfully note that the reviewer appears to have focused on an incomplete line, which may have caused some confusion. As described in the text, this is an assumption rather than a well-established claim, and it is exactly what we aim to test in our study.

      (3) Lines 38-42: The logical connection between the sentences is unclear. If the authors want to emphasize that children from rich home literacy environments HLE can distinguish letters from non-letters before formal literacy instruction, this should be made clearer.

      We apologize for any confusion. Here, our intent was simply to highlight that children can become familiar with written forms, even before formal reading instruction. The reference to a rich home literacy environment (HLE) is related to the cited paper and not a claim we are making in our study.

      (4) The distinction between Lower and Upper Kindergarten is unclear, as the age ranges are similar, and the LKG group may even have a higher mean age. The criteria for this grouping should be clarified.

      The distinction between Lower and Upper Kindergarten (LKG and UKG) is based solely on the class in which the children were enrolled during data collection. In India, schooling typically consists of LKG, UKG, and then first grade. Placement criteria can vary slightly across schools (resulting overlapping age range across LKG and UKG), and we have not examined these school-specific differences.

      (5) In Experiment 3, a Wilcoxon signed-rank test was used to compare upright vs. inverted letters. It is unclear whether the data were tested for normality to justify using a non-parametric test rather than a paired t-test. The rationale for choosing a non-parametric test should be provided.

      This is a valid concern, as our reasoning was not explicitly stated. We consistently tested all parameters for normality, and whenever one or both parameters failed, we applied a non-parametric test. We have now added the following clarification to the Methods section: “While reporting comparison results, we always tested parameter pairs for normality first, and applied non-parametric alternative to t-tests whenever even one parameter failed normality testing.” (L.791-793)

      (6) Lines 324-325 mention a baseline motor task measuring speed and accuracy, but the manuscript does not describe when or how it was administered, what stimuli were used, or whether it was part of the main experiment or separate. This information is necessary to interpret the correlation analysis in Figure 3.

      We thank the reviewer for pointing this out. Now we have added details of the motor task in the method section: “At the beginning, to estimate motor speed…”(L:867).

      (7) The distributions of task scores for kindergarten and Grade 1 children are not provided. This is particularly important when discussing potential ceiling effects.

      We have now included distributions across all children in the Section S1.2, but we did not feel that it was useful to separate them into groups.

      (8) Line 548 mentions 'components of emergent literacy evolve over time.' It is unclear whether this refers to the developmental stages of children or the evolution of the theoretical concept.

      We agree that the original sentence was ambiguous. We have now rewritten this section such that, this phrase does not exist anymore.

      References

      Caffarra, S., Karipidis, I. I., Yablonski, M., & Yeatman, J. D. (2021). Anatomy and physiology of word-selective visual cortex: From visual features to lexical processing. Brain Structure and Function, 226(9), 3051–3065. https://doi.org/10.1007/s00429-021-02384-8

      Lerma-Usabiaga, G., Carreiras, M., & Paz-Alonso, P. M. (2018). Converging evidence for functional and structural segregation within the left ventral occipitotemporal cortex in reading. Proceedings of the National Academy of Sciences, 115(42), E9981–E9990. https://doi.org/10.1073/pnas.1803003115

      Levy, B. A., Gong, Z., Hessels, S., Evans, M. A., & Jared, D. (2006). Understanding print: Early reading development and the contributions of home literacy experiences. Journal of Experimental Child Psychology, 93(1), 63–93. https://doi.org/10.1016/j.jecp.2005.07.003

      Lochy, A., Van Reybroeck, M., & Rossion, B. (2016). Left cortical specialization for visual letter strings predicts rudimentary knowledge of letter-sound association in preschoolers. Proceedings of the National Academy of Sciences, 113(30), 8544–8549. https://doi.org/10.1073/pnas.1520366113

      Maurer, U., Brem, S., Bucher, K., & Brandeis, D. (2005). Emerging Neurophysiological Specialization for Letter Strings. Journal of Cognitive Neuroscience, 17(10), 1532–1552. https://doi.org/10.1162/089892905774597218

      Muter, V., Hulme, C., Snowling, M. J., & Stevenson, J. (2004). Phonemes, Rimes, Vocabulary, and Grammatical Skills as Foundations of Early Reading Development: Evidence From a Longitudinal Study. Developmental Psychology, 40(5), 665–681. https://doi.org/10.1037/0012-1649.40.5.665

      Nag, S., John, S., & Agrawal, A. (2024). NSP-SCD: A corpus construction protocol for child-directed print in understudied languages. Behavior Research Methods, 56(4), 2751–2764. https://doi.org/10.3758/s13428-024-02339-x

      Noel Foulin, J. (2005). Why is letter-name knowledge such a good predictor of learning to read? Reading and Writing, 18(2), 129–155. https://doi.org/10.1007/s11145-004-5892-2

      Sigmundsson, H., Haga, M., Ofteland, G. S., & Solstad, T. (2020). Breaking the reading code: Letter knowledge when children break the reading code the first year in school. New Ideas in Psychology, 57, 100756. https://doi.org/10.1016/j.newideapsych.2019.100756

      Stainthorp, R., Stuart, M., Powell, D., Quinlan, P., & Garwood, H. (2010). Visual Processing Deficits in Children With Slow RAN Performance. Scientific Studies of Reading, 14(3), 266–292. https://doi.org/10.1080/10888431003724070

      Stephenson, K. A., Parrila, R. K., Georgiou, G. K., & Kirby, J. R. (2008). Effects of Home Literacy, Parents’ Beliefs, and Children’s Task-Focused Behavior on Emergent Literacy and Word Reading Skills. Scientific Studies of Reading, 12(1), 24–50. https://doi.org/10.1080/10888430701746864

    1. Author response:

      The following is the authors’ response to the previous reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      This article presents a study consisting of two experiments, which aim to dissociate and quantify the distinct motivational functions of phasic and tonic pain within a naturalistic and immersive VR setting. Specifically, the Authors test two hypotheses: (i) that phasic pain acts as a punishment signal that drives avoidance learning; (ii) that tonic pain reduces motivational vigor, promoting energy conservation and recuperation. In both experiments, participants performed a free operant foraging task, where they collected virtual pineapples to earn points.

      In Experiment 1, phasic pain was delivered as a brief electric shock to the grasping hand when picking up green pineapples. As phasic pain intensity increased, participants were less likely to choose painful fruits. A reinforcement learning model that incorporated reward, pain cost and effort cost was able to successfully capture behavior.

      Experiment 2 combined effects of phasic and tonic pain. Tonic pain was induced by a pressure cuff on the non-dominant arm, simulating sustained discomfort. Interestingly, tonic pain did not affect the perceived intensity or avoidance of phasic pain. However, it significantly reduced movement velocity and pineapple collection rate, interpreted as a reduction of motivational vigor. A temporal decision model incorporating vigor cost successfully captured these effects.

      Concomitant EEG recordings showed that tonic pain was associated with reduced alpha and beta power in parietal and temporal areas. Phasic pain ratings and decision values distinctively correlated with skin conductance responses.

      Overall, these findings indicate that phasic and tonic pain have distinct and dissociable motivational effects.

      Strengths:

      This is an ambitious study that provides a quantitative dissociation of the roles of phasic and tonic pain in adaptive behavior, by integrating ecological neuroscience, motivational theory, and computational modeling. The use of immersive VR combined with a free-operant foraging task offers a more ecologically valid context to study pain-related behavior compared to traditional paradigms. Furthermore, the study employs a multimodal approach by combining behavioral data, computational frameworks, physiological signals and EEG. In particular, one of the main strengths of the study is the use of sophisticated computational modeling to capture phasic and tonic pain effects. The experiment codes are available on GitHub, increasing reproducibility.

      Weaknesses:

      As recognized by the Authors, there is no control condition involving an innocuous salient stimulus to rule out non-specific effects of distraction.

      We thank the reviewer for their positive assessment of the study and for highlighting this remaining limitation. We acknowledge that, without an innocuous salient control condition, a nonspecific contribution of distraction cannot be ruled out. The Discussion retains this limitation and considers such a comparison as a direction for future work.

      Reviewer #2 (Public review):

      Summary:

      The study investigated the distinct roles of phasic and tonic pain in adaptive behavior. Phasic pain was proposed to function as a teaching signal, promoting avoidance of further injury, while tonic pain was hypothesized to support recuperative behavior by reducing motivational vigor. This hypothesis was tested using an immersive virtual reality (VR) EEG foraging task, in which participants harvested fruit in a forest environment. Some fruits triggered brief phasic pain to the grasping hand, which in turn reduced the likelihood of choosing those fruits. Concurrently, tonic pressure pain applied to the contralateral upper arm was associated with reduced action velocities. The authors employed a free-operant computational framework to quantify how phasic and tonic pain modulate motivational vigor and decision value. Importantly, model parameters were found to correlate with EEG responses, providing neurophysiological support for the hypothesized functional distinctions.

      Comments on revised version.

      All my comments have been well addressed.

      We thank the reviewer for reviewing the revised manuscript and for confirming that their comments have been addressed.

      Reviewer #3 (Public review):

      Summary:

      This study investigates how phasic and tonic pain modulate behaviour in a free-operant foraging paradigm. The authors apply a computational modeling approach to the behavioural data to quantify the decision value of phasic pain, as well as the degree to which tonic pain reduces motivational vigour. EEG assessments showed, e.g., reduced signal power at alpha and beta frequencies in tonic pain conditions compared to no-tonic-pain conditions, but no association between these neural measures and motivational vigour. The authors conclude that tonic and phasic pain serve different motivational functions, with phasic pain acting as a punishment signal promoting avoidance and tonic pain reducing motivational vigour.

      Strengths:

      The experimental paradigm is highly innovative. Assessing human behaviour in a naturalistic yet highly controlled setting represents a promising approach to pain research. Notably, assessing pain magnitude implicitly, via its motivational value, offers insights about the overall pain experience that are not usually accessible via common pain ratings.

      We thank the reviewer for their assessment of the paradigm and its potential to complement conventional pain ratings. We also appreciate their further recommendations, which we address individually below.

      Recommendations for the authors:

      Reviewer #3 (Recommendations for the authors):

      Overall, the manuscript has improved substantially and is now considerably clearer.

      The following comments refer to the numbering of my previous review comments:

      (2) If C_m is a unit vector with components h and v, these components are necessarily interdependent and therefore should not be treated or presented as independent variables.

      We agree that these components are interdependent. We have corrected and clarified the description of the implemented parameter constraints. In Experiment 1, the fitted movement coefficient vector is normalised jointly with the pain coefficient, such that |C_p|+sqrt(h^2+v^2)=1; describing C_m itself as a unit vector in this experiment was therefore inaccurate. This constraint fixes an otherwise arbitrary common scale: multiplying C_p and C_m by the same positive constant leaves the predicted choices unchanged. We have corrected the definition and distinguished the searched parameters from the derived coefficient C_p in the Experiment 1 model-properties table.

      Experiment 2 uses a different parameterisation: C_m is a non-negative unit vector, with h fitted and v=sqrt(1-h^2) derived. The separate vigour coefficient C_v scales the movement cost, and unit length removes the redundant scale between C_m and C_v. The average reward parameter 𝑅̅ is fixed at 1 during fitting to set the overall value scale, with C_p and C_v fitted separately. We have made these constraints explicit in the Experiment 2 model properties table and corrected its list of fitted parameters so that h and v are not presented as separately fitted parameters.

      We apologise for the inaccurate description in the previous version of the manuscript and thank the reviewer for helping us identify and correct this issue.

      Regarding possible concerns on statistical results involving these interdependent variables: The comparison in panel D of the Experiment 1 behaviour and modelling figure uses a two-sided paired t-test, equivalent to a one-sample test of each participant's difference h-v against zero. It does not require independence between the two components within a participant: the independent units are the participant-level differences. Following the eye-tracking exclusions described below, 20 participants contribute one difference each, giving 20-1=19 degrees of freedom. The within-participant normalisation constraint does not require a further reduction in these degrees of freedom.

      We have revised the panel D caption to identify the paired test and the contrast h-v explicitly. After the eye-tracking exclusions, the updated result is t(19)=6.37, p<.001, compared with t(23)=6.72, p<.001 in the reviewed version. The qualitative conclusion remains: the fitted penalty is greater for vertical than horizontal movement.

      (5) It is still not full clear to me, what the SCR analysis adds. The central argument appears to be that the relationship between decision values, pain ratings, and SCRs varies across contexts (e.g., target fixation versus painful stimulation), and that SCRs therefore capture distinct aspects of the pain experience. However, this interpretation seems to assume that SCRs measured in different contexts are established markers of separable dimensions of pain experience, which I do not find sufficiently justified.

      We have revised the manuscript to distinguish the motivation for the SCR analysis, what the present evidence establishes, and the direction it motivates for further investigation. Our original question remains: what does a pain decision value estimated from choices capture about pain, and how does it relate to subjective ratings? Their correlation does not resolve whether they reflect the same aspects of pain's aversiveness or whether choice-derived values provide additional information. We introduced SCRs as a complementary physiological measurement through which to investigate this question. This rationale is now stated explicitly at the beginning of the revised SCR Results subsection, “Skin conductance responses and the interpretation of pain decision values”.

      The two event contexts were chosen because of their roles in the task. Fixation on pain-associated fruit can accompany evaluation of an anticipated cost, whereas shock delivery accompanies receiving the painful stimulus. Comparing physiological associations at these stages offers a way to investigate the relationship between prospective valuation and subsequent pain experience. We agree that event timing alone does not establish either SCR response as a selective marker of a separate dimension of pain. Establishing whether these physiological responses can distinguish aspects captured by ratings and decision values is an empirical objective of this line of research.

      The revised analyses do not resolve that distinction. The shock–rating association was the only association consistently supported across both experiments by the primary analysis and both sensitivity specifications. Associations involving decision values provided a less consistent pattern. We have therefore removed the double-dissociation interpretation that was added in the previous version and clarified that separate significance tests do not demonstrate differences between associations; inconclusive findings likewise do not establish equivalence between ratings and decision values. The accompanying timing, eye-tracking and SCR-estimation changes are described under Additional Changes below.

      These findings refine the next question without removing the original motivation. The revised Discussion advocates combining subjective reports, choice-based models and physiological measurements to quantify where these measures converge and where they may capture distinct aspects of pain's aversiveness. In our view, future work should directly test differences between their associations and establish the functional interpretation of the physiological responses. We have revised the Results, Methods, figure caption and Discussion to make this progression from rationale, through current evidence, to future investigation explicit.

      (8) I think the manuscript should state more explicitly that the assumption that "motivational vigour in a free-operant task can be quantified through an RL framework" is, in fact, a modelling assumption. While this is an interesting and promising approach, the interpretation of the model parameters depends critically on the validity and adequacy of the underlying model.

      We agree that the modelling assumption should be explicit. Our aim is to provide a quantitative operationalisation of motivational vigour within a framework relating choices to movement costs and the opportunity cost of time. Movement speed and collection rate describe the behavioural expression of effort and pace, whereas C_v quantifies the weighting of vigour-related movement costs in the choice model. The model gives this quantity a precise mathematical role; interpreting it in motivational terms depends on the validity and adequacy of the framework for the task. We have revised the Discussion to explain this rationale and make that dependence explicit.

      The Discussion now states: “We use motivational vigour here for the regulation of effort and pace in goal-directed behaviour, informed by accounts of competing motivations in pain (Fields, 2006). Movement speed and collection rate describe its behavioural expression, while the fitted C_v provides a choice-based operationalisation of vigour-related movement costs. Its motivational interpretation is a modelling assumption that depends on the validity and adequacy of the model; neither approach uniquely identifies motivation.”

      We have also examined how well the observed choices constrain this operationalisation. The new fit profiles show that different parameter combinations attain the same minimum prediction error. Within the searched grid, equally optimal fits permit mean tonic-minus-no-tonic C_v contrasts from −4.48 to +31.74, showing that the fitted contrast, including its direction, depends on selection among optima. These are sensitivity bounds, not confidence limits. We retain the first encountered joint minimum as a reproducible reporting convention with a heuristic rationale that C_v estimated from choice trade-off is often bounded below rather than above in this foraging paradigm, and explicitly disclose its limitations in the Results.

      This analysis motivates further work on both the estimation of model-based vigour and its relationship to behavioural measures. The revised Discussion proposes richer choice sets to constrain individual C_v estimates more closely, while recognising the additional search, memory and planning demands such tasks may introduce. The objective is to strengthen quantitative tests of how pain regulates effort and pace, and to establish how different operationalisations contribute to that understanding.

      Additional changes made to the manuscript

      Eye tracking data issue

      We identified an acquisition failure in which an asynchronous eye-tracking callback stopped updating, while Unity continued ray casting with stale gaze data marked as valid. Four participants per experiment were excluded from eye-dependent analyses when an identical gaze-direction vector occurred in more than 100 frames (not necessarily consecutive) within any analysed 60-s block, leaving 20 and 27 participants, respectively, before any further analysis-specific quality exclusions. Independent Experiment 2 analyses of ratings, choice probability, whole-block hand speed and collection rate retain 31 participants; the fixation-selected reaching-trajectory analysis uses 27. The main manuscript now declares the eye-tracking exclusions. The new supplementary section, “Eye tracking methods and generation attempt”, details acquisition and quality control, exploratory HAGI gaze generation, and replay limitations. Generated data were not used to reinstate excluded participants.

      SCR and EEG clock synchronisation

      We added affine clock corrections to improve the alignment of SCR and EEG recordings with task events. The Methods now refer readers to the new supplementary section, “Clock synchronisation”, for the procedures, diagnostic figures and limitations.

      SCR estimation and sensitivity analyses

      Alongside the clock-synchronisation corrections and eye-tracking exclusions, we revised the SCR analyses to retain eligible block-level coefficients irrespective of their first-level statistical significance. A nonsignificant coefficient remains an uncertain estimate; selecting coefficients according to their significance can distort subsequent association analyses. The primary analysis therefore includes these estimates without significance-based selection. Supplementary inverse-variance models using metafor and brms incorporate differences in coefficient-estimation precision using heteroskedasticity- and autocorrelation-consistent (HAC) sampling variances, while allowing participant variation and additional block-level heterogeneity. These analyses assess whether the conclusions depend on how estimation uncertainty is handled. The specifications and results for both experiments are reported in the new supplementary section, “Skin conductance sensitivity analyses”.

      Uncorrelated random effects model

      We have clarified in the Methods (“Statistical Analysis”) that, when singular fits occurred within an analysis block, we used a no-correlation structure for the entire block of analysis, including otherwise nonsingular fits, while retaining all subject-level intercepts and random slopes included in the original specification. This applies to SCR models, EEG channel-wise fits and permutation batches. The supplementary “Linear mixed model outputs” section now includes “Maximal and no-correlation fits”, comparing the choice-distance and SCR analyses on identical observations and reporting slopes, confidence intervals, test statistics and singularity classifications for both specifications.

      Cluster permutation tests

      We added cluster-based permutation tests to the main manuscript alongside the existing electrode-wise Bonferroni correction and updated the channel-wise EEG results following the analysis revisions. The tonic-pain alpha cluster survives cluster correction (p=.006), although none of its individual electrodes survives Bonferroni correction. The beta association does not survive cluster correction. For fitted vigour constants, the alpha association at Pz survives Bonferroni correction (p=.042) but does not reach the cluster-corrected threshold (p=.059). The Results and Discussion now distinguish these outcomes and present the neural associations cautiously, without treating them as uniquely identifying a motivational mechanism.

      Event-related and induced responses to phasic pain

      In the previous version, the analysis labelled as induced oscillatory responses calculated total event-related power without subtracting the evoked response. We have revised the supplementary section to present both total-power results and induced-power estimates obtained by subtracting each participant’s condition-specific ERP before time–frequency analysis. The induced high–low phasic pain contrast was significant without tonic pain (cluster p = .0001) but not with tonic pain (smallest cluster p = .1925). Direct comparisons between tonic conditions were nonsignificant. We additionally tested the tonic-by-phasic intensity interaction on the baseline-normalised log-power scale; no significant clusters were identified for either total power (smallest cluster-level p = .8382) or induced power (smallest cluster-level p = .1575).

      Interpretation is limited by unequal and sometimes sparse high-pain trial counts (3–49; mean 15.48, sample SD 10.06 across 62 participant-by-tonic-condition counts from 31 participants). The free-operant design allowed participants to avoid high-pain outcomes, and ERP estimates based on few trials may retain non-phase-locked activity and noise, limiting the separation of evoked and induced activity. We have added the following paragraph to the main-text Discussion:

      “It is worth noting that, while we found no clear behavioural or ERP evidence that tonic pain modulated phasic pain responses, this does not establish that phasic pain processing is independent of tonic pain. Supplementary analyses identified a significant high-low phasic pain contrast in induced power without tonic pain but not with tonic pain; however, direct interaction tests were non-significant for both total event-related and induced power. These findings warrant caution because the free-operant task allowed participants to avoid high-pain outcomes, leaving limited and unequal high-pain trial counts. The subtracted ERP estimate may therefore retain non-phase-locked activity and noise, limiting the separation of evoked and induced activity.”

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      This study addresses a fundamental question in cognitive neuroscience regarding how the brain transitions from a reactive state of following external instructions to a proactive state of self-directed agency. The authors utilize an ambitious multimodal design by combining the spatial precision of fMRI with the temporal resolution of EEG across two independent datasets from the University of Florida and UC Davis. By applying multivariate pattern analysis, the work demonstrates that while both instructed and willed attention engage the Dorsal Attention Network, willed choices uniquely recruit a frontoparietal decision network including the dACC and anterior insula. Furthermore, the study shows that pre-cue alpha oscillations can predict subsequent spontaneous choices. This provides a neural link between pre-existing brain states and intentional action, representing a significant technical effort to characterize the neural scaffolding of internal goal generation.

      Thank you for the succinct summary of our work.

      Strengths:

      The primary strengths of this work include the integration of fMRI and EEG which allows the authors to bridge the gap between slow metabolic signals and fast oscillatory brain states. The use of two independent cohorts is a commendable effort to ensure the reproducibility of the willed attention effect, which is often a concern in small-sample neuroimaging studies. Additionally, the move beyond univariate activation toward information-based mapping demonstrates that the identified networks actually contain specific information about the direction of attention.

      Thank you for the positive assessment of our work.

      Weaknesses:

      (1) However, several critical weaknesses must be addressed to support the fundamental claims made in the manuscript. There are significant behavioral differences in performance between the two sites, specifically regarding the UC Davis cohort exhibiting slower reaction times and lower accuracy compared to the UF group. These discrepancies suggest potential differences in subject populations or experimental environments that are not currently accounted for in the neural models. The fMRI analysis lacks temporal precision because the use of beta series regression collapses the complex BOLD response into a single estimate per trial. This loss of temporal information obscures the evolution of the decision process and makes it difficult to distinguish whether the identified patterns represent a truly spontaneous choice or a slow-building, pre-planned strategy.

      The reviewer is correct to point out the quantitative differences in behavioral performance between the UF and UCD cohorts, with the UCD participants exhibiting slower reaction times and somewhat lower accuracy despite the use of the same willed‑attention paradigm and matched stimulus parameters. The exact source of these differences is not fully known, but one likely contributor is that at UF, EEG and fMRI were recorded simultaneously in a single session, whereas at UCD, EEG and fMRI were acquired in separate sessions, which may have affected overall task engagement and fatigue. To address this concern in our analyses, we (i) first examined each dataset separately, showing that the main qualitative findings (choice‑cue activation of the frontoparietal decision network, decoding of choice in frontoparietal regions, and precue alpha predictability of willed choices) replicate across sites, and (ii) then combined datasets only at a higher level (using meta‑analytic/summary‑statistic approaches) to increase statistical power while respecting site‑specific differences. We note the behavioral differences and emphasize the analysis strategy in the revised manuscript.

      Regarding the temporal precision of the fMRI analysis, we agree that single‑trial beta estimates do not allow us to track the evolution of the decision process on a sub‑second timescale and thus cannot, by themselves, distinguish a truly spontaneous choice from a slowly developing pre‑planned strategy. Our fMRI analyses were designed to identify where willed versus instructed attention engage distinct control networks and encode decision‑relevant information, rather than to resolve the precise timing of decision formation. The temporal aspects of the decision process in this paradigm have been addressed in prior work using EEG (Rajan et al., 2018). In that study, we found that frontal theta oscillations serve as an index of decision‑making: for choice trials, a burst of frontal theta power emerged between approximately 400 and 800 ms after the cue, a pattern that was not present in instructed trials. In addition, using the onset of posterior alpha lateralization as a marker of attentional set implementation, we showed that in choice trials the deployment of the posterior attention set was delayed by about 400–500 ms relative to instructed trials. Together, these EEG findings suggest that the decision process takes place in the time period of 400 to 800 ms after the choice cue and the duration of the process is in the neighborhood of 400–500 ms, supporting the view that the decision about where to attend are formed during the cue–target interval, rather than being fully pre‑planned well in advance. We now discuss the temporal dynamics more explicitly in the revised manuscript.

      (2) Furthermore, the EEG decoding approach utilized the entire topography of electrodes rather than a biologically motivated posterior region of interest. Given that alpha-mediated spatial attention is traditionally localized to parieto-occipital sensors, using the full electrode set risks the inclusion of non-neural artefacts such as microsaccades or muscle activity which can contaminate multivariate classifiers. The introduction of the neural efficiency metric also requires further validation as the current ratio is mathematically sensitive to small denominators in the BOLD contrast.

      The reviewer’s point about the decoding topography is well taken. To assess whether our results depend on using the full electrode set, we re-ran the precue alpha decoding using only posterior parieto‑occipital electrodes (posterior ROI) and, separately, using only frontal electrodes (frontal ROI). In Figure A1, all three analyses (whole‑head, posterior‑only, and frontal‑only) yielded a similar pattern: for choice trials, decoding accuracies were reliably above chance, whereas for instructed trials, decoding accuracies remained at chance. Thus, the key qualitative effect does not depend on including non‑posterior channels.

      We chose the whole‑topography approach because our question concerned distributed alpha patterns rather than strictly local effects. In particular, frontal structures such as dACC and DLPFC are known to monitor internal brain states and interact with posterior attention networks, making it plausible that both posterior and frontal channels can contribute to decoding the upcoming decision about where to attend. At the same time, we agree that artefacts are a concern in multivariate EEG analyses. In the present case, the decoding window is strictly precue. Given that instructed and choice trials are interleaved and subjected to identical preprocessing and artefact rejection procedures, it is unlikely that systematic differences in eye or muscle artefacts drive the choice‑specific decoding. We now report the posterior‑only and frontal‑only decoding results in the Supplementary Materials and comment on the result in the revised manuscript.

      Regarding the neural efficiency metric, we agree that ratio measures can, in principle, be sensitive to small denominators. In the present data, the BOLD contrasts used in the denominator are significantly different from zero at the group level, and we interpret the neural efficiency metric as a descriptive summary of the relationship between decoding and BOLD responses rather than as a standalone biomarker. We now explicitly note this potential sensitivity and limitation in the revised manuscript.

      (3) Crucially, the manuscript does not address the physiological implications of recruiting additional frontoparietal networks when behavioral performance remains identical across conditions. The activation of the anterior insula and dACC is frequently associated with increased autonomic arousal and effort. If the willed condition requires more extensive neural scaffolding to reach the same behavioral output as the instructed condition, it raises the question of whether this internal decision process is accompanied by changes in arousal levels. The authors should consider whether the lack of a behavioral tax is due to a compensatory increase in arousal, which could be reflected in the EEG data or pupil diameter if recorded, and potentially also in the amplitude of BOLD activity, which is being masked by the neural efficiency metric. Without an account of how the brain balances this increased computational demand without impacting behavioral performance, the functional significance of the willed attention network remains partially obscured.

      We thank the reviewer for this comment, which prompted us to examine the behavioral and physiological data more closely for evidence of a compensatory arousal or effort mechanism.

      Regarding behavior, Table 1 shows that choice trials are associated with longer reaction times but higher accuracy relative to matched instructed trials (choose-left vs. cue-left, choose-right vs. cue-right). These effects were not consistently significant across both measures and both sites (UF: RT p = .438, accuracy p = .012; UCD: RT p = .830, accuracy p = .292), so we interpret this pattern cautiously rather than as a fully established effect. Nonetheless, the direction of the pattern—slower but more accurate responses on choice trials—is consistent with a speed–accuracy trade-off associated with increased cognitive control, rather than with a straightforward behavioral cost of engaging the willed attention network. This supports the interpretation that additional recruitment of anterior insula and dACC may reflect increased effortful control that helps offset, rather than degrade, task performance.

      Regarding physiological arousal more directly, pupillometry was not recorded in this study, so we cannot speak to pupil-based arousal measures. However, following the reviewer's suggestion, we examined the time course of occipital alpha power (averaged across O1, O2, and Oz, using 500-ms sliding windows in 20-ms steps, expressed as dB change from pre-cue baseline) as an EEG-based index of attentional/arousal-related engagement. In Figure A2, alpha suppression 600–1200 ms after cue onset was significantly stronger for choice trials than instructed trials in the UF dataset (p = .030), with a difference in the same direction, though not statistically significant, in the UCD dataset (p = .163). Stronger alpha suppression is generally taken to reflect greater cortical engagement/arousal, so this pattern is broadly consistent with the idea that willed attention trials involve a heightened engagement state relative to instructed trials.

      Together, these behavioral and EEG results provide converging, though not uniformly robust, evidence that the additional frontoparietal (and salience network) recruitment associated with willed attention may be accompanied by a compensatory increase in effort/arousal-related engagement, which could help explain why behavioral performance is not impaired—and if anything trends toward improved accuracy—in the choice condition. We now include Figure A2 in the Supplementary Materials and note that direct physiological arousal measures (e.g., pupillometry) were not available in the present dataset and would be a valuable addition in future work directly designed to test this hypothesis.

      Reviewer #2 (Public review):

      Summary:

      This manuscript combines fMRI and EEG investigations performed at two research sites to examine 'willed' or volitional visuospatial attention, as contrasted with more standard cued (or 'instructed') visuospatial attention. The primary findings are: 1) willed attention (vs. instructed attention) drives additional cortical circuitry across a broad fronto-parietal network; 2) the direction of willed attention, but not instructed attention can be decoded from the pre-cue EEG data and from MVPA analysis of the trial-level fMRI data; and 3) the subjects with high EEG decoding also exhibited high neural efficiency (i.e., high decoding with low BOLD signal change) in the fMRI data. The methods and data analysis are generally sound, and these results appear solid. On the negative side, it is not made clear how the present findings extend our understanding beyond prior published work from one of the senior authors. There are also three significant concerns regarding interpretation of the findings. One has to do with the causal interpretation of the pre-cue alpha EEG signal determining the direction of willed attention. The second concern is the degree to which the present research paradigm adequately examines 'willed attention.' The third is that the MVPA analysis is not sufficiently described, and Permutation testing needs to be done to validate these findings. Otherwise, this manuscript appears methodologically sound, but questions about interpretation may mute the potential impact.

      Thank you for the succinct summary of our work. We address the concerns below.

      Strengths:

      The focus on willed attention attempts to move beyond some of the many limitations of standard laboratory investigations of attention.

      The shared paradigm across two modalities and two research sites demonstrates solid reproducibility, even though a few minor differences are observed across sites.

      Thank you for the positive assessment of our work.

      Weaknesses:

      (1) There are concerns about this experimental paradigm carrying the banner of Willed Attention, because the application of 'Will' appears quite modest. Yes, extra brain activity is exhibited for this condition vs. its control, but do the cognitive processes isolated adequately stand in for 'Willed Attention?" Willed attention, as operationally defined here, appears to involve a simple decision process prior to the shifting of spatial attention. The cue is internally generated, but after that the rest of the attentional processes appear identical to standard externally cued visuospatial attention experiments. This self-generated cue process likely involves some sort of memory/history of the recently selected cues and then some randomish selection between A and B. This appears very similar to asking the subject to guess whether a fair coin flip will be heads or tails on each trial. A mental 'coin flip' feels like a very weak version of 'will.' As a potential remedy, it would be helpful to discuss what other phenomena might fall within 'willed attention' and what some future studies might choose to focus on, along with some potential pitfalls (e.g., the reasons why the current study avoided more robust exemplars of will).

      Thank you for this thoughtful comment about the implications of “willed attention” as instantiated in our paradigm. Our use of the term follows earlier work in this line of research, where attention that is endogenously directed in the absence of external attention‑directing cues has been referred to as “willed attention” (Bengson et al., 2014, 2015; Liu et al., 2017; Rajan et al., 2018; see also Nadra et al., 2023, for review). In these studies, and in the present work, participants are prompted to decide for themselves where to attend (left vs right) when a choice cue appears, rather than being instructed where to attend by an external cue.

      We agree that, viewed from a broader perspective on “will,” this is a modest instantiation. The choice component can be described as a simple internally generated decision between two alternatives, and we do not claim that it captures the full richness of everyday volitional attention (e.g., spontaneously deciding what to attend, when to shift, or sustaining attention over longer time scales). Our aim here was to isolate, under tightly controlled conditions, the additional control processes that are engaged when the direction of spatial attention is chosen endogenously rather than specified by an external cue. The evidence we present— that the choice cue recruits a frontoparietal decision network, that choice direction can be decoded from this network only in choice trials, and that ongoing alpha patterns bias upcoming choices—speaks directly to this internally generated decision stage within the broader spatial attention framework.

      We have revised the manuscript to emphasize the limited nature of our paradigm and discuss other phenomena that could fall under willed attention, such as self‑initiated shifts of attention without any external prompt, decisions about what feature or object category to attend, or self‑timed initiation and termination of attentional episodes, and moreover, we refer to the review by Nadra and Mangun (2023) where broader issues are discussed.

      (2) The manuscript is lacking a description of the decision processes used during the willed attention paradigm and is lacking evidence as to WHEN subjects made their willed decision. Both of these points are of major concern:

      These are important points. The temporal aspects of the decision process in this paradigm have been addressed in prior work using EEG (Rajan et al., 2018). In that study, we found that frontal theta oscillations serve as an index of decision‑making: for choice trials, a burst of frontal theta power emerged between approximately 400 and 800 ms after the cue, a pattern that was not present in instructed trials. In addition, using the onset of posterior alpha lateralization as a marker of attentional set implementation, we showed that in choice trials, the deployment of the posterior attention set was delayed by about 400–500 ms relative to instructed trials. Together, these EEG findings suggest that the decision process takes place in the time period of ~400–800 ms after the choice cue and it lasts on the order of 400–500 ms. We now explicitly discuss the timing of the decision process in the revised manuscript.

      (a) The authors state: "For willed attention, participants were explicitly told to avoid relying on any stereotypical strategies of generating decisions, such as always attending the same/opposite side they attended during the previous trial, as well as to avoid randomizing or equalizing their decisions to choose left or right across trials; prior studies found that decisions to explicitly randomize decisions might invoke additional working memory related processes (Spence & Frith, 1999)." Subjects were instructed NOT to apply a simple heuristic and NOT to randomize or try to equalize their decisions, but exactly HOW the subjects made their decisions is not at all clear. What options does that leave? How does this strategy avoid the working memory-related processes mentioned in the Spence & Frith, 1999 citation? The brain regions that comprise the network of interest (aka Frontoparietal Decision Network) are activated by a very broad range of visual cognitive tasks, including many working memory paradigms. The Anterior Insula and dACC nodes Salience Network often simply reflect task difficulty. Obviously, making a choice is more cognitively demanding than not making a choice. The present experiments do not distinguish functional roles between different regions of the Frontoparietal Decision Network. On the whole, the study does very little to isolate the cognitive processes or neural bases of willed attention beyond calling out the set of 'Usual Suspects' for visual cognition.

      These are important issues. The purpose of the instructions was to encourage subjects to make a genuinely spontaneous decision about where to attend on each choice trial, rather than relying on simple deterministic strategies (e.g., always alternating left/right) or explicitly trying to randomize or equalize their choices across the session. Spence and Frith (1999) pointed out that attempts to explicitly generate random sequences can recruit working memory and additional control processes. Our instructions were therefore designed to minimize both stereotyped patterns and explicit randomization strategies, and instead to encourage subjects to “go with their momentary choice” on each trial. While we cannot directly observe the exact decision rule each individual used, prior analyses of sequence structure in this paradigm (Bengson et al., 2014) found no evidence that first‑ or second‑order sequence effects (e.g., simple alternation or repetition biases) explained the pattern of choices, consistent with the idea that responses were not governed by a simple fixed strategy.

      Regarding the frontoparietal network, prior work has indeed shown that the choice cue in this task activates regions such as dACC, DLPFC, anterior insula, and IPL (Bengson et al., 2015; Liu et al., 2017). We fully agree with the reviewer that these regions support a wide range of cognitive functions (including working memory, cognitive control, and task difficulty), and we do not claim to have dissociated all of these functions here. The contribution of the present work is to go beyond univariate “activation maps” by showing that: (i) multivoxel patterns in this frontoparietal network encode which spatial alternative is chosen on a given trial (left vs right) in willed attention, whereas no such information is decodable in instructed attention, and (ii) trial‑by‑trial patterns of precue alpha activity predict subsequent choices and frontoparietal activity. Together, these findings link this network not only to general task engagement, but specifically to the internally generated decision about where to attend in this paradigm. We have revised the manuscript to further clarify these points and emphasized that the component nodes of the frontoparietal network are not functionally decomposed in detail by the present study.

      (b) The finding that pre-cue EEG signals predicted the post-cue decision is intriguing. It could mean that the seemingly irrelevant and transient state of the brain causally and unconsciously biased the subject to one direction or the other. Alternatively, it could mean that the subjects utilized the pre-cue period to make their decision and hold it in case it was needed (i.e., that it was a choice trial). While 2-8 seconds ITI variability makes sense for fMRI decoding, it is a long time for a subject to idly wait, so they might fill that time preparing for the next trial. There appears to have been a substantial amount of individual difference in the pre-cue alpha decoding, which could reflect individual differences in cognitive strategy, specifically in the use of the pre-cue period to make their decision. More efficient decision makers might have pre-decided, which might account for the neural efficiency. The experiments lack any measurement of WHEN participants made their decision. For that reason, I would ask that the authors temper their claims about the significance of the alpha decoding and its possible causality.

      Thank you for this thoughtful comment. The two interpretations the reviewer raises—momentary brain state unconsciously biasing the upcoming choice versus subjects pre‑deciding during the inter‑trial period and holding that decision—are both, in principle, possible. Our design does not allow us to measure the exact moment at which each decision is made, so we cannot definitively rule out pre‑decision during the ITI. However, several considerations make a full “pre‑decide and hold” account less likely.

      First, choice trials constituted only one third of all trials. Any decision formed and held throughout the pre‑cue period would have to be discarded on the majority of trials when an instruction cue appeared. This would impose a relatively inefficient strategy that we did not encourage. Second, if subjects were consistently forming decisions well before the cue and maintaining them, we would expect above‑chance decoding from alpha patterns earlier in the pre‑cue interval. Instead, see Figure 4B, only alpha activity in the last ~500 ms prior to the cue reliably predicts the upcoming choice; earlier windows do not show robust predictive information. This temporal profile is more consistent with a decision process that crystallizes in close temporal proximity to the cue rather than being stably maintained over the entire 2–8 s interval.

      Regarding the broader temporal dynamics of the decision process, prior EEG work in this same paradigm (Rajan et al., 2018) showed that frontal theta activity specific to willed attention emerges 400–800 ms after the choice cue, and that the implementation of the posterior attention set (indexed by alpha lateralization) is delayed by approximately 400–500 ms in choice trials relative to instructed trials. Together, these findings place the main decision stage within the cue–target interval, rather than far in advance of the cue, and support the view that choices are formed spontaneously when the choice cue appears.

      At the same time, we fully agree that the present experiments do not provide a direct measure of when each individual subject commits to a particular choice, and that alpha decoding alone does not establish a causal influence of precue brain state on behavior. In the revised manuscript we therefore temper our wording about the implications of the precue alpha decoding, explicitly describing it as evidence that ongoing brain state carries predictive information about upcoming choices.

      (3) Did individual subjects exhibit a choice bias of location for the willed trials? If not, doesn't that raise concerns that subjects were trying to equalize their trials? If they do exhibit location biases, how does that impact the decoding? A simple decoder could learn to always just guess the biased direction for a subject and would perform > 50%. Consider the example in which an individual subject chooses 'Left' 55% of the time. A classifier that simply learns to choose 'Left' on every trial will be correct on 55% of trials. The training data would likely be sufficient to learn the direction of choice bias in each individual subject. So the classifiers could perform significantly above 50% without learning anything beyond the tendency of each subject. That is to say, 50% is not truly chance in this data set. It doesn't appear that Permutation testing has been performed to empirically determine chance for an individual's data. Permutation methods, scrambling the labels 1000 or 10000 times to establish a true baseline would be preferred over simply comparing to 50% and would address concerns about individual subject biases.

      Thank you for this thoughtful comment. To address the possibility that individual choice biases might inflate decoding above 50% accuracy, we conducted additional analyses.

      First, we examined whether subjects showed systematic left/right choice biases on willed trials. Figure A3A shows left/right choice proportions for each subject and dataset; dots indicate individual subjects’ percentages of left choices. Across the combined datasets, the mean proportion of left choices was 48.9%, which did not differ significantly from 50% (p = 0.581). At the individual-subject level, 10 of 31 subjects fell outside the 40–60% range, indicating that some degree of bias was present for a subset of participants, but that there was no consistent group-level bias toward one side.

      Second, to test whether such biases might drive the decoding results, we repeated the precue alpha decoding after equating the number of choice-left and choice-right trials within each subject. We then performed 10,000 within-subject label permutations to obtain an empirical chance distribution for each subject and for the group. In Figure A3B, balanced decoding of 52.81% was significantly above the empirical permutation baseline decoding accuracy of 50.01% at p = 0.028, indicating that precue decoding remains significantly above chance after accounting for trial imbalance and subject-specific choice biases. We now include these results in the Supplementary Materials and describe them in the revised manuscript, and we explicitly state that decoding accuracy is evaluated against an empirical permutation baseline rather than assuming a fixed 50% chance level.

      (4) The novel contributions of this work beyond the two prior Bengson et al papers from Dr. Mangun's lab appear quite modest. The discussion would be enhanced by specifically stating how the present work advances understanding beyond the prior Bengson studies.

      The Bengson studies have indeed laid an important foundation for the present work, and we agree that it is useful to explicitly articulate how our study extends their findings. Below we highlight three main advances.

      First, Bengson et al. (2015) showed that the choice cue in the willed attention paradigm activates a frontoparietal network, including regions such as dACC, DLPFC, and parietal cortex. In the present work, we replicate this activation pattern and go beyond it by using multivoxel pattern analysis to demonstrate that this network carries information about which spatial alternative is chosen (left vs right) on each willed attention trial. In other words, we attach the specific function of representing willed spatial decisions to this previously identified frontoparietal network, rather than only showing that it is engaged by the task.

      Second, Bengson et al. (2014) reported that choice-left and choice-right trials are accompanied by different patterns of precue alpha lateralization. Here, we build on that result by showing, with MVPA decoding, that distributed patterns of alpha power in the precue interval systematically predict the subsequent choice, and by mapping the time course of this effect. Our decoding time-course analysis indicates that predictive information is confined to the final ~600 ms before cue onset, rather than being present throughout the entire inter-trial interval. This timing supports the interpretation that the decision about where to attend is formed relatively close in time to the cue, rather than being pre-planned early in the ITI and simply held until needed.

      Third, we introduce a neural efficiency metric that links precue alpha decoding to postcue frontoparietal activation and decoding. This analysis shows that individuals with stronger precue alpha-based predictability of their choices tend to show more efficient (i.e., lower-amplitude yet still decodable) frontoparietal responses when implementing those choices. By relating ongoing brain state to subsequent decision-related network engagement, this provides a novel connection between spontaneous precue dynamics and the efficiency of the decision network that was not addressed in the earlier Bengson studies.

      Taken together, these contributions extend prior work by (i) demonstrating that the frontoparietal network encodes the content of willed spatial decisions, (ii) showing that precue alpha patterns in a specific late time window bias those decisions, and (iii) linking these precue patterns to individual differences in the efficiency of decision-related neural responses. We further highlight these points in the revised manuscript to clarify the added value of the present study over the earlier Bengson et al. reports.

      Reviewer #3 (Public review):

      Summary:

      This manuscript analyzes two independent datasets collected at different sites. Using the same willed-attention paradigm (instructional vs. choice cues) and combining fMRI and EEG analyses, the authors investigate how attentional direction is selected when no external instruction is provided. Their main claims are that the dorsal attention network is engaged by both cue types, whereas the choice cue additionally involves a frontoparietal decision network. Moreover, left-versus-right attentional decisions can be decoded in this decision network only on choice trials, and multichannel pre-stimulus alpha patterns predict the subsequent attentional choice. Finally, individuals with more predictive alpha patterns show greater neural efficiency in the decision network, i.e., higher decoding with lower BOLD activation.

      The question is worthwhile and the two-site design is a genuine strength. At the same time, several central inferences rely on decoding analyses for which the statistical testing and cross-validation structure are not described in enough detail to assess robustness. In addition, using a ratio-based neural-efficiency measure make the interpretation more fragile than it needs to be. With a focused revision that tightens inference around MVPA and clarifies a few methodological points, I think the paper could become substantially more convincing.

      Thank you for the succinct summary of our work and positive assessment. We address the concerns below.

      Strengths:

      The work extends previous willed attention studies by attempting to link pre-stimulus alpha pattern predictability to post-cue frontoparietal representations, and by testing reproducibility across two datasets. The conceptual advance beyond previous studies, e.g., Bengson et al. (2015), however, depends on how solid the decoding-based evidence is and whether alternative explanations are convincingly excluded. At present, the strength of support is limited mainly by incomplete reporting and/or controls for MVPA significance testing, as well as potential inflation of decoding estimates if folds are not independent of run structure. Concerns about statistical assessment of decoding accuracy are well documented in the literature (Combrisson & Jerbi, 2015).

      Thank you for raising concerns regarding the analysis in the paper. We address these concerns below.

      Weaknesses:

      (1) The manuscript describes the decoding pipeline for both fMRI and EEG MVPA. However, it does not clearly specify how "significantly above chance" is determined for the fMRI ROI decoding, nor how multiple comparisons across ROIs are handled, even though p-values are reported. The same issue applies to the time-resolved EEG analysis across many time points. For each decoding analysis, please specify the inferential test (e.g., permutation test within participant, group-level test on subject accuracies, binomial test, etc.) and report effect sizes with confidence intervals (e.g., Combrisson & Jerbi, 2015). Further, for EEG decoding over time, it would be preferable to control family-wise error, e.g., cluster-based permutation, rather than thresholding pointwise p-values. A standard approach here is the nonparametric cluster framework (e.g., Maris & Oostenveld, 2007).

      We thank the reviewer for this detailed and constructive comment. For the fMRI ROI decoding, each participant contributed one decoding accuracy value per ROI, obtained by averaging across cross-validation repetitions. In our original analysis, we tested whether decoding accuracy was significantly above the 50% chance level using group-level one-sample t-tests across participants, with FDR correction applied to control for multiple comparisons across ROIs. We now make this clear in the revised manuscript.

      Following the reviewer's suggestion, we additionally performed a random permutation test for each ROI, following the approach of Combrisson and Jerbi (2015), and computed effect sizes. See Table A1 (now included in the Supplementary Materials), decoding accuracy in all 9 ROIs was significantly above chance at the combined-dataset level, with multiple comparisons controlled via FDR. We include this permutation-based analysis in the Supplementary Materials and comment on the result in the revised manuscript.

      For the EEG time-resolved decoding, we followed the reviewer's suggestion and implemented a cluster-based permutation approach (Maris & Oostenveld, 2007) to control the family-wise error rate across time points. At each time point, decoding accuracy was compared against the 50% chance level using a one-sided dependent-samples t-test across participants. Consecutive time points exceeding an initial threshold of p < .05 were grouped into clusters, with cluster size defined as the number of consecutive significant time points. We then constructed a null distribution of the maximum cluster size using 10,000 sign-flip permutations and evaluated the observed cluster against this null distribution to control the familywise error rate. Using this approach, the cluster identified in Figure 4 was significant at pFWER = .008 at the combined-dataset level. We now report this cluster-based permutation result in the revised manuscript, along with the original analysis, in the revised manuscript.

      (2) The cross-validation approach used here is appreciated and appropriate in principle. However, random 10-fold splits across trials can inflate accuracy if training and test folds share run-specific noise, scanner drift, or autocorrelated structure. The manuscript should indicate whether folds were blocked by run or randomized across the entire session. In addition, please report the number of trials per condition after artifact rejection and after removing short ITIs for the long prestimulus epochs (−2500 ms to 0 ms) for each dataset in the section of EEG preprocessing. Similarly, please report how often participants chose left vs. right on choice trials, and whether balanced folds (or an equivalent balancing procedure) were used if needed.

      We thank the reviewer for this careful comment. To clarify, cross-validation folds were randomized across the entire session rather than blocked by run. We acknowledge that this approach could in principle allow training and test folds to share run-specific noise or scanner drift, which may inflate accuracy estimates relative to run-blocked cross-validation. In the revised manuscript, we note this as a limitation of our cross-validation scheme.

      We have also added the requested trial-count information to the EEG preprocessing section, reporting the number of trials per condition after artifact rejection and after excluding short-ITI trials for the long prestimulus epochs (−2500 to 0 ms), separately for each dataset.

      Regarding choice behavior, we now report the proportion of left versus right choices on choice trials for each dataset (see also our response to Reviewer 2's related comment on choice bias, where we found a group mean of 48.9% left choices, not significantly different from 50%). To address potential imbalance in individual subjects, we repeated the decoding analysis using trial-balanced folds (equating the number of left- and right-choice trials within each subject) and confirmed that the pattern of decoding results was consistent with our original analysis. This balanced-fold analysis is now reported in the revised manuscript.

      (3) Moreover, ROI definition is not sufficiently specified and independence should be clarified. The ROIs are defined based on peaks from the choice-instructed univariate contrast (Table 2) and then used for MVPA. First, are these ROIs defined as spheres around peaks or using anatomical masks? What radius or voxel count was used? This needs to be explicit. Second, I am concerned about circularity risk. Although choice-vs-instructed selection is not identical to left-vs-right decoding, ROI selection from the same dataset can still bias descriptive estimates and encourage overinterpretation if not carefully justified (Kriegeskorte et al., 2009). At minimum, the authors should explain why their selection criterion is independent of the decoded contrast under the null, and ideally provide a robustness check using either anatomical ROIs or independently defined ROIs, e.g., from prior literature or an atlas.

      We thank the reviewer for this comment. Regarding ROI definition, the ROIs were defined as 5-mm-radius spheres centered on peak voxels from the choice > instructed contrast; no anatomical masks were used. This is now stated explicitly in the revised Methods.

      Regarding the concern about circularity, our ROIs were indeed defined using the choice > instructed contrast from the same dataset, and left–right decoding was subsequently performed within these ROIs. As the reviewer notes, this raises a general concern about "double dipping" (Kriegeskorte et al., 2009) whenever the selection contrast is not independent of the statistic used in the selective analysis under the null hypothesis. In our design, the choice–instructed contrast was constructed by collapsing across left and right trials within each condition, and was therefore driven by overall differences in activation magnitude between willed and instructed attention, not by the left–right spatial distinction that is the target of the decoding analysis. Under the null hypothesis of no left–right information in the multivoxel patterns, the mean activation level used for ROI selection and the spatial pattern used for decoding are distinct quantities: a region could show a large choice–instructed activation difference while carrying no left–right information whatsoever, or vice versa. This argues that the two statistics are not mechanically coupled, reducing the risk that ROI selection based on the former systematically inflates decoding accuracy for the latter. We have clarified this logic explicitly in the revised Methods.

      Thanks for the comment. Regarding ROI definition, the ROIs were defined as spheres around contrast peaks, where the radius is 5 mm. No anatomical masks were used. This is now made clear in the revised manuscript. Regarding potential circularity in our ROI-based analyses, our ROIs were defined using the choice > instructed contrast from the same dataset, and we then performed left–right decoding within these ROIs. As the reviewer notes, this raises a general concern about “double dipping” (Kriegeskorte et al., 2009) if the selection contrast is not independent of the statistic used for the selective analysis under the null hypothesis. In our design, the choice–instructed contrast was constructed by collapsing across left and right trials within each condition and thus was sensitive to overall differences in activation between willed and instructed attention conditions, but not to the left–right distinction that is the target of the decoding analysis. Under the null hypothesis of no information about left vs. right in the multivoxel patterns, the choice–instructed contrast and the left–right decoding statistic are therefore orthogonal by construction, which reduces the risk that ROI selection based on the former will inflate the latter.

      (4) Using an index of neural efficiency is conceptually interesting. However, if the denominator, computed as the activation difference between choice and instructional conditions, is near zero or noisy, the ratio can become unstable. I would rather see a multivariate model that treats activation and decoding as separate dependent measures, or a latent-variable approach, than a single ratio.

      We appreciate the reviewer’s thoughtful comment. Our aim in using the neural efficiency metric was to provide an intuitively interpretable summary measure linking frontoparietal activation amplitude to decoding performance, but we agree that ratio measures can be problematic if not carefully evaluated. We also agree that more sophisticated multivariate or latent-variable approaches could provide a richer characterization of the joint relationships among activation, decoding, and behavior than a single ratio. Implementing and validating such models would, however, require additional analytic development that is beyond the scope of the present manuscript. We have therefore tempered our language when discussing neural efficiency, explicitly acknowledging the limitations of ratio-based measures and noting that future work could profitably apply multivariate or latent-variable modelling to more fully capture these relationships.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      The authors should update Figure 2 to include a color bar representing t or z values and explicitly state the thresholding used for the maps. It is also essential that Figure 5B be updated to use identical scaling for both the UF and UCD subplots to ensure a transparent comparison of effect sizes across the two datasets. Regarding the statistical metrics, the authors should provide a sensitivity analysis or permutation test for the neural efficiency metric to ensure the ratio is stable and not driven by low variance BOLD denominators in the denominator of their calculation. A report of the univariate alpha asymmetry results is also recommended to validate that the multivariate patterns correspond to established raw alpha lateralization patterns in the posterior sensors.

      We thank the reviewer for these comments. Figure 2 has been updated to include a color bar indicating t-values, and the figure legend now explicitly states the statistical thresholding used to generate the map (including the threshold value and correction method applied). Figure 5B has also been revised so that the UF and UCD subplots now use identical axis scaling, allowing for a transparent, direct comparison of effect sizes across the two datasets.

      Regarding additional sensitivity analyses for the neural efficiency metric, our aim in using this metric was to provide an intuitively interpretable summary measure linking frontoparietal activation amplitude to decoding performance, and we agree that ratio measures can be problematic if not carefully evaluated. In line with Reviewer 3's related comment, we have tempered our interpretation of this metric in the revised manuscript and now explicitly describe it as an auxiliary, descriptive index rather than a primary inferential measure. We also note that more sophisticated multivariate or latent-variable approaches, as suggested by the reviewer, would provide a more rigorous characterization of the joint relationships among activation, decoding, and behavior, but that implementing such models is beyond the scope of the present study.

      Regarding univariate alpha asymmetry, Bengson et al. (2014) have already shown that the alpha asymmetry pattern prior to the choice cue in this paradigm is consistent with established attentional modulation of posterior alpha lateralization. We now explicitly note in the revised manuscript that our multivariate precue alpha decoding builds on this prior univariate finding, and we cite Bengson et al. (2014) as providing the corresponding raw alpha lateralization results.

      The methods section should be updated to explicitly state which TRs were used for the fMRI decoding and provide a justification for why a time-resolved approach was not utilized given the richness of the temporal data. Furthermore, the authors should provide a theoretical explanation for the observed behavioral parity between conditions. Specifically, it would be beneficial to discuss why the additional metabolic cost and recruitment of the willed network do not result in a behavioral tax such as slower reaction times or lower accuracy. This discussion should address whether the recruitment of the anterior insula and dACC might trigger an internal arousal shift or compensatory effort that allows the brain to maintain performance levels identical to the simpler instructed condition. Finally, the authors should clarify if site specific effects were modeled in their meta-analysis to account for the performance differences between UF and UC cohorts.

      We thank the reviewer for these helpful suggestions. With respect to the fMRI decoding, we did not use TR‑level data. Instead, we modeled each trial using a single‑trial GLM and extracted one beta estimate per trial, which served as the input to the multivoxel pattern analysis. In other words, the decoding was performed on trial‑wise parameter estimates rather than on individual TRs. We have clarified this explicitly in the Methods. Because our primary question about temporal dynamics was addressed using EEG, we did not implement a time‑resolved fMRI decoding approach. We now briefly justify this choice in the Methods, noting that the richer temporal information from EEG was used to characterize time courses, whereas the fMRI analysis focused on spatial patterns at the level of trial‑wise responses.

      Regarding the relation between behavior and insula/dACC activation, we agree that this is an important issue and have addressed it in detail in our response to Reviewer 1’s comment #2 in the Public View section above.

      Finally, we did not model site‑specific effects in our meta‑analysis. We now state this explicitly in the Methods.

      Reviewer #2 (Recommendations for the authors):

      Copying key text from the above section:

      (1) It would be helpful to discuss what other phenomena might fall within 'willed attention' and what some future studies might choose to focus on, along with some potential pitfalls

      (2) If possible, state your understanding of what processes where engaged by the decision component of the Willed Attention trials.

      (3) Discuss the timing of when subjects made decisions. Please temper claims about the significance of the alpha decoding and its possible causality.

      (4) Re-run MVPA analysis with Monte Carlo Methods to rule out potential biases at the level of individual subjects and to more properly establish chance levels. That is, scramble the labels and run it at least 1000 times per subject to establish what chance actually is.

      (5) The discussion would be enhanced by specifically stating how the present work advances understanding beyond the prior Bengson et al. studies.

      We appreciate the reviewer’s detailed suggestions and have addressed each of the points (1–5) in our responses above. In the revised manuscript, we now (1) expand the Discussion to consider other phenomena that may fall under willed attention and potential future directions and pitfalls, (2) clarify our interpretation of the processes engaged by the decision component of the willed attention trials, (3) discuss the timing of decisions and temper our claims regarding the significance and possible causality of the precue alpha decoding, (4) add permutation-based analyses of the MVPA to better characterize empirical chance levels and potential individual-subject biases, and (5) explicitly articulate how the present work extends the prior Bengson et al. studies.

      Minor Concerns:

      (1) Introduction. I found this set of statements to be confusing. I ‘Think’Table 1 that the statement implies that several one-second intervals were examined. If so, changing 'sequential 1 sec period' to 'sequential 1 sec periods' would help to reduce confusion. "The previous study (Bengson et al., 2014) reported that the amplitude of left parieto-occipital EEG alpha power in the 1 sec period immediately before the unpredictable appearance of the choice cue predicted the decision about where to attend. How far does this alpha-based predictability extend before the choice cue? Bengson and colleagues (2014) investigated sequential 1 sec period prior to the choice cue, and reported no significant predictive value of the parieto-occipital alpha power earlier in time.

      Thank you for pointing out this ambiguity. In the revised Introduction, we have clarified that Bengson et al. (2014) examined multiple sequential 1‑s periods prior to the choice cue, and we now use the plural “periods” to reflect this. We also rephrased the passage to more clearly distinguish their 1‑s windowed analysis from our finer‑grained time‑course decoding, which refines their result by localizing the predictive alpha pattern to approximately the final 600–700 ms before the cue.

      (2) Methods - Neural Efficiency: The definition of 'Neural efficiency' appears to be novel. This is quantified by the difference in decoding accuracy (choice vs. instructional) divided by the difference in BOLD activation (choice vs. instructional). Was this Neural Efficiency measure pre-registered or only derived post-hoc? While this is an intriguing construct, it is not clear why this metric was chosen over simply looking at the numerator. Isn't fMRI decoding accuracy the more relevant measure to compare to EEG decoding accuracy?

      We appreciate the reviewer’s careful comments on the neural efficiency metric. This measure was not preregistered; it was introduced post hoc as an intuitively interpretable, summary index relating frontoparietal activation amplitude to decoding performance. In defining it as the difference in decoding accuracy (choice vs. instructed) divided by the difference in BOLD activation (choice vs. instructed), our goal was to capture, in a single quantity, how much additional decodable information is obtained per unit increase in metabolic activity, in line with common informal uses of “neural efficiency” as doing more with less.

      We agree that fMRI decoding accuracy alone is a highly relevant and more standard measure to compare with EEG decoding accuracy, and we do not claim that the ratio is superior to examining the numerator by itself. In the revised manuscript, we therefore (i) clarify that the neural efficiency index was exploratory and not preregistered, (ii) present the decoding results themselves as the primary inferential measure, and (iii) describe the ratio explicitly as a descriptive, auxiliary metric that combines activation and decoding in a way that is conceptually appealing but statistically more fragile. We also note that more formal multivariate or latent‑variable approaches, as suggested by the reviewer, would provide a more principled way to model the joint relationships among activation, decoding, and behavior, but that developing such models is beyond the scope of the present study.

      (3) Methods - fMRI MVPA - which TRs from the trial were included in the MVPA analysis? All TRs following the onset of the cue? Does this include the actual deployment of spatial attention? Did any regions of the brain show effects for the instructed trials? One would think that even the univariate analysis would reveal right/left differences in dorsal attention network regions, including those in lateral frontal cortex.

      We thank the reviewer for these insightful questions. With respect to the MVPA analysis, we did not operate directly on TR‑level time series. Instead, we modeled each trial with a single‑trial GLM, using a canonical hemodynamic response function aligned to cue onset, and extracted one beta estimate per trial. These trial‑wise parameter estimates, which summarize the cue‑evoked BOLD response over the relevant post‑cue TRs, served as the input to the multivoxel pattern analysis. In other words, the decoding was performed on trial‑wise beta images rather than on individual TRs. Because these betas reflect the cue‑locked response, they capture activity associated with the deployment of spatial attention following the choice or instruction cue.

      Regarding effects in the instructed trials, the present work focused primarily on regions identified by the choice > instructed contrast, and on decoding within this willed attention network. The attention effects of instructed trials, including univariate contrasts between attending left and attending right in dorsal attention network regions and the visual cortex, are analyzed and reported in detail in Meyyappan et al. (2025). In the revised manuscript, we now clarify this focus in the Methods and refer explicitly to Meyyappan et al. (2025) for a treatment of lateralized attention effects in DAN and the visual system.

      (4) Results: It is curious that RTs differed by ~100 ms across data collection sites. Could the authors offer an explanation for this difference? This doesn't seem critical for any of the paper's claims, but it is a large effect left unexplained.

      The reviewer is correct to point out the quantitative differences in behavioral performance between the UF and UCD cohorts, with the UCD participants exhibiting slower reaction times and somewhat lower accuracy despite the use of the same willed‑attention paradigm and matched stimulus parameters. The exact source of these differences is not fully known, but one plausible contributor is procedural differences between sites: at UF, EEG and fMRI were recorded simultaneously in a single session, whereas at UCD, EEG and fMRI were acquired in separate sessions, which may have affected overall task engagement, familiarity with the task, and fatigue. We now comment on this site‑related behavioral difference in the revised manuscript.

      Reviewer #3 (Recommendations for the authors):

      Minors:

      (1) The sample characteristics are somewhat imbalanced by sex in the UCD dataset. I am not suggesting that a gender analysis is essential, but this should be transparently reported and briefly noted as a limitation.

      We appreciate the reviewer’s comment. In the revised manuscript, we now clearly point out the sex distribution of participants in the UCD dataset in the Methods section and explicitly note the resulting sex imbalance as a limitation.

      (2) Please clarify whether any site differences in acquisition, e.g., TR, slice order, EEG montage, simultaneous vs. separate EEG recording, were modeled as moderators.

      We did not model these factors as moderators. All datasets were acquired using highly similar acquisition protocols, and our primary analyses were conducted at the within-subject level, which reduces the impact of between-site differences. We now note this explicitly in the Methods.

      (3) In several places the writing uses strong mechanistic language, e.g., "These results demonstrate that the network of frontal and parietal brain regions preferentially activated during willed attention is involved in deciding (choosing) the direction of attention (left vs. right)." Given the correlational nature of the evidence, I would suggest toning this down to "consistent with" unless stronger causal constraints are added.

      The reviewer’s point is well taken. We have revised the manuscript to tone down mechanistic language, replacing strong causal statements with more conservative phrasing (e.g., “consistent with”) that reflects the correlational nature of our evidence.

      References:

      Rajan A, Siegel SN, Liu Y, Bengson L, Mangun GR, Ding M (2018). Theta Oscillations Index Frontal Decision-Making and Mediate Reciprocal Frontal–Parietal Interactions in Willed Attention. Cerebral Cortex 29(7): 2832-2843

      Nadra JG, Mangun GR (2023). Placing willed attention in context: a review of attention and free will. Frontiers in Cognition 2: https://doi.org/10.3389/fcogn.2023.1205618

      Bengson JJ, Kelley TA, Mangun G R (2015). The neural correlates of volitional attention: A combined fMRI and ERP study. Human Brain Mapping 36(7): 2443–2454.

      Bengson JJ, Kelley TA, Zhang X, Wang JL, Mangun GR (2014). Spontaneous Neural Fluctuations Predict Decisions to Attend. Journal of Cognitive Neuroscience 26(11): 2578– 2584.

      Liu Y, Hong X, Bengson JJ, Kelley TA, Ding M, Mangun GR (2017). Deciding where to attend: Large-scale network mechanisms underlying attention and intention revealed by graphtheoretic analysis. NeuroImage 157: 45–60.

      Kriegeskorte N, Simmons WK, Bellgowan PSF, Baker CI (2009). Circular analysis in systems neuroscience: The dangers of double dipping. Nature Neuroscience 12(5): 535–540.

      Combrisson E, Jerbi K (2015). Exceeding chance level by chance: The caveat of theoretical chance levels in brain signal classification and statistical assessment of decoding accuracy. Journal of Neuroscience Methods 250: 126–136.

      Maris E, Oostenveld R (2007). Nonparametric statistical testing of EEG- and MEG-data. Journal of Neuroscience Methods 164(1): 177–190.

    1. Author response:

      The following is the authors’ response to the previous reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      The authors describe a massively parallel reporter assays (MPRA) screen focused at identifying polymorphisms in 5' and 3' UTRs that affect translation efficiency and thus might have a functional impact on cells. The topic is of timely interest, and indeed, several related efforts have recently been published and preprinted (e.g., https://pubmed.ncbi.nlm.nih.gov/37516102/ and https://www.ncbi.nlm.nih.gov/pmc/articles/PMC10635273/). This study has several major issues with the results and their presentation.

      Major comments:

      The main issue remains that it appears that the screen has largely failed, and the reasons for that remain unclear, which make it difficult to interpret how useful is the resulting data. The authors mention batch effects as a potential contributor. The authors start with a library that includes ~6,000 variants, which makes it a medium-size MPRA. But then, only 483 pairs of WT/mutated UTRs yield high confidence information, which is already a small number for any downstream statistical analysis, particularly since most don't actually affect translation in the reporter screen setting (which is not unexpected). It is unclear why >90% of the library did not give high-confidence information. The profiles presented as base-case examples in Fig. 2B don't look very informative or convincing. All the subsequent analysis is done on a very small set of UTRs that have an effect, and it is unclear to this reviewer how these can yield statistically significant and/or biologically-relevant associations.

      We recognize that RNA distribution within polysomes is inherently less stable than the associated protein components. This instability has been noted in previous studies, including those cited by the reviewer, which used RNA from bulk polysomes to infer the translatome without fractionation. Acknowledging this limitation, we purposely adopted a conservative strategy: (i) performing gross fractionation of polysomes, and (ii) collaborating with biostatisticians at the Institute of Statistical Science, Academia Sinica, to design a conservative yet optimized analysis pipeline that minimized batch effects.

      To better illustrate the observed differences, we revised Fig. 2B to show the summarized proportions across fractions with error bars, allowing clearer visualization of the differences between genotypes.

      From our high-confidence dataset, we applied a well-established statistical framework specifically designed to accommodate multiple influencing factors in relatively small datasets (Elements of Statistical Learning by Hastie, Tibshirani, and Friedman). We further conducted sensitivity analyses to select an optimal QC cutoff across a range of stringencies, ensuring maximal reliability of our results. We have therefore successfully shortlisted UTR variants which have strong effect on translation.

      Building upon these conservative measures, we developed a predictive model for translation effects of UTR variants. Importantly, this model was validated not only with our internal test dataset but also with independent external datasets. In addition, the sequence features identified by the model were validated through reporter assays and in vivo CRISPR editing. These external and functional validations establish the generalizability and robustness of our approach.

      From the variants that had an effect, the authors go on to carry out some protein-level validations, and see some changes, but it is not clear if those changes are in the same direction was observed in the screen. In their rebuttal the authors explain that they largely can not infer directionality of changes form the screen, which further limits its utility.

      To determine the direction of polysome shifting, we repeated polysome profiling of the UTR libraries, separating transcripts into free RNA, 40S, and fractions containing 1–8 ribosomes (See Fig. 7A). Following established approaches, we used log<sub>2</sub> [polysome (F2–F8)/ (free + 40S)] as an estimate of translational efficiency. This measure showed a strong correlation with translational efficiency determined by luciferase activity normalized to RNA expression (Spearman r = 0.744; See Fig. 7B). We then used this measure to assign the direction of polysome shifting (increased or decreased) to the significant variants (Supplemental Table S4).

      Because the contribution of 5’ UTRs to translation was more evident than that of 3’ UTRs, we further used the estimated ribosome load of WT 5’ UTR sequences to construct a multivariable model explaining variation in 5’ UTR translational efficiency (Fig. 7C). The model significantly explained ribosome load in held-out data and was further supported by independent reporter transfections, in which model-derived values correlated with luciferase output (Spearman r = 0.762; Fig. 7D, E).

      We have modified the main text to describe these measurements and modeling analyses (p. 23–24):

      “Modeling the polysome occupancy of 5’ UTRs

      Because 5’ UTRs contain multiple features, including RBP-binding motifs and RNA folding energy, that may jointly influence translation, we next asked whether these features could explain variation in polysome occupancy. We performed high-resolution polysome profiling of the UTR library, separating transcripts into free RNA (Free), 40S, monosome (1 ribosome), and polysome fractions containing 2-8 ribosomes (Fig. 7A). We evaluated several metrics of ribosome association and found that the polysome fraction normalized to the free and 40S fractions [Poly/ (Free + 40S)] showed the strongest agreement with the change in translational efficiency between WT and mutant pairs measured using luciferase reporters (Spearman r = 0.744) (Figs. 3 and 7B). We therefore used this index as a quantitative measure of polysome occupancy and assigned the direction of occupancy change (increased or decreased) for each polysome-shifting variant (Supplemental Table S4).

      To identify 5’ UTR features associated with polysome occupancy, we first selected representative features from highly correlated feature groups (for example, CG dinucleotide frequency and overall GC content) and then applied standardized multivariable regression to estimate their relative effects, statistical significance, and confidence intervals (see Methods). Of the 2,850 WT 5’ UTRs in the library, 2,362 passed the read-depth and quality-control criteria and were included in the model. The resulting model revealed positive associations of GC-rich k-mers with polysome occupancy. GA-repeat motifs recognized by SRSF-family proteins were also positively associated with polysome occupancy (Fig. 7C), consistent with their enrichment among polysome-shifting UTR variants identified independently in our variant analysis (Figs. 4 and 5).

      The multivariable model significantly explained variation in the observed polysome occupancy (Fig. 7D, Supplemental Table S4). Moreover, model derived polysome occupancy highly correlated with luciferase activity measured independently across eight WT 5’ UTRs (Spearman r = 0.762) (Fig. 7E), providing functional support for the relationships captured by the model. Together, these results identify sequence and regulatory features associated with 5’ UTR-dependent ribosome loading and provide a quantitative framework linking UTR composition and RBP-binding motifs to translational output.”

      The corresponding experimental and modeling details have also been added to the Methods section (p. 7-8 and 14-16).

      It is particularly puzzling how the authors can build a machine learning predictor with >3,000 features when the dataset they use for training the model has just a few dozens of translation-shifting variants.

      Starting with variants that passed our stringent quality-control criteria, we applied a statistical framework suited for evaluating multiple features in relatively small datasets (Hastie, Tibshirani, and Friedman, The Elements of Statistical Learning). We also systematically varied the QC threshold to assess the robustness of the results across different filtering stringencies. Importantly, the resulting findings were supported by independent reporter assays and further validated using an external dataset, demonstrating their reproducibility across experimental platforms and datasets.

      Comments on revisions:

      It appears that the authors have extracted the information they could from the problematic dataset they obtained. Repeating the experiments in a cleaner setting, obtaining data for the >6000 UTRs they intended will allow the authors to achieve the goals they set out to achieve in establishing the screen.

      We appreciate the reviewer’s valuable comments. In response, we repeated polysome profiling of the UTR library. The repeated experiment not only reproduced the overall results of our initial screen but also provided additional information on the distribution of UTRs in the free RNA and 40S fractions. Using these data, we derived a polysome association index [Poly/ (Free + 40S)], which showed strong agreement with translational efficiency independently measured using individually transfected luciferase reporters. Together with the extensive additional analyses and revisions described above, these new data substantially strengthen the experimental foundation of our study and provide a more quantitative framework for interpreting the effects of UTR variants on translation.

      We sincerely thank the reviewer for this constructive comment, which helped us improve the rigor and overall quality of the study.

    1. Author response:

      We thank the Editors and reviewers for their careful reading of our manuscript and their constructive comments. We appreciate their positive assessment of our work and recognize the importance of the concerns they raise. In the revised manuscript, we will address the potential contribution of stimulus repetition and adaptation by introducing additional control analyses examining how preceding stimuli and responses influence perceptual reports. These analyses will help assess the extent to which recent stimulus and response history may contribute to our findings. Furthermore, we will provide a more detailed explanation and justification of the two-alternative detection-choice (2-ADC) model, including how sensitivity (d′) and response criteria were estimated from the stimulus–response contingencies. Additional methodological and statistical clarifications will address the staircase procedure and the calculation and interpretation of the reported bootstrap p-value in Experiment 2. The reviews also offer several suggestions for improving the presentation, terminology, and clarity of the manuscript. In particular, we will clarify our use of the terms “feature expectation” and “feature probability,” distinguishing the experimental manipulation from its interpretation in terms of expectation. Finally, we will revise the discussion of the latency results to incorporate the literature on oculomotor interference and stimulus-induced saccadic inhibition highlighted by the reviewers. A detailed response to the reviewers’ comments will accompany the revised manuscript.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      In this study, Angla et al investigate the basis of observations made from previous studies where loss of Onecut (OC) transcription factors leads to changes in spinal interneuron populations that do not themselves normally express OC. The authors hypothesize that OC expression in spinal motor neurons has non-cell-autonomous effects on pre-motor interneuron (V1, V2a/b/c) population size and distribution. By knocking out OC in the motor neuron lineage (i.e., downstream of Olig2, a motor neuron progenitor marker gene), they indeed show that motor neuron-specific loss of OC expression decreases V2c interneuron number and alters the spatial distribution of V1, V2a, V2b, and V2c populations. Using bulk RNA-sequencing of WT and OC conditional knockout (cKO) motor neurons, the authors identify that the neurotrophic factor Ntf3 is downregulated by OC expression. They subsequently hypothesize that the non-cell-autonomous effects observed by loss of OC expression in motor neurons can be explained by de-repression of Ntf3. To test this, the authors conditionally knock out Ntf3 downstream of Olig2 and show that this leads to increased interneuron numbers and alters their spatial distribution, ultimately leading to dysregulation of spinal motor circuits and motor activity.

      Strengths:

      The authors use sophisticated genetic tools to precisely remove OC and Ntf3 expression in a lineage-specific manner and comprehensively assess the downstream effects across brachial, thoracic, lumbar levels of the spinal cord, as well as at two developmental timepoints, E12.5 and E14.5.

      Weaknesses:

      There are two main concerns that are not fully addressed:

      (1) Based on the effects observed with OC vs. Ntf3 cKO, it is unclear whether OC is indeed exerting its non-cell-autonomous effects via Ntf3. Knocking out both Ntf3 and OC and comparing the effects to those seen with just OC cKO alone could provide more insight on this point.

      In this study, we did not intend to demonstrate that Onecut transcription factors exert their non-cell autonomous action on spinal interneuron development by regulating Ntf3 expression, and we do not state in the manuscript that this is the case. We only show that Onecut factors and Ntf3, the expression of which they regulate, contribute to the non-cell autonomous regulation of spinal interneuron development by the motor neurons. We are convinced that Onecut factors could regulate multiple independent factors and pathways involved in extrinsic regulation of interneuron development. This possibly also includes, as demonstrated in cell culture for multiple homeoproteins including human Onecut factors, the intercellular transfer of the Onecut homeoproteins during spinal cord development, a process that we are currently investigating. Knocking out both OC and Ntf3 in the motor neurons, beyond being technically extremely challenging (1/64 probability to obtain double-mutant embryos), would not enable to address this question, as it will simply results in the addition of two different defects.

      Also, a quantitative summary of the effects of Ntf3 overexpression in motor neurons in the chick is lacking.

      A quantitative summary of the effects of Ntf3 overexpression in the chicken embryonic spinal cord is provided in Figure S2.

      (2) How the authors assess changes in the spatial distribution of interneurons is unclear. In Figures 2 and 4, the control distributions (despite reporting the same populations in the same regions) look different, suggesting large sample-to-sample variance in distribution. Although the authors report that several sections in each level were taken from at least three animals for each condition, it's unclear how variance within WT or cKO sections was accounted for in the final statistical evaluation. It seems at a glance that a comparison between control samples in Figure 2 and Figure 4 could report statistically significant differences, which would be problematic. A more rigorous report of sample-to-sample variance and a more in-depth explanation of the statistical methods are needed.

      The experimental procedure to analyze the spatial distribution of spinal interneurons at different stages of development is described in details in the “Statistical analyses” paragraph of the Materials and Methods section of the manuscript, and has been repeatedly used by ourselves [1,2] and by others (see for example [3-5]) to conduct similar analyses.

      We also noticed that the distribution of the different analyzed interneuron populations in the control embryos showed some differences between the cOc1Oc2<sup>-/-</sup> and in the cNtf3<sup>-/-</sup> lines. Several parameters can account for this observation. First, this study has been conducted over a period of 15 years, different investigators each contributing to different steps of the analysis. Second, the genetic background of these two lines is not identical, impacting both the duration of the gestation (hence, the embryonic stage of the performed analyses, even if the embryos were collected on the same gestation day) and possibly the distribution of some interneuron populations. Third, because of evolutions in the availability of the primary antibodies used to label the interneuron populations of interest, the same antibodies were not used throughout the study, as stated for in the Materials and Methods section for Chx10, Gata3 and Sox1, although the same antibody was used by the same investigator to label the same interneuron population in each mouse line at each developmental stage.

      A detailed description of the number of sections and embryos included in each analysis as well as the whole statistical workflow that was used for the distribution analyses, which takes into account variance within control or mutant samples, is now provided in the revised version of the manuscript.

      Reviewer #2 (Public review):

      The study by Angla et al. proposes a model in which NT-3 produced by motor neurons regulates interneuron numbers and distribution in a non-cell autonomous manner. The authors demonstrate that ablation of motor neurons (MNs) and global and conditional deletion of OC transcription factors lead to changes in interneuron distribution. They identify that NT3 is upregulated after MN-specific OC deletion in RNA-seq experiments and show that olig2-cre mediated NT3 deletion leads to increased ventral interneuron numbers, altered distribution, and defects in locomotor behavior. The authors conclude that MN-derived NT3, under OC control, regulates interneuron development. While this is an intriguing hypothesis, additional experiments are needed to support it and strengthen the link between the different experiments described here.

      (1) The study primarily quantifies interneuron numbers and distribution at different levels of the spinal cord and under different genetic manipulations. Experimental details are lacking, defining how many sections were analyzed (several are noted in the methods) and how the rostrocaudal levels of the spinal cord were precisely aligned.

      A detailed description of the number of sections and embryos included in each analysis as well as the whole statistical workflow that was used for the distribution analyses is now provided in the revised version of the manuscript. The rostrocaudal levels of the spinal cord were precisely aligned using the distribution of Foxp1 in the Lateral Motor Columns (LMCs) at brachial or lumbar levels of the spinal cord, which is also indicated in the revised version.

      In different figures, the values and distributions shown for controls vary quite a lot. For example, in Figure 2B vs Figure 4B, the number of FoxP2+ V1 neurons at brachial levels is ~350 vs 125. Similarly, the control distributions in 2I and 4I are quite different. This makes it challenging to determine whether the conclusions regarding the impact of each genetic manipulation on interneuron numbers and distribution are valid.

      Several parameters can account for these observations. First, this study has been conducted over a period of 15 years, different investigators each contributing to different steps of the analysis. Second, the genetic background of these two lines is not identical, impacting both the duration of the gestation (hence, the embryonic stage of the performed analyses, even if the embryos were collected on the same gestation day) and possibly the distribution of some interneuron populations. Third, because of evolutions in the availability of the primary antibodies used to label the interneuron populations of interest, the same antibodies were not used throughout the study, as stated for in the Materials and Methods section for Chx10, Gata3 and Sox1, although the same antibody was used by the same investigator to label the same interneuron population in each mouse line at each developmental stage.

      (2) The relationship between OC and NT3 deletion data is not entirely clear. Both deletions presumably lead to changes in interneuron distribution, but is there any reverse relationship between the two that relates to relative changes in NT3 levels? The authors do not directly compare NT3 and OC KO IN distributions. Similarly, one might expect a decrease in interneuron numbers in OC mutants, which is only reported for V2c neurons. However, the image presented in Figure 2G shows an equal number of V2c INs in control and mutant.

      In this study, we did not intend to demonstrate that Onecut transcription factors exert their non-cell autonomous action on spinal interneuron development by regulating Ntf3 expression, and we do not state in the manuscript that this is the case. We only show that Onecut factors and Ntf3, the expression of which they regulate, contribute to the non-cell autonomous regulation of spinal interneuron development by the motor neurons. We are convinced that Onecut factors could regulate multiple independent factors and pathways involved in extrinsic regulation of interneuron development. For example, as mentioned above, we observed intercellular transfer of the Onecut homeoproteins during spinal cord development, suggesting different strategies for non-cell autonomous regulation of interneuron development. The two mouse lines studied here consist on the one side in a combination of OC inactivation and Ntf3 increased expression, and on the other side in Ntf3 inactivation. Therefore, a reverse relationship between the changes in interneuron distribution is not expected. Furthermore, gain-of-function and loss-of-function experiments in mouse models frequently generate phenotypes that are not inverse to each other.

      (3) It is not clear that the behavioral phenotypes seen in the olig2-cre mediated deletion of NT3 can be attributed to changes in interneuron development. How about a role of NT3 in oligodendrocytes? There is a big gap between the embryonic changes shown here and behavior, with no in-between circuit-level changes in locomotor circuits shown.

      We agree, the motor behavior changes that we recorded in Ntf3 conditional mutant mice are, as stated, “consistent with the hypothesis that Ntf3 produced by MNs is required to generate locomotor circuits with properly coordinated activity” but do not demonstrate a direct causal relationship. However, investigating the intrinsic activity of the spinal locomotor circuits, independently from, for example, oligodendrocyte contribution may prove to be extremely challenging and was beyond the scope of this study. In addition, to our best knowledge, Ntf3 has not been shown to be expressed in healthy oligodendrocytes in vivo, and TrkC has not been reported to be displayed by these cells in the same conditions.

      A more restricted manipulation would be deleting TrkC from specific interneuron populations. Related to this, although TrkC is shown to be broadly expressed in ventral interneurons, it is not shown specifically to colocalize with any of the interneuron markers. The authors should validate that the receptor is expressed in the subsets that they are investigating.

      We agree, investigating the consequences of inactivating the TrkC receptor in specific interneuron populations would be extremely informative. However, this experiment is also very challenging to perform, as most of the driver lines available to target spinal interneuron populations additionally target multiple neuronal populations outside of the spinal cord that are also involved in the control of movements and could therefore induce confounding effects on motor behavior analyses.

      We thank the reviewer for suggesting to investigate in more details the interneuron populations that display TrkC receptors, which is now included in the revised version of the manuscript (Figure 3E-G).

      (4) The rationale for following up on NT3 seems to be the chick electroporation experiments; however, no changes in distribution are shown in those experiments, and only a very minor decrease in Chx10 interneurons. Shouldn't NT3 overexpression lead to substantial decreases in IN numbers according to the authors' model? The "data not shown", which presumably refers to distribution, would be important to show here, to further support this rationale.

      Chicken spinal cord electroporation only enables to study spinal cord development for a few days, given the high mortality rate observed after longer incubation. At the stage we collected the electroporated embryos for analyses, interneuron migration has barely been initiated, and distribution cannot be studied yet. Consistently, we are not aware of any report of interneuron distribution analysis in electroporated chicken embryonic spinal cord, as compared to mouse embryos [1-5].

      (5) The idea that NT3 downregulation causes an increase in IN numbers is not intuitive. Also, considering the DTA experiments in Figure 1, showing that MN ablation leads to a decrease in several IN subtypes and no changes in V2a neurons. It would be helpful for the reader if the authors could synthesize their results in the discussion and reconcile their experimental findings.

      We agree, this has now been included in the Discussion section of the revised manuscript.

      Reviewer #3 (Public review):

      This manuscript aims to investigate cell extrinsic mechanisms that regulate the differentiation and distribution of interneuron types in the spinal cord. The authors demonstrate that the loss of motor neurons leads to changes in the number and distribution of different interneuron types, specifically V0v, V1, and V2b (but not V2a). The authors then hypothesize that this phenotype may be controlled by the action of Onecut (OC) transcription factors in motor neurons. Conditional knockout of OC1 + OC2 in motor neurons using Olig2-Cre, however, does not lead to significant changes in the numbers of V1, V2a, and V2b interneurons, although there is a change in their spatial distribution. While the authors do not check V0v neurons in OC mutants, they do check V2c, which show a reduction in number and change in distribution. Why the same neurons are not checked across experiments is unclear. The authors then analyze existing RNA-seq data to identify factors that could be mediating the effects of the OC factors in motor neurons. They identify Ntf3 as a candidate and confirm that it is upregulated in OC mutants. Conditional loss of function of Ntf3 (Olig2-Cre) leads to increases in V1, V2a, and V2b (but not V2c) interneurons and changes in the distribution of all four interneuron types. Finally, the authors demonstrate that these Ntf3 conditional mutants have major defects in motor function.

      The conclusions of this manuscript are not well supported by the data for the reasons listed below, making it difficult to assess the impact of this work on the field.

      (1) The manuscript relies heavily on quantifying numbers and the spatial distribution of interneuron populations. However, these do not seem to be consistent in control animals across experiments, making it difficult to interpret any changes observed in genetic manipulations. Specifically, in Figures 2 and 4, the same markers are being used to quantify V1, V2a, V2b, and V2c interneurons in controls vs. OC (Figure 2) or Ntf3 (Figure 4) conditional knockouts, but the numbers of neurons and their distribution in control animals are variable between these two figures. For example, there seems to be a mean of >300 V1 neurons in E12.5 brachial sections of Fig. 2 controls, but this number is <150 in Fig. 4 controls. The cell distribution scoring is similarly variable between these controls without any explanation. The same is true for E14.5 controls used in Figure S1 vs. Figure S3.

      We also noticed that quantifications and distributions of the different analyzed interneuron populations in the control embryos showed some differences between the cOc1Oc2<sup>-/-</sup> and in the cNtf3<sup>-/-</sup> lines. Several parameters can account for this observation. First, this study has been conducted over a period of 15 years, different investigators each contributing to different steps of the analysis. Therefore, the interneuron distribution analyses in these two mouse lines were not conducted by the same researchers. Second, the genetic background of these two lines is not identical, impacting both the duration of the gestation (hence, the embryonic stage of the performed analyses, even if the embryos were collected on the same gestation day) and possibly the distribution of some interneuron populations. Third, because of evolutions in the availability of the primary antibodies used to label the interneuron populations of interest, the same antibodies were not used throughout the study, as stated in the Materials and Methods section for Chx10, Gata3 and Sox1, although the same antibody was used by the same investigator to label the same interneuron population in each mouse line at each developmental stage.

      (2) Neurotrophic factors generally promote neuronal survival. However, in this study, the loss of Ntf3 leads to increased numbers of interneurons. This finding is in disagreement with previous observations in slice cultures of spinal cords, as stated in the discussion. This discrepancy makes it even more important that the cell counts reported in the figures discussed above are robust.

      Considering that neurotrophic factors only support neuronal survival would strongly neglect their important function in neuronal differentiation, which has been broadly demonstrated. Severe immunotoxic ablation of motor neurons or anti-serum blockade of Ntf3 activity severely depleted inhibitory, but not excitatory, interneurons in a highly apoptotic-prone organotypic culture model of embryonic rat spinal cord slices, which was rescued by Ntf3 in the first model [6]. Opposite results were obtained in vivo by other researchers using mouse models lacking almost all MNs due to the elimination of skeletal muscles, where the number of spinal INs remained unaffected [7,8]. Combined to our results, these in vivo observations suggest that Ntf-3 is involved in interneuron differentiation rather in their survival. Consistently, Ntf3 has been shown to promote neuronal differentiation [9].

      (3) The claim that phenotypes are non-cell autonomously driven by motor neurons is not well supported. In Olig2-Cre conditional knockouts of Onecut and Ntf3, there is no confirmation that the loss of these factors is specific to motor neurons. Therefore, it cannot be ruled out that other cell populations may be mediating the phenotypes.

      Combined conditional inactivation of Oc1 and Oc2 has been reported in [10]. Conditional inactivation of Ntf3 only impacts motor neurons as it is the only cell population in the ventral spinal cord wherein this factor is produced (this study and [11-13]). Furthermore, Olig2-Cre has been shown to be active in motor neurons and in V3 interneurons (see for example [14], which, for this reason, have not been studied in the frame of this project as stated in the manuscript.

      (4) The claim that interneuron development is regulated by OC control of Ntf3 expression in motor neurons is not well supported. The authors show that loss of OC1/2 leads to an increase in Ntf3 expression in motor neurons. If this pathway were controlling interneurons, loss of OC function and overexpression of Ntf3 would have the same phenotype, which is not the case. Additionally, it would also be expected that loss of OC function and loss of Ntf3 function would have inverse phenotypes, which is also not the case. The phenotypes from OC loss of function and Ntf3 loss of function seem distinct from one another. The authors state that too little and too much Ntf3 are both bad for interneuron development, but there is no data to support their claim that OC1/2 mutants have altered interneuron development because of higher Ntf3 expression.

      In this study, we did not intend to demonstrate that Onecut transcription factors exert their non-cell autonomous action on spinal interneuron development by regulating Ntf3 expression, and we do not state in the manuscript that this is the case. We only show that Onecut factors and Ntf3, the expression of which they regulate, contribute to the non-cell autonomous regulation of spinal interneuron development by the motor neurons. We are convinced that Onecut factors could regulate multiple independent factors and pathways involved in extrinsic regulation of interneuron development. This possibly also includes, as demonstrated in cell culture for multiple homeoproteins including human Onecut factors, the intercellular transfer of the Onecut homeoproteins during spinal cord development, a process that we are currently investigating.

      (5) It is not clear that interneurons being studied express the Ntf3 receptor TrkC, which makes it difficult to assess whether changes in Ntf3 signaling are directly responsible for the phenotype.

      We thank the reviewer for suggesting to investigate in more details the interneuron populations that display TrkC receptors, which is now included in the revised version of the manuscript (Figure 3E-G).

      (6) While the behavioral phenotypes are consistent with Ntf3 playing a role in motor circuits, there is no evidence to suggest that Ntf3's influence on premotor interneurons being studied is driving or contributing to this phenotype, as discussed by the authors.

      We agree, the motor behavior changes that we recorded in Ntf3 conditional mutant mice are, as stated, “consistent with the hypothesis that Ntf3 produced by MNs is required to generate locomotor circuits with properly coordinated activity” but do not demonstrate a direct causal relationship. However, investigating the intrinsic activity of the spinal locomotor circuits was beyond the scope of this study.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      (1) Figure 3: A more comprehensive overview of the RNA-seq results would be helpful to see how much gene expression is shifted as a result of OC loss (e.g., volcano plot, pathway enrichment analysis).

      We agree, this has now been added in Figures 3B and S3 of the revised manuscript.

      (2) Figure 2, 4: How does the spatial distribution of motor neurons change?

      Describing the distribution of motor neurons is highly challenging given that the expression of markers that are collectively required to label all the motor neuron subset, including Foxp1, Hb9 and most significantly Isl1, is altered when Onecut expression is modified. Furthermore, changes in motor neuron distribution could constitute consequences of alterations in pre-motor interneuron numbers or distributions. However, as far as we can observe, motor neuron distribution was not obviously modified in the studied mutants.

      (3) Figure S2: Why is Ntf3 expression so limited compared to Isl1-expressing motor neurons? An explanation would be helpful.

      As stated in the Material and Methods section and in the legend of Figure S4 of the revised manuscript, expression after chicken embryonic spinal cord electroporation is transient and maximal reporter gene expression, including GFP, can usually only be visualized 24h after electroporation, but not at later stages. Forty-height hours after electroporation, only residual expression can still be detected in a few targeted cells.

      Reviewer #3 (Recommendations for the authors):

      (1) Changes in interneuron numbers are attributed to defects in differentiation. However, the possibility that these could be caused by changes in cell death has not been ruled out.

      Absence of increased cell death had been demonstrated previously for Onecut mutant embryos [15] and has been verified now in conditional Ntf3 mutant embryos (Figure S5). Both information have been included in the text.

      (2) In Figures 2 and 4, it is unclear if the images of the spinal cords are from brachial, thoracic, or lumbar levels. As the three levels frequently show different phenotypes, it is difficult to match the immunostaining with the reported quantification.

      All the pictures show thoracic regions of the spinal cord, as now stated in the figure legends of the revised version of the manuscript.

      (3) Statistics are missing in the cell distribution plots in Figure S1.

      This is not the case in our version of the pdf file.

      (4) In experiments where motor neurons are eliminated with Olig2-Cre/DTA, the authors write that progenitors are not affected without showing data. These data should be included because i) Olig2 is expressed in progenitors, so it would be expected that motor neuron progenitors are lost or reduced in this mouse, and ii) showing no changes in progenitors is crucial to the claim that postmitotic motor neurons are affected interneuron populations.

      We agree, these data are now included as Figure S1 of the revised version of the manuscript.

      (1) Harris, A. et al. Onecut factors and Pou2f2 regulate the distribution of V2 interneurons in the mouse developing spinal cord. Front Cell Neurosci 13 (2019). https://doi.org/10.3389/fncel.2019.00184

      (2) Kabayiza, K. U. et al. The Onecut Transcription Factors Regulate Differentiation and Distribution of Dorsal Interneurons during Spinal Cord Development. Front Mol Neurosci 10, 157 (2017). https://doi.org/10.3389/fnmol.2017.00157

      (3) Deska-Gauthier, D. et al. Embryonic temporal-spatial delineation of excitatory spinal V3 interneuron diversity. Cell Rep 43, 113635 (2024). https://doi.org/10.1016/j.celrep.2023.113635

      (4) Bikoff, J. B. et al. Spinal Inhibitory Interneuron Diversity Delineates Variant Motor Microcircuits. Cell 165, 207–219 (2016). https://doi.org/10.1016/j.cell.2016.01.027

      (5) Hayashi, M. et al. Graded Arrays of Spinal and Supraspinal V2a Interneuron Subtypes Underlie Forelimb and Hindlimb Motor Control. Neuron 97, 869–884 e865 (2018). https://doi.org/10.1016/j.neuron.2018.01.023

      (6) Bechade, C., Mallecourt, C., Sedel, F., Vyas, S. & Triller, A. in J Neurosci Vol. 22 8779–8784 (2002).

      (7) Grieshammer, U., Lewandoski, M., Prevette, D., Oppenheim, R. W. & Martin, G. R. Muscle-specific cell ablation conditional upon Cre-mediated DNA recombination in transgenic mice leads to massive spinal and cranial motoneuron loss. Dev Biol 197, 234–247 (1998). https://doi.org/10.1006/dbio.1997.8859

      (8) Kablar, B. & Rudnicki, M. A. Development in the absence of skeletal muscle results in the sequential ablation of motor neurons from the spinal cord to the brain. Dev Biol 208, 93–109 (1999). https://doi.org/10.1006/dbio.1998.9184

      (9) Dutton, R., Yamada, T., Turnley, A., Bartlett, P. F. & Murphy, M. Regulation of spinal motoneuron differentiation by the combined action of Sonic hedgehog and neurotrophin 3. Clin Exp Pharmacol Physiol 26, 746–748 (1999). https://doi.org/10.1046/j.1440-1681.1999.03108.x

      (10) Toch, M. et al. Onecut-dependent Nkx6.2 transcription factor expression is required for proper formation and activity of spinal locomotor circuits. Sci Rep 10, 996 (2020). https://doi.org/10.1038/s41598-020-57945-4

      (11) Buck, C. R., Seburn, K. L. & Cope, T. C. Neurotrophin expression by spinal motoneurons in adult and developing rats. J Comp Neurol 416, 309–318 (2000). https://doi.org/10.1002/(sici)1096-9861(20000117)416:3<309::aid-cne3>3.0.co;2-u

      (12) Henderson, C. E. et al. Neurotrophins promote motor neuron survival and are present in embryonic limb bud. Nature 363, 266–270 (1993). https://doi.org/10.1038/363266a0

      (13) Usui, N. et al. Role of motoneuron-derived neurotrophin 3 in survival and axonal projection of sensory neurons during neural circuit formation. Development 139, 1125–1132 (2012). https://doi.org/10.1242/dev.069997

      (14) Debrulle, S. et al. Vsx1 and Chx10 paralogs sequentially secure V2 interneuron identity during spinal cord development. Cell Mol Life Sci 77, 4117–4131 (2020). https://doi.org/10.1007/s00018-019-03408-7

      (15) Roy, A. et al. Onecut transcription factors act upstream of Isl1 to regulate spinal motoneuron diversification. Development 139, 3109–3119 (2012). https://doi.org/10.1242/dev.078501

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public Review):

      In this study, the authors set out to investigate spatial RNA processing events, specifically alternative splicing and 3' UTR usage, in mouse brain and kidney tissues using ReadZS and SpliZ methodologies on spatial transcriptomics data. The research contributes to understanding tissue-specific gene expression regulation from a spatial perspective. The study introduces a novel approach for analyzing spatial transcriptomics data, allowing for the identification of RNA processing and regulation patterns directly from 10X Visium data. The authors present convincing evidence supporting the identification of novel RNA processing patterns using their methodology, which holds significant implications for researchers in the field of spatial transcriptomics and the study of alternative splicing and 3' UTR usage.

      Thank you for this thorough overview of our work.

      The conclusions of the study are mostly well-supported by the data; however, certain aspects could be improved to strengthen the findings.

      (1) The conclusions of this study would be strengthened by conducting a more extensive tissue sample analysis and including biological replicates. Additionally, appropriate batch effect corrections should be applied when dealing with biological replicates.

      We agree that including biological replicates would strengthen our findings. We have included biological replicates of the mouse brain tissues in the revision. See Figure 3-figure supplements 1, 3, and 5.

      (2) The 3' UTR usage and alternative splicing should be compared among clearly labeled clusters for a more comprehensive analysis.

      We understand that it can be difficult to see how the SpliZ quantiles map spatially onto the tissue images. For the splicing of Gng13, Myl6, and Rps24, We have included box plots broken down by spatial quadrant in the revision. However, this does result in an oversimplification of the spatial patterns found in the tissue slices, which make the plots less informative than the quantile plots to our view. See Figure 3—figure supplements 2, 4, and 6.

      (3) The authors should clarify their rationale for choosing ReadZS and SpliZ approaches and provide comparisons with other methods to demonstrate the advantages and potential limitations of their chosen methodologies.

      Thank you for pointing out the lack of sufficient discussion of ReadZS and SpliZ in the manuscript. The ReadZS and SpliZ were chosen for this analysis because both of these methods provide an individual score for each cell-gene pair, which is easily adapted to providing a score for each spot-gene pair. Due to the sparsity and 3’ bias of Visium data, approaches designed to analyze RNA processing in full-length sequencing analysis are not applicable. The SpliZ and ReadZS are two of the limited number of tools available that are designed for the analysis of RNA processing in droplet-based data. Other available tools tend to rely on aggregating data across multiple cells using a method called pseudo-bulking (Li et al., 2021; Patrick et al., 2020). It is not clear how this could be used for spatial transcriptomics data without potentially obscuring subtle spatial patterns in the data. Others are based on PSI measurements, which are vulnerable to artifacts due to sparsity (Buen Abad Najar et al., 2020; Olivieri et al., 2022; Wen et al., 2022). The tradeoff between pseudo-bulking and a single score per spot-gene pair means that the ReadZS and SpliZ do not have the power to detect changes for genes with very low read counts. We have added text in the revision to clarify this point. This explanation has now been added as the second paragraph in the “Results” section on page 2.

      Reviewer #2 (Public Review):

      The authors applied existing ReadZS and the SpliZ methods, previously developed to analyze RNA process in scRNA-seq data, to Visium data to study spatial splicing and RNA processing events in tissues by Moran's I. The authors showed several example genes in mouse brain and kidney, whose processing are spatially regulated, such as Rps24, Myl6, Gng13.

      Thank you for this thorough overview of our work.

      The paper touches on an important question in RNA biology about how RNA processing is regulated spatially. Both experimental and computational challenges remain to address it. Despite some potentially interesting findings, most claims remain to be validated by orthogonal methods such as RNA FISH and simulations.

      We appreciate that the reviewer finds the question important, and that the findings are potentially interesting. In the revision, we have included biological replicates for our findings in the mouse brain. See Figure 3—figure supplements 1, 3, and 5. Unfortunately, experimental validation is outside of our budget for this project. It is unclear what further simulations could validate the biological discoveries in this manuscript: permutations were used to calculate the p-value of each discovery, and the false positive and negative rates of the SpliZ have been assessed through simulation (Olivieri et al., 2022).

      In addition, the percentage of spatial processing events (splicing in 0.8-2.2% of detected genes, i.e. 8-17 genes and RNA processing in 1.1-5.5% of detected genomic windows, i.e. 57-161 windows) discovered is low. Does it suggest that most of RNA processing events were not spatially regulated across the tissue? Or does it question the assumption of treating spatial transcriptomics data similar to scRNA-seq data?

      We agree that the question of the prevalence of spatial RNA processing regulation is critical. Rather than the two options proposed here, we believe that the sparsity of the data limits our ability to call more of these events. In the revision, we have provided a supplemental figure showing the relationship between read depth and p-value for each gene to quantify how the fraction of observed regulation changes with sequencing depth. It is worth noting that as these technologies improve, we expect the sequencing depth of spatial technologies to increase which would likely result in more discoveries.

      The unique features for ST data, such as mixture of neighboring cells, different capture biases and much smaller number of spots (pseudo cells here), may have significant effects on the power of scRNA-seq based methods, but it is not discussed in the manuscript. The lack of careful evaluation and low discovery rates could limit application of the approach to other tissues and subcellular data.

      We appreciate the concern that technical differences between scRNA-seq data and spatial transcriptomics data could affect our results. We agree that this point could be addressed more thoroughly in the text. None of the specificities of spatial transcriptomics data invalidate the assumptions of the SpliZ or ReadZS. The method we use to identify genes with significant spatial regulation of RNA processing was specifically created to be used for Visium data. It takes into account mixture of RNAs in neighboring cells by randomly sampling scores of neighboring cells, rather than randomization of the location of the spots themselves, which does indeed result in a high false positive rate (see “Permutations for Moran’s I” in the Methods). Text was added to clarify this point in the first paragraph of the “Results” section on page 2. We do note that there is a limit to the power of this kind of analysis based on the number of spots and the read depth, which we have to quantify in a plot in the revision.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      (1) To strengthen the study's conclusions and broaden its impact, consider analyzing additional tissue types and incorporating biological replicates. This would provide a more comprehensive view of the spatially regulated RNA processing events in various tissues. Apply appropriate batch effect corrections when including biological replicates for ReadZS and Spliz Scores.

      We have included biological replicates for mouse brain tissue sections in the revision. Because the SpliZ is calculated separately for each sample and the score is relative, this serves as appropriate batch correction. See Figure 3—figure supplements 1, 3, and 5.

      (2) Provide a clearer rationale for choosing the ReadZS and SpliZ approaches and compare their performance with other existing methods in the field. This would help to establish the advantages and potential limitations of your chosen approaches.

      This explanation has now been added as the second paragraph in the “Results” section on page 2.

      (3) In Figure 3 and 4, it would be beneficial to provide separate density and box plots for each tissue region within the brain and kidney instead of quantiles. This will allow for clearer visualization and comparison of the data across different regions, enhancing the interpretation of the results.

      We have included separate box plots for each quadrant of the tissue region for the SpliZ data in the revision. See Figure 3—figure supplements 2, 4, and 6.

      (4) In Figure 2, please clarify the rationale behind choosing different Moran I value thresholds for SpliZ and ReadZS.

      Thank you for pointing out this lack of sufficient documentation here. To clarify, the significance thresholds are the same for each figure. The thresholds indicated in the caption just specify which gene labels were shown on the plot itself. These thresholds were chosen so that the plot would not be overly clogged with gene names, while still allowing the “most significant” gene names for each analysis to be easily distinguished. This clarification has been made in the Figure 2 caption on page 6.

      Reviewer #2 (Recommendations for the authors):

      (1) An overview of the proposed pipelines to analyze ST data in Fig 1 could be helpful.

      We agree that this would be a useful addition to the manuscript, we have included a pipeline figure in the revised manuscript. This has now been added to Figure 1.

      (2) Fig 2A most left panel: The label "mouse brain kidney" needs correction

      Thank you for pointing this out, this has been fixed.

      (3) It could be helpful to include a discussion on the limitation of integrating SpliZ and ReadZS for analyzing ST data. Do they apply only to 3' UTR regions or across gene body regions? What are the requirements for reads? Are there any features for genes that are called in scRNA-seq data but not in Visium?

      Thank you for pointing out the lack of detail on this point. Both the SpliZ and the ReadZS take into account reads throughout the gene body (though of course this is limited by the 3’ bias of the data). Different biases of read coverage between technologies do not affect the applicability of the SpliZ and the ReadZS, because both are calculated only relative to the reads found in the particular sample. We have included a discussion of these details in the second paragraph of the “Results” section on page 2.

      References

      Buen Abad Najar, C. F., Yosef, N., & Lareau, L. F. (2020). Coverage-dependent bias creates the appearance of binary splicing in single cells. ELife, 9, e54603. https://doi.org/10.7554/eLife.54603

      Li, W. V., Zheng, D., Wang, R., & Tian, B. (2021). MAAPER: Model-based analysis of alternative polyadenylation using 3′ end-linked reads. Genome Biology, 22(1), 222. https://doi.org/10.1186/s13059-021-02429-5

      Olivieri, J. E., Dehghannasiri, R., & Salzman, J. (2022). The SpliZ generalizes ‘percent spliced in’to reveal regulated splicing at single-cell resolution. Nature Methods, 19(3), 307–310.

      Patrick, R., Humphreys, D. T., Janbandhu, V., Oshlack, A., Ho, J. W. K., Harvey, R. P., & Lo, K. K. (2020). Sierra: Discovery of differential transcript usage from polyA-captured single-cell RNA-seq data. Genome Biology, 21(1), 167. https://doi.org/10.1186/s13059-020-02071-7

      Wen, W. X., Mead, A. J., & Thongjuea, S. (2022). MARVEL: An integrated alternative splicing analysis platform for single-cell RNA sequencing data (p. 2022.08.25.505258). bioRxiv. https://doi.org/10.1101/2022.08.25.505258

    1. Author response:

      The following is the authors’ response to the original reviews.

      Reviewer #1 (Public review):

      Summary:

      The authors present a novel approach to subcellular spatial proteomics by combining laser microdissection with expansion microscopy and LC-MS/MS analysis (SPEx). They implement two different workflows for LMD and LC-MS/MS quantification:

      (1)The standard approach, where an area of interest is cut out by LMD, subjected to proteomics analysis, and compared to the rest of the cell without the dissected ROI.

      (2) The subtraction approach, where ROIs are removed, and the remaining cellular material is compared to samples containing both the surrounding material and the ROI.

      The authors assess the technique by applying it to subcellular targets of various sizes, volumes, and protein compositions such as the nucleus, nucleoli, and Golgi. They demonstrate that SPEx can identify proteins enriched or reduced in ROIs.

      Strengths:

      The broad, relatively easy, and inexpensive applicability of this approach to potentially many cell types and subcellular areas of interest provides an exciting alternative to subcellular fractionation, native immunoprecipitation, or genetically encoded proximity labeling constructs. Moreover, by visually selecting ROIs for subsequent analysis, subcellular context or organelle morphology can be taken into account, as discussed by the authors in the discussion section.

      Weaknesses:

      While strongly supporting the sharing of this approach, we have a number of comments and questions that will improve the impact of the manuscript:

      We thank the reviewer for the careful evaluation of our manuscript and the generally positive assessment.

      (1) General:

      (a) The manuscript would benefit from restructuring and language revision. In its current form, the writing is sometimes dense and verbose (in particular, the Results section). This makes it difficult to follow the authors' arguments.

      We improved readability and clarity in the revised manuscript. We added subheadings to facilitate reading.

      (b) The authors mention the possibility of selecting organelles based on morphology. This is left for the discussion, but it seems like a missed opportunity - the authors could compare individual organelles in different morphological states, e.g., connected vs. fragmented mitochondria.

      The authors agree with the reviewers’ assessment that investigating proteome of organelles based on morphology or cellular state is an exciting application of SPEx. While we plan experiments along this line in the future, we think that these experiments are beyond the scope of this manuscript, which is meant to describe the method and its general usefulness.

      (2) Technical:

      (a) Why do the authors strive and optimize for a 10x expansion factor? Is SPEx compatible with a more standard 4x expansion, as e.g., used in the classic U-ExM approach (https://www.nature.com/articles/s41592-018-0238-1)? This could be added to the discussion.

      We aimed for 10x expansion solely because our ultimate goal is to cut out very small structures. 10x expansion results in a 100x increase in area, while in U-ExM the area increase would only by 16x. Thus, this makes a huge difference for small structures such as nucleoli. We did not assess the compatibility with U-ExM. Still, we performed pilots with just 4x expansion (using TREx) in the early stages of optimization. We were able to isolate single cells and obtain similar protein coverage as with 10x expansion. We further clarified our motivation to use 10x expansion in the discussion.

      (b) The U-ExM approach shows improved ultrastructural preservation when using 3%FA with 0.1% glutaraldehyde fixation (GA). Is SPEx compatible with the use of low amounts of GA for fixation?

      We tried different fixation methods in the early stages of this study (where expansion was not yet close to 10x). We saw a mild negative effect of GA on the expansion factor, so we avoided it in the later experiments since it also did not seem necessary to preserve the structure of our organelles of interest. However, the use of GA would generally be compatible with SPEx, potentially at the cost of a mild negative effect on expansion factor (see Author response image 1) and proteome coverage. We discussed the use of GA in the discussion section.

      Author response image 1.

      Fixation methods mini-screen. Cells were fixed with the indicated reagents for 10 minutes at 37°C. After TREx expansion, the diameter of the nucleus was measured (A) and the resulting expansion factor compared to the non-expanded control was determined (B).

      Related to the above, was the anchoring efficiency reduced only to achieve a 10x expansion factor or does this additionally affect the proteome coverage?

      We solely lowered the anchoring to increase expansion factors. In earlier pilots we performed proteomic analysis on samples that were just expanded 4x using standard TREx expansion (also using the original anchoring strategy from the TREx publication, consisting of 0.2 mg/ml AcX for overnight at RT). We presented the results of this pilot in Fig S1A. We still detected over 2,000 proteins from 10 cells, a coverage, which is highly similar to what we found in the final experiments (Figure 2F), in which the anchoring was lower for 10x expansion. Based on these data, we think that anchoring (and expansion factor!) has a negligible impact on protein coverage. We clarified this point in the manuscript.

      (d) Have the authors considered using alternative anchoring approaches, such as GMA (https://journals.plos.org/plosone/article?id=10.1371/journal.pone.0291506#pone.0291506.s001), which potentially increase the amount of sample retained in the hydrogel, thus allowing for better proteome coverage? This could be added to the discussion.

      We did not use alternative anchoring approaches. We modified the TREx protocol to fit our purposes and since this was sufficient, we did not explore alternatives. However, using anchoring approaches, in which higher amounts of sample could be retained in the gel might be beneficial for the proteomics coverage. We will keep this suggestion in mind for future experiments. Thank you for the suggestion!

      (e) The limitation of the approach to near-2D samples should be mentioned, and alternative approaches for more 3D samples could be discussed.

      The authors agree that SPEx is limited to near-2D samples at this point. We suggest that SPEx is applicable for 3D samples (e.g. in tissues) by performing cryosectioning. TREx has been shown to be compatible with sectioned tissue (Damstra et al., 2022). We discuss this point in the discussion.

      (f) How are peptides that are directly anchored to the hydrogel dealt with during LC-MS/MS analysis? Are they excluded, or can they be identified during the spectral search? The latter would allow us to get a deeper structural understanding of how proteins are actually anchored into hydrogels, which so far has not been assessed.

      The reviewer raises an interesting point. In general, peptides carrying the anchoring modification are analysed by LC-MS, but we did not include these specific modifications in the database search. Overall, we assumed that the labeling would be low and stochastic and hence should, if at all, only minimally affect the detection of peptides. Nevertheless, in response to the reviewers’ comment, we searched the MS data again for the crosslinking reagent linked to lysine residues. However, we could not get any confident hit for any peptide containing this modification. Since we cannot exclude that the modification precludes the identification of the corresponding peptides, we compared the number peptides generated by trypsin cleavage after arginine and lysine. As the human genome contains similar proportions of both amino acids, one would expect similar numbers for both peptide types being identified. Any modifications of lysine by the anchoring reagent, would prevent tryptic cleavage and thus reduce the number of lysine peptides. As shown in Figure S1C, the number of lysine-terminating is only slightly lower compared to arginine-terminating peptides. Notably, the proteomics results of a different fixed human tissue sample directly extracted by laser capture micro dissection without expansion showed a very similar lysine-to-arginine peptide ratio. This indicates that the large majority of lysine residues is not modified and affected by the hydrogel anchoring. We included these data into the manuscript.

      An alternative approach to address this question would be to investigate if the peptide coverage of proteins detected by SPEx is enriched for peptides representing the folded core of proteins as opposed to the surface-exposed regions, which likely get more anchored into the hydrogel.

      Because of the negligible amounts of modified peptides, we did not investigate this potential bias of surface-exposed versus folded-core peptides.

      (g) Same question regarding peptides with NHS labeling. Can they be identified, or do they just compete for ionization and thus negatively affect coverage and dynamic range of the LC-MS/MS approach?

      The reviewer raises a similar point as above for another lysine labeling used during the SPEx protocol. Again, we specifically looked for this modification by re-searching the raw MS data, but still could not identify any peptides, carrying this modification on a lysine residue. Even though we cannot exclude that this rather large modification prevents detection, considering the high number of lysine-terminating peptides in our dataset (see Figure S1 C), we would expect that also this labeling step is stochastic and affects only a minor proportion of the proteins. We discuss the potential NHS labeling in the manuscript.

      (h) How are the primary and secondary antibodies affecting the proteomics analysis identified as contaminants?

      We thank the reviewer for this comment. Since antibodies bind to proteins in a non-covalent manner, they will be released during the denaturing steps of the protocol. Of course, the antibodies will stay in the sample, be digested and analyzed and could, if very abundant, affect the analysis of the proteins from the samples. To check this possibility, we re-searched the MS data including the sequences of the antibodies used. To our surprise, we could not detect any peptides of these antibodies. This suggests that the concentrations of the antibodies used are much lower than those of the sample proteins and thus should not have any impact on the proteomics results. We interpret this result also as a benefit of our method compared to organellar-IP.

      (i) Have the authors observed differences in proteomics coverage of only antibody vs NHS-labeling? Depending on the questions above, could pure antibody-based labeling increase proteomic coverage?

      We did not perform this comparative analysis, since we always used NHS dyes. In the experiments presented in this manuscript, NHS dyes allowed easy visualization of the whole cell without the use of antibodies. This NHS staining was essential for this particular setup for sample acquisition. We cut out entire cells, cells lacking the nucleus and cells lacking the Golgi apparatus, which served as critical controls. However, other ways of detecting cell boundaries could be used to avoid NHS staining. As shown above, both, the anchor and NHS labeling are likewise sparse and stochastic. Moreover, we could not detect any impact of the antibody labeling to our results. Thus, we assume that both labeling procedures could be used.

      Reviewer #1 (Recommendations for the authors):

      (1) Introduce the aberration PPS-membrane.

      We apologize for the omission and now explain the PPS abbreviation.

      (2) Please state which cells are used already in the first section "Development of the SPEx method" as opposed to only further down in the manuscript.

      We apologize for the omission, which has been fixed.

      (3) In Figures 2D and E, the authors should also show the hydrated expansion factors for better comparison.

      We agree that the inclusion of the hydrated expanded gels allows for better comparison. These data are now included in the manuscript.

      Reviewer #2 (Public review):

      Summary:

      This study introduces a method that combines physical expansion of cells, imaging-guided isolation of defined regions, and protein identification to enable compartment-resolved analysis of protein composition at the subcellular scale. The authors aim to address a central limitation in existing approaches, namely the loss of spatial information during sample preparation or the indirect nature of proximity-based labeling methods. Using several cellular compartments as examples, they demonstrate that their approach can recover compartment-enriched protein sets and identify candidate proteins with previously unassigned localization.

      Strengths:

      A major strength of this work is the conceptual simplicity and accessibility of the approach. By combining established techniques in a modular way, the method avoids the need for genetic manipulation or specialized labeling strategies, making it broadly adaptable across experimental systems. The ability to directly select regions of interest based on imaging represents a clear advantage over indirect enrichment strategies and allows flexible targeting of both membrane-bound and non-membrane-bound compartments.

      The experimental design is also a strong aspect of the study. The use of complementary comparison strategies-analyzing isolated compartments alongside matched "subtracted" controls-provides an internal framework for assessing enrichment and depletion, increasing confidence in spatial assignment. The application of the method across multiple organelles of different sizes and properties demonstrates versatility, and the reported specificity for several compartments is encouraging. In particular, the ability to profile small and biochemically challenging structures highlights a potentially important niche for the approach.

      Weaknesses:

      Despite these strengths, several methodological limitations constrain the interpretation of the results. The most important relates to spatial accuracy in three dimensions. While lateral resolution is improved through physical expansion, the lack of depth resolution introduces uncertainty regarding contributions from structures above and below the selected region. Although the authors argue that this does not substantially affect specificity, the current evidence is largely indirect, and a more rigorous quantification of potential contamination would strengthen this conclusion.

      Quantitative interpretation also remains challenging. Because the measurements reflect total protein abundance rather than local concentration, differences in compartment size and protein density can influence enrichment values, particularly for small structures embedded within larger volumes. This issue is evident in the analysis of smaller compartments and complicates direct comparison across conditions. Additional normalization or modeling would help clarify how to interpret these measurements.

      Another limitation concerns variability in the expansion process and its downstream consequences. Differences in expansion factor across samples may affect the definition of regions of interest and introduce variability in sampling, yet the impact of this variability is not fully explored. Similarly, the use of a modified chemical treatment to preserve proteins for downstream analysis is central to the workflow but is not extensively validated with respect to preservation of spatial organization.

      While the identification of previously unannotated proteins is an appealing aspect of the study, validation is limited to a small number of examples, and broader support from independent datasets or literature context is lacking. In addition, the study primarily focuses on steady-state measurements in a single cell type, and therefore does not yet demonstrate the ability of the method to capture dynamic or condition-dependent changes in protein localization.

      Finally, the positioning of the method relative to existing approaches could be more clearly articulated. Although qualitative comparisons are provided, a more systematic and quantitative benchmarking against alternative strategies would help readers better understand the specific advantages and trade-offs.

      We thank the reviewer for the careful evaluation of the manuscript and for the constructive feedback. The reviewer raises valid points, which we addressed in the revised manuscript.

      Reviewer #2 (Recommendations for the authors):

      Additional experiments and analyses

      (1) To strengthen confidence in the spatial specificity of the method, the authors should include experiments or analyses that directly estimate potential cross-compartment contamination. For example, using markers that are known to localize to mutually exclusive cellular regions would allow an empirical assessment of signal carryover. Alternatively, a computational or geometric model could be used to estimate how much material from adjacent regions is expected to contribute to the sampled proteome, given the loss of depth information.

      We agree with the reviewer’s concern regarding spatial resolution and potential contaminations resulting from it. We had the same concerns. We have obviously no resolution in z and we detected about 700 proteins (Fig. 5F) in our all samples, likely representing proteins residing above and below of (and potentially next to) the structures we cut out. To overcome this issue, we always compare the proteome of the structure of interest with an appropriate control. We also determined that mitochondria proteins are specifically omitted from our nuclear samples. Moreover, we provide evidence that our analysis methods can be used also to determine proteins that are specifically lost from a structure. Omitting the comparative approach would clearly result in very low specificity and a high number of false positives. However, we argue that comparison to a control largely removes these unspecific contaminations and we think that this is illustrated by our excellent specificity. Nevertheless, to address these concerns further, we have determined the masses of all quantified proteins using iBAQ values. We then summed the masses of all proteins being annotated to a specific organelle and calculated the percentage to the summed masses of all quantified proteins. As expected, we found that in our excised nuclei samples, 75.5% of the protein molecules originate from the nucleus and only 24.5% of protein mass was derived from other regions. Likewise, we found 84.7% of the protein mass in the excised Golgi samples annotated with Golgi or extracellular by GO. This analysis revealed that we detect an expected amount of contaminant proteins derived from other compartments due to the lack of resolution in z, but most of protein mass excised is already organelle-specific. The additional quantification step further enhances assignment accuracy, boosting the overall specificity of our approach. In the case of the nucleoli the mass contribution from known nucleoli proteins is significantly lower (~4%), which would be expected for a structure that only covers a fraction of the cell in z-direction. In the case of such small targets comparison to a fitting control is therefore essential. We added this analysis to the revised version of the manuscript and discuss it in detail (see “SPEx is best used as a comparative approach”). We thank the reviewer for bringing this up!

      (2) Given that drying results in compression along the vertical axis while largely preserving the lateral dimensions, it would be valuable to provide a quantitative analysis of how this affects spatial accuracy. This could include comparing marker distributions before and after drying or examining signal distribution across depth.

      Even though we were unable to image a particular cell before and after drying (due to the physical properties of the gels and the change in size during drying), we did so for the bulk of cells. We did not observe discernible morphological alterations after drying. The investigated structures (Golgi, nucleus and nucleoli) still looked morphologically similar to expanded cells (before drying) and non-expanded cells. We cannot exclude that the drying process introduced minor distortions of the sample. We would like to point out, however, that our focus is mainly on the spatial proteomics and to a lesser extent on the perfect conservation of the ultrastructure during drying. As long as we can maintain very good spatial separation and are able to cut out individual structures, our method should work just fine.

      In addition, trimming or sectioning the expanded samples along the z-axis prior to microdissection could help minimize contributions from structures above and below the region of interest, thereby improving spatial specificity.

      We tried to cut expanded samples (monolayer of cells) with a microtome prior to laser dissection. This approach did unfortunately not work. Mounting a monolayer of cells for microtome cutting is non-trivial!  The very thin monolayer of cells would need to be perfectly aligned with the plane where the cryo-sectioning takes place. Moreover, the different densities of the hydrogel without cells and the expanded cells in the same hydrogel appeared to be particular challenging during sectioning. Therefore, we gave up on this approach for monolayers. For a monolayer of cells, the contamination in the lateral dimension seems to be small enough so it can be eliminated by comparing the sample to appropriate controls, preventing the need for cryo-sectioning. We do think, however, that cryo-sectioning should be feasible for tissues since the combination of cryo-sectioning and TREx expansion in tissues has been described previously (Damstra et al., 2022).

      (3) Because the method relies on imaging-guided spatial dissection of a three-dimensional structure, further validation of spatial precision would strengthen the manuscript. Applying z-stack trimming to reduce depth-related ambiguity and comparing results obtained with more conservative and spatially restricted cutting boundaries would help determine how sensitive the proteomic output is to segmentation strategy and provide a clearer assessment of robustness.

      As pointed out above, we were unable to perform trimming in z. Therefore, the proposed analysis cannot be performed.

      (4) The use of SDS-based denaturation instead of protease digestion represents a key methodological deviation from conventional expansion workflows and is central to enabling downstream proteomic analysis. The authors should provide additional validation demonstrating that this approach preserves spatial fidelity without introducing distortion or bias in protein localization.

      We respectfully disagree with the reviewer. SDS denaturation was used previously in both the TREx and the U-ExM protocols (Damstra et al., 2022; Gambarotto et al., 2021). The preservation of ultrastructure has been established in both studies. Still, as pointed out by the reviewer, protease digestion is frequently used in ExM, likely because it minimizes distortion of the sample by eliminating any mechanical resistance to expansion. We omitted protease treatment to be able to perform LC-MS/MS. Protease treatment would likely reduce the amounts of peptides we would be able to detect. However, with the extended SDS denaturation, we were able to maintain excellent expansion even in the absence of protease treatment.

      (5) The manuscript reports variability in expansion factors across conditions, and it would be important to more clearly establish reproducibility. The authors should quantify variability across biological replicates and discuss how differences in expansion factor influence region-of-interest selection, spatial resolution, and downstream quantitative analysis.

      We were surprised that this reviewer thinks that we have variability in the expansion factors across conditions. In fact, the expansion is rather reproducible, and we only observe very minor variability in expansion factors between samples. The minor differences in expansion factor are unlikely to affect sampling because sampling happens manually and differences in the size of an organelle are accounted for by just adjusting the size of the isolated ROI. Even if we would have some discernible difference in the expansion factor between samples, this would not matter. The organelle of interest is cut out from the same cell, which will be subsequently used as control. Each sample subjected to LC-MS/MS contained at least 10 individually cut-out objects, further eliminating variability potentially introduced by minor changes in expansion levels.

      (6) The authors should also address how differences in compartment size and protein density influence quantitative interpretation. Because proteomic measurements reflect total protein abundance rather than local concentration, smaller compartments may be underrepresented. Incorporating normalization strategies or simulations would help clarify how enrichment values should be interpreted across compartments.

      We agree with the reviewer that comparison of structures of very different sizes might be technically difficult and that in such cases, controls should be collected in a similar size range to the actually studied compartments. We have implemented this change already in our workflow and mention this consideration in the discussion.

      Regarding normalization, we employed median normalization to our proteomics data abundances which controls for different sample amounts and eventually results in a comparison of protein concentration rather than pure protein abundances. This approach eliminates any knowledge of cell or organelle size and allows a more uniform comparison. We do agree, however, with the reviewer that for differential proteomics analysis, regions of interest should be preferable of the similar size and protein amount to avoid normalization biases. We discussed this point in the revised manuscript.

      (7) Validation of newly identified compartment-associated proteins should be expanded. In particular, the interpretation of proteins such as C7orf50 and SPOUT1 would benefit from deeper contextual discussion, including whether prior studies have reported alternative localizations under different cellular conditions and whether their localization may be cell-type-specific or context-dependent.

      We agree that more contextual discussion of the newly localized proteins will benefit the manuscript. We added more information about the newly identified proteins to the results section.

      (8) To support broader claims about the utility of the method, the authors should consider demonstrating that the approach can capture biologically meaningful, context-dependent changes in protein localization. For example, comparing different cell types or applying defined perturbations such as stress or apoptosis would help establish the ability of the method to resolve dynamic intracellular remodeling.  

      The authors agree with the reviewers’ assessment that studying context-dependent changes at a subcellular level is an exciting idea to explore. While we are currently planning such experiments, we think that these experiments are beyond the scope of this manuscript, which is meant to describe the method and its general usefulness.

      (9) The manuscript would benefit from a more direct and quantitative comparison with existing spatial proteomics approaches. In particular, benchmarking against proximity labeling methods would help clarify relative performance in terms of specificity and false positive rates, and comparison with published datasets could provide an objective frame of reference.

      We are a bit puzzled by the reviewer’s request. We already compared SPEx to a number of established spatial proteomics methods in the paper (Figure S1I-J, Figure S2F-G, Figure 5F-G) and discuss coverage and specificity. However, we expanded this comparison further to methods using Exm combined with LMD in the new manuscript (see below).

      (10) In addition, the positioning of the method relative to other expansion-based spatial proteomics approaches remains insufficiently defined. The authors are encouraged to include a structured comparison, ideally in the form of a summary table, outlining key parameters such as sampling strategy, spatial resolution, proteome depth, spatial specificity, throughput, and limitations. This would help clearly delineate the unique contributions of the approach within the broader methodological landscape.

      Peer reviewer’s request, we added a table (S15) on spatial proteomics methods combining expansion microscopy with manual or laser dissection and also provide information about lateral resolution, sampling strategy, proteome coverage, advantages and limitations.

      Writing and presentation

      (1) The presentation of expansion-related measurements would benefit from clearer organization. Currently, expansion factors from non-dried and dried samples are presented in separate figures, which may create redundancy and confusion. Reorganizing these data to directly compare pre- and post-drying conditions, or moving non-essential measurements to supplementary material, would improve clarity.

      We now also show the hydrated expansion factors in Figure 2C-D for comparison.

      (2) The method used for quantifying expansion should be described more explicitly. It should be clarified whether the same structures were tracked before and after expansion or whether independent samples were used, particularly for nuclei, which vary in size.

      We use the nucleus because this also used by other groups in the field (Liffner et al., 2024). The tracked structures are from independent samples. Thus, we average over a number of structures and calculate the expansion factor based on the mean diameter. We made this clearer in the manuscript.

      (3) Additional clarification is needed regarding the fluorescent labeling strategy. The rationale for using different dyes across experiments should be explained to distinguish whether these choices are driven by technical constraints, experimental design, or visualization preferences.

      We agree with the reviewer that the manuscript will profit from a more in-depth discussion of the labeling strategy. The structure of interest was always labeled in red because in our hands more red-shifted dyes are more resistant to drying than e.g. green dyes. We added this information to the manuscript.

      (4) Several figure legends and result descriptions would benefit from revision for clarity and completeness. In particular, complex panels such as intersection analyses should be more fully explained to ensure accessibility to readers.

      We agree with the reviewer’s assessment. The intersection analysis and the PCA, which represent the most complex panels in the manuscript, are now more clearly described in the legends.

      (5) The authors should also improve clarity in describing structural changes associated with drying. Including representative images of gels before and after drying would help illustrate the preservation of lateral dimensions and compression along the vertical axis.

      We agree that this addition would improve the manuscript. We included the images as Figure S1B. The gel post-drying is outlined by black dots because the gels become very thin and near-invisible post-drying.

      Minor corrections

      (1) Minor issues should be addressed to improve consistency and readability. These include correcting figure cross-references, standardizing statistical notation throughout the manuscript, and resolving typographical inconsistencies.

      Done.

      (2) Specific figure-related issues should also be addressed, including clarifying mislabeled figure references and improving color schemes in plots where group distinctions are currently difficult to interpret.

      Done.

      Data and reproducibility

      (1) The authors should ensure that all datasets and analysis workflows are fully accessible and sufficiently documented to enable reproducibility. This includes providing raw and processed proteomics data, as well as detailed descriptions of analysis pipelines and parameter settings.

      Raw proteomics data for all experiments will be publicly available upon publication of the final version and workflows are described in a detailed manner. To improve reproducibility, we also included a step-by-step explanation of the assembly of the gelation chamber, which represents the handling-wise most challenging step of the protocol, in Figure S3D.

      Reviewer #3 (Public review):

      Franziscus et al. describe an elegant approach for spatially specific proteome analysis. To achieve this, they expand fixed cells and subsequently use a laser to micro-dissect a region of interest, which is then analyzed by mass spectrometry.

      They demonstrate the effectiveness of their approach by analyzing the nucleus, nucleolus, and the Golgi, and benchmark their hits against previous datasets for these organelles.

      The manuscript is very well written and nicely guides the reader through the applied methods. The presented data is convincing, and I do not see the need for additional experimental verification of the protocol. The only minor concern is the novelty of the method and the presentation. A combination of expansion, laser microdissection, and proteomics has been applied in the past (PMID: 36450705, PMID: 39477916). In the manuscript, one of these studies is cited, though it does not become clear that this approach is already described. However, Franziscus et al. describe the approach better and make it more accessible to the reader, especially since the other studies described this methodology in combination with tissue expansion and not in combination with single cell expansion as it is done here. I would ask the authors to be clearer in the introduction about what others have already done and what their contribution is here. In general, I am convinced that the community will benefit from the presented protocol to analyze organelle proteomics in detail.

      We thank the reviewer for the careful evaluation of our manuscript and overwhelmingly positive assessment. We apologize for the omission of the mentioned citations, which are now included in the manuscript together with a direct comparison with the mentioned methods (Table S15).

      References

      Damstra HG, Mohar B, Eddison M, Akhmanova A, Kapitein LC, Tillberg PW. 2022. Visualizing cellular and tissue ultrastructure using Ten-fold Robust Expansion Microscopy (TREx). eLife 11:e73775. DOI: https://doi.org/10.7554/eLife.73775

      Gambarotto D, Hamel V, Guichard P. 2021. Ultrastructure expansion microscopy (U-ExM). Methods in Cell Biology 161:57–81. DOI: https://doi.org/10.1016/bs.mcb.2020.05.006, PMID: 33478697

      Liffner B, Silva TLA e., Vega-Rodriguez J, Absalon S. 2024. Mosquito Tissue Ultrastructure-Expansion Microscopy (MoTissU-ExM) enables ultrastructural and anatomical analysis of malaria parasites and their mosquito. BMC Methods 1:13. DOI: https://doi.org/10.1186/s44330-024-00013-4

    1. Author response:

      The following is the authors’ response to the original reviews.

      eLife Assessment:

      This important study identifies and characterizes a set of amino acid states that can rescue protein function in the presence of substantially deleterious mutations. Some of these super-compensatory substitutions also confer substantial mutational robustness, with broader implications for understanding epistasis, protein evolution, and protein engineering. The evidence is convincing, supported by a creative reanalysis of a large deep-mutational-scanning dataset, statistically rigorous treatment of anticipated error rates, experimental validation, and analyses of additional proteins, although clearer presentation and deeper investigation of the evolutionary implications and structural mechanisms would further strengthen the study.

      We sincerely thank the Reviewing Editor, the Senior Editor, and the three reviewers for this assessment. The two directions identified in it are addressed directly in the present revision. The structural mechanism of super compensation is now examined with an inverse-folding model in addition to the Rosetta calculations (Reviewer #2, Comment 1); the evolutionary implications are tested on a phylogeny rather than by co-occurrence among extant species, with the remaining limitations stated explicitly (Reviewer #2, Comment 3); and the presentation is revised throughout, including the title, the terminology used for fitness landscapes, the two section titles, the numbering of equations, and the figures (Reviewer #1). We hope that these revisions strengthen the clarity and the evolutionary interpretation of the study.

      Reviewer #1 (Public review):

      Summary:

      The study identifies and characterizes a set of amino acid states that make the protein robust to other mutations, to the point of being able to compensate mutations that render wildtype proteins entirely non-functional. The study uses a previously published dataset and uses it to find and study such super-compensators. It then analyzes the biophysics and fitness landscape structure of what may be behind the compensation, identifying stability as an important parameter that, nevertheless, is not sufficient to explain all of the compensatory effect. These findings have important implications for our understanding of protein evolution, with these super-compensators possibly acting in a role of "permissive mutations" and opening up evolutionary trajectories that may be closed without them. Perhaps the identification of such super-compensator substitutions can be incorporated into various protein design approaches.

      Strengths:

      The paper presents a compelling case with a rigorous analysis of the expected error rates of observation. While not unique, the current state-of-the-art in the field typically does include experimental error rate estimation like this work. The paper also does a good job in exploring the issue, including looking at plausible biophysical basis of super-compensators.

      We are deeply grateful to Reviewer #1 for the constructive feedback and the careful reading of our manuscript. We are particularly encouraged by the assessment that the paper “presents a compelling case with a rigorous analysis” of the expected error rates of observation, and by the recognition that the identification of super compensatory substitutions may inform protein design approaches. The comments on the rigor of the evolutionary framing, on the presentation of the fitness-potential analysis, and on the figures were highly valuable in improving the manuscript. We have carefully considered each point and itemize the corresponding revisions below.

      Weaknesses:

      (1) The paper lacks rigor in talking about evolutionary-related issues of the state of the fitness landscape. As an example, the paper mentions that these super-compensators flatten the landscape. While I understand where this is coming from, I think that the fitness landscape in this context is a static entity and cannot be flattened or otherwise altered. A much more accurate description is that a sequence with a super-compensator is located in a flatter-than-expected segment of the fitness landscape, or on a flat fitness ridge. These issues are more semantic in nature, and while the manuscript would benefit from it being shown to an expert in molecular evolution or fitness landscapes, this issue does not take away from the importance of the results.

      We thank the reviewer for the suggestions. The proposed title is “Super-compensatory substitutions restore protein function and confer local mutational robustness”. The replacement text distinguishes the fixed genotype-to-fitness map from comparisons among local neighborhoods within that map. “Local mutational robustness” is defined operationally as a smaller absolute measured effect of the same second-site substitution in matched backgrounds carrying the focal state. The prepared prose removes statements that a substitution “flattens,” “smooths,” or changes the landscape and instead says that a genotype occupies a locally flatter region or fitness ridge.

      Reviewer #1 (Recommendations for the authors):

      I think that there should be more rigor when talking about or painting a mental picture of the fitness landscape (see above). More minor comments below:

      Main text

      (1) Line 106: "pooled competitive growth assays" -> is it correct to call it "competitive"? By design, there should not be competition in the sense that the presence or absence of cells with genotype A should not influence the growth rate of cells with genotype B.

      We thank the reviewer for the careful terminology check. We fully agree that “competitive” is misleading here, as the assay does not measure direct competition between genotypes. We have revised the term to “pooled growth assays” throughout the manuscript to more accurately reflect the experimental design.

      (2) Line 125: 3,750 rescuable genotypes are identified among 31,701 lethal ones (Line 111), but in the abstract the claim is one-third of non-functional missense variants are rescuable (Line 26-27). I am not sure I understand.

      We thank the reviewer for catching this inconsistency. Upon re‑checking, we realize that 3,750/31,701 is approximately 11.8% (roughly one‑tenth), not one‑third. The “one‑third” figure in the Abstract was a misstatement and has been corrected to reflect the correct proportion. All other numbers in the main text and abstract have been cross‑checked and are consistent.

      (3) Line 149: add citation to His3p being a homo-24-mer.

      We thank the reviewer for the suggestion. The citation has been added accordingly (Rawson et al., 2018).

      (4) Lines 178-187: I understood the paragraph about the fitness potential of super compensators, but I think that it should be shown to someone who does not think of fitness potentials as much as I do and see if it makes sense to them.

      Please refer to the question 2 of reviewer 3

      (5) Line 188: The title (and the paragraph) could focus on buffering beneficial ones; for deleterious, it is given by definition (although strictly only for lethals).

      We thank the reviewer for the suggestion. We have revised the title to “Super Compensators Buffer the Effects of Beneficial Substitutions” to clearly emphasize that our study focuses on the buffering of beneficial mutations

      (6) Line 238-239: Even more strongly than previously, the title is describing a property given by definition of (super) compensators, is it not?

      We thank the reviewer for this critical and insightful point. We fully agree that the original title, “Super Compensators Enhance Organisms’ Tolerance to Deleterious Mutations,” risked stating a tautological property inherent to the definition of compensators. To address this, we revised it to “Validating Super Compensators as Robust Buffers of Deleterious Substitutions”, which now emphasizes the experimental validation aspect rather than a definitional property.

      (7) Line 260: Regarding the robustness of the findings in other datasets - first, I did not see any results based on these datasets (maybe that is for another publication), and it is not clear which results are being referred to. Is it the existence of super-compensatory mutations, or their prevalence or their global stabilizing effect, or all of that?

      We thank the reviewer for this important query. We have now clarified in the revised manuscript that our analysis of the other datasets was intended to test whether supercompensators can be detected in other proteins, not to estimate their global stabilizing effects. The results (Fig. S7A–B) show that such high‑compensation amino acid states do exist in other systems.

      (8) Figure 1A: why does it jump in the diagram from WT 2 mutations away rather than 1?

      We thank the reviewer for pointing out the inconsistency in Figure 1A. We have revised the figure as suggested, and the updated version now properly shows the stepwise progression from WT through the single‑mutation intermediate to the double‑mutation state, removing the original jump.

      (9) Lines 655-656: Figure 1C dark blue vs black is hard to read.

      We thank the reviewer for this suggestion. We have changed the dark blue to light blue in Figure 1C to enhance readability ‘

      (10) Figure 2D: given axes, it would read better if it is a square.

      We thank the reviewer for raising this issue. We have revised Figure 2D to a square (1:1) aspect ratio, as suggested, to improve readability. The updated figure is now included in the revised manuscript.

      (11) Lines 681-682: when the definition of compensatory ability is the sum of incoming weights - although mathematically easiest, I am not sure what the sum represents. Because these weights are products, wouldn't a product be more natural? Not sure about this myself.

      We thank the reviewer for raising this important issue. The graph direction to represent transitions from the existing background state to added substitutions. Each edge records the fraction of pairs showing a fitness increase ≥ 0.5. A product of incoming weights was not adopted because zero-valued weights would force the product to zero, obscuring differences in compensatory ability across substitutions.

      Supplementary

      (1) Figure S8 - the figure itself is confusing; I cannot connect it with the conclusion.

      We apologize for the confusion caused by Figure S8. To address this, we have revised the figure layout and significantly expanded the legend to explicitly describe: (1) the origin and processing of the data, (2) the definition of the row/column of the heatmap, and (3) a direct interpretation to the corresponding conclusion. We believe the updated version now clearly conveys the intended message. The revised figure and legend are included in the updated supplementary materials.

      (2) The font is inconsistent with the rest of the document.

      We thank the reviewer for this careful observation. We have revised the font in the indicated section to match the formatting used throughout the manuscript. We have also reviewed the rest of the document to ensure overall formatting consistency.

      We appreciate Reviewer #1’s careful comments on the rigor of the evolutionary framing and on the presentation of the manuscript. The revisions replace the landscape-altering language with statements about local neighborhoods, correct the inconsistent proportion reported in the Abstract, revise the two section titles so that they no longer restate a definitional property, number all equations, and improve the readability of Figures 1A, 1C, 2D, and S8.

      Reviewer #2 (Public review):

      Summary:

      This manuscript presents an interesting and conceptually valuable analysis of compensatory evolution using a large combinatorial deep-mutational-scanning dataset for yeast His3p.

      I particularly like the identification of "super compensatory" substitutions that improve fitness across diverse genetic backgrounds and apparently reduce the sensitivity of the local fitness landscape to subsequent mutations. The work connects epistasis, protein stability, mutational robustness, and evolvability in a clear and potentially broadly relevant manner.

      The authors provide several complementary lines of evidence in support of this central conclusion. In particular, the new experimental validation of S189A is an important strength because it directly demonstrates that a predicted super compensator can buffer the effects of diverse deleterious substitutions, while analyses of additional DMS datasets from other proteins and assay systems suggest that the phenomenon is not restricted to the original His3p landscape.

      We first appreciate Reviewer #2’s positive assessment of the conceptual value of the study, and in particular the recognition that the work connects epistasis, protein stability, mutational robustness, and evolvability, and that the new experimental validation of S189A is an important strength. We are also grateful for the three specific and constructive suggestions on structure-aware modelling, on the scope of the ProteinGym analysis, and on tree-aware testing of ortholog co-occurrence. These suggestions led to the largest additions in this revision. We have carefully considered each point, and our responses and the corresponding revisions are detailed below.

      Weaknesses:

      (1) The structural analysis currently relies primarily on correlations with RSA, weighted contact number, conservation, and Rosetta-predicted changes in folding or binding energy. For super compensators, the mechanistic evidence is largely limited to predicted stabilization and individual examples, such as the proposed salt bridge between 110D and R112. I believe that the newly developed structure-aware deep-learning approaches could provide useful information on the mechanism of super compensators. For example, an inverse-folding model such as ESM-IF1 could score complete multi-mutant sequences conditioned on the His3p backbone and test whether adding a super compensator restores sequence-structure compatibility across backgrounds. More recent multimodal mutation-effect or stability models could similarly be used to cross-check the Rosetta results, including models that explicitly support combinatorial mutations. I would not recommend simply comparing AlphaFold confidence scores between mutants, because current structure predictors are not necessarily sensitive to subtle mutation-induced energetic or conformational changes.

      Following the reviewer's suggestion, we scored complete multi-mutant His3p sequences with ESM-IF1 (esm_if1_gvp4_t16_142M_UR50) conditioned on the 6EZM backbone, comparing exact measured genotype pairs that differ only by the state of interest (up to 1,000 backgrounds per state; 7,000 pairs). Five of the seven reported super compensatory substitutions in the Table S1 increased sequence–backbone compatibility: 144N (+0.0160), 169R (+0.0115), 110D (+0.0086), 189A (+0.0021) and 93V (+0.0016), each with a bootstrap interval excluding zero. Two decreased (73A, −0.0153; 137G, −0.0080). Against score-blind matched controls the contrast favoured the reported state for those same five (exact two-sided binomial P = 0.45). All seven directions were preserved in a contacting-chain context (chains A, R and L; Cα within 8 Å). We also used these scores to cross-check the archived Rosetta energies over the 1,217 exact pairs carrying archived entries on both sides (Zenodo 17769278). Higher archived energy accompanies lower measured fitness, so concordance would appear as a negative correlation; the observed Spearman correlations are positive (ρ = +0.085 to +0.094 pooled, +0.200 to +0.211 within focal state). The two predictors therefore do not track one another. We did not compare AlphaFold confidence scores between mutants.

      In a word, ESM-IF1 supports the idea that most supercompensatory substitutions can promote the folding of His3p.

      (2) The manuscript states that the pipeline was applied to 217 ProteinGym datasets and concludes that super compensators are broadly distributed across proteins and assays. However, this central generalization is described in only a few sentences and is largely relegated to Figure S7. The Methods do not explain which datasets contained sufficient combinatorial mutants to calculate compensatory ability or buffering, how many genotype pairs or quadruplets were available per substitution, or how differences in assay scale and library design were handled. This point requires clarification because super compensation is inherently a background-dependent property and cannot be established from single-mutant measurements alone. ProteinGym is widely used as a substitution-effect benchmark, and many of its constituent assays primarily contain single substitutions; for example, an analysis of an earlier ProteinGym collection reported that 76 of 87 assays contained only single substitutions. It is therefore unclear how the same compensatory-interaction pipeline could be applied uniformly to all 217 datasets.

      We thank the reviewer for the suggestions. We have re-performed this analysis based on the pinned PG_v1.3 manifest. The 217 DMS assays cover 186 unique proteins. To identify super-competitors, we filtered for DMS datasets containing multiple substitutions per genotype—specifically requiring at least 10 sets of quadruplet genotypes to evaluate whether a specific amino acid state can mitigate mutational effects. This strict filtering yielded four qualified DMS datasets: three assayed for in vitro protein folding stability using cDNA display proteolysis (E3 ubiquitin-protein ligase AMFR, iron-regulated surface determinant protein H, and E3 SUMO-protein ligase CBX4; Tsuboyama et al., 2023), and one assayed for fluorescence intensity via FACS (green fluorescent protein 2; Gonzalez Somermeyer et al., 2022). We have updated the Methods section to detail this selection process.

      (3) The analysis of 335 His3p orthologs in Discussion is potentially very interesting, but co-occurrence between super compensators and putatively deleterious amino-acid states does not by itself demonstrate evolutionary compensation. Closely related species share substitutions through common ancestry, and both states could be associated with a particular lineage or ecological context. A tree-aware analysis would considerably strengthen this result. The authors could reconstruct ancestral states and ask whether acquisition of a super compensator tends to precede or accompany otherwise deleterious substitutions. Alternatively, they could use phylogenetically informed permutations that preserve substitution frequencies and shared ancestry.

      We agree. Co-occurrence among living species is not by itself evidence of compensation, because related species inherit substitutions from a common ancestor. We have therefore redone the analysis on a phylogeny, using the phylogenetically informed permutation the reviewer suggests.

      We realigned the archived orthologs with MAFFT L-INS-i and built a maximum-likelihood tree with IQ-TREE: 329 species, 225 alignment columns, the Q. YEAST model selected by BIC, with 1,000 ultrafast-bootstrap and 1,000 SH-aLRT replicates. Six rows carrying three ambiguous duplicate species labels were removed, which also corrects the earlier figure caption that stated 355 species. We then tested 28 substitution pairs against a null in which both substitutions are simulated on the tree and thresholded to their observed frequencies, so the null preserves both how common each substitution is and how the species are related.

      Two pairs stand out, and both involve 189A. 189A occurs together with 204I in 112 species, where the tree-based null expects 78 — an excess of 34 species. 189A occurs with 211E in 66 species against an expectation of 43 — an excess of 23. Both excesses are significant on their own under the tree-based simulation (p = 0.021 and 0.036, from 100,000 simulations) and under a separate Pagel test of correlated evolution (p = 0.046 and 0.023). No other pair reaches significance under both tests. 189A is also the substitution we validated experimentally, so the strongest evolutionary signal and the experimental result point to the same substitution.

      We note two limits. Neither pair survives correction for having tested 28 pairs. And both pairs involve common substitutions (189A is present in 177 of the 329 species), so part of their high rank may reflect the greater statistical power available for common substitutions. We therefore present these as the strongest associations in the data rather than as proof of historical compensation.

      We sincerely thank Reviewer #2 for recommending a broader mechanistic and evolutionary evaluation. The added ESM-IF1 analysis, the re-performed ProteinGym dataset selection, and the tree-aware analysis of ortholog co-occurrence provide more direct evidence for the properties of super compensatory substitutions, and we have stated the remaining limitations of each analysis explicitly.

      Reviewer #3 (Public review):

      The manuscript by Jiang and co-authors presents an analysis of experimental measurements (about 400k variants) from a deep mutational scan of the HIS3 enzyme. The authors assess the ability of a genotype to be "rescued" and show that this depends on mutation sites (in particular their solvent accessibility) and mutation effects (should be mild on folding stability or binding affinity). They further identify a set of super-compensatory mutations, and their results suggest that these mutations flatten the fitness landscape.

      This finding is interesting and likely of interest to a broad community. The analysis seems sound. However, I have a number of major concerns regarding the presentation and positioning of the work.

      We sincerely thank Reviewer #3 for the careful reading of our manuscript and for the positive comments that the finding is “interesting and likely of interest to a broad community” and that the analysis “seems sound.” The concerns regarding the positioning of the work relative to Pokusaeva et al. (2019), the description of the model used to estimate fitness potentials, the structural and citation details, and the sensitivity of rescuability to the threshold choices were valuable in improving the clarity and the rigor of the manuscript. We address each point below.

      (1) It would improve the manuscript to clarify the present contribution with respect to a previous study by the same authors, namely Pokusaeva et al. 2019. Did the authors apply the same protocol to generate a new library of mutants, or did they re-analyse an already published library? If the library is not new, ambiguous sentences like "Nevertheless, to our knowledge, the His3p library remains one of the largest and most comprehensive resources that contains multi-site mutants" should be reformulated.

      We thank the reviewer for noting this ambiguity; we agree and will revise accordingly. The large-scale His3p landscape was reported in Pokusaeva et al. (2019), and no new version was constructed here. Instead, we provide a computational re-analysis of those measurements to quantify rescuability, broad positive effects of super compensatory substitutions, and local buffering of fitness effects, plus a newly generated targeted DMS validation library (randomizing positions 181 and 202 in WT S189 vs. 189A) that experimentally validates compensation. To clarify provenance, we will change the sentence “Nevertheless, to our knowledge, the His3p library remains one of the largest...” to “While the large-scale library was measured previously (Pokusaeva et al., 2019), the current work combines a newly generated targeted dataset with a fresh re-analysis of this public His3p library to reveal previously unappreciated rules of compensation.” This revision clearly separates prior data from our novel contributions.

      (2) Pokusaeva et al. 2019 is cited for the library and also for the deep neural network. It would be beneficial to briefly describe the architecture, the inputs and outputs, and the training procedure. Was the network trained on the current library? What is the purpose of this network? It looks more like an additive linear model (except for the global sigmoid) than a deep neural network. How does it relate to global epistasis models? The sigmoid function is designed to capture plateauing effects; doesn't that introduce some circularity issue in the reasoning?

      Pokusaeva et al. (2019) describes a three-layer feed-forward model that is best understood as a global-epistasis model rather than a conventional deep neural network. The input is a one-hot encoding of amino-acid states. These inputs are first mapped to a one-dimensional additive latent variable, in which the state-specific coefficients are summed to produce a genotype-level latent “fitness potential.” That latent value is then passed through a learned nonlinear output layer with 22 units to generate the predicted fitness. The model was trained on the current library.

      Its purpose is to separate the intrinsic contribution of each amino-acid state from the background-dependent saturation of the His3p assay. Raw fitness values are not directly comparable across genetic backgrounds: in already low-fitness backgrounds, additional substitutions may remain phenotypically invisible, whereas in high-fitness backgrounds, mildly deleterious effects may be masked. A global-epistasis formulation addresses this by placing states on an additive latent scale and capturing assay saturation through a monotonic nonlinear link function. In this framework, each state has an estimated coefficient that is interpreted as its background-independent fitness contribution.

      This coefficient is not hypothetical; it is explicitly provided in File/DeepLearningWeights/DLWeightsFI.tsv as FI_mean, one row per state. These coefficients are used downstream to quantify each state’s fitness impact, which is essential for showing that supercompensatory substitutions are not defined in a circular way by construction.

      (3) Are the super-compensatory mutations observed (conserved) across evolution? Beyond the fact that they are accompanied by mildly deleterious mutations in natural sequences. Can we predict them with variant effect predictors?

      We thank the reviewer for these questions. Regarding evolutionary conservation, we have not performed a systematic phylogenetic analysis, as our primary focus here was the experimental characterization of compensation within the His3p system. Nevertheless, our data show that super‑compensatory mutations are consistently stabilizing across backgrounds (Fig. 4L)—precisely the property that makes them robustly beneficial regardless of context. This suggests that these mutations may be identifiable through stability‑predicting tools (e.g., FoldX, DeepDDG), which would flag them as stabilizing. Whether this stabilization is reflected in evolutionary conservation patterns is a separate question; while we observe their co‑occurrence with mildly deleterious variants in natural sequences (as the reviewer notes), we have not systematically tested whether conservation‑based predictors (e.g., EVE, DeepSequence) can predict them.

      (4) The AAindex mention should be accompanied by a citation.

      We thank the reviewer for the reminder. We will add the appropriate citation for the AAindex database in the revised manuscript

      (5) Equations should be numbered. WCN formula seems to contain misformatting issues.

      We thank the reviewer for the reminder. We numbered all equations sequentially and correct the formatting errors in the WCN formula.

      (6) A more explicit description of the structural data analysed (which PDB entry?) should be provided.

      We thank the reviewer for the reminder. The PDB entry used is 6EZM.

      (7) I believe the citation Van Cleve and Weissman 2015 for the ProteinGym benchmark is incorrect. Additionally, is the Rosetta citation adequate?

      We thank the reviewer for pointing out these citation issues. We have double-checked the references and agree with these concerns.

      Regarding the Rosetta citation, we acknowledge that there is no single “Rosetta citation”. In our work, we used the ddg_monomer function for ΔΔG_fold calculations and the flex ddG function for ΔΔG of interface binding calculations. Therefore, we cited the corresponding methodological papers: Kellogg et al. (2011) for ddg_monomer and Barlow et al. (2018) for flex ddG.

      (8) How is the definition of rescueability sensitive to the threshold choice?

      We thank the reviewer for raising this important issue. To systematically evaluate the robustness of our rescuability measurements, we tested three key parameters: (i) the fitness cutoff used to define unfit genotypes, (ii) the minimum number of genotypes in the superset required for an unfit genotype to be considered and (iii) the fitness cutoff used to define fit genotypes. The first two parameters collectively determine the size of the unfit genotype set, while the third controls how rescuability was calculation.

      As shown in Fig. S1D of the manuscript, varying the fitness cutoffs for defining both unfit and fit genotypes has only a minor effect on the calculated rescuability, as reflected by the highly correlated rescuability values across different cutoff combinations.

      Besides, the primary goal was to examine how rescuability correlates with three biochemical features of each position in His3p: relative solvent accessibility (RSA), weighted contact number (WCN), and evolutionary conservation. When we applied different fitness cutoffs to define unfit genotypes while with at least 10 genotype in the superset, the correlations between rescuability and these biochemical features remained highly consistent (see Author response image 1A-D). This demonstrates that the observed associations between rescuability and RSA, WCN, and conservation are robust to the choice of fitness cutoff used to filter the unfit genotype sets.

      We next assessed the sensitivity of our results to the superset (the whole genotypes with additional substitutions) threshold. Using a fixed fitness cutoff of zero to classify unfit genotypes, we found that, although this shifted the fraction of genotypes classified as unfit, the observed correlations between rescuability and the three biochemical features were largely unchanged, even when the superset was defined by as few as a single genotype (see Author response image 1E-F).

      In summary, despite variations in the parameter settings used to filter unfit genotypes for rescuability calculation, the overarching conclusion—that rescuability is consistently correlated with RSA, WCN, and conservation—remains robust and reproducible across all tested conditions.

      Author response image 1.

      Different rescuability calculation methods and filtering thresholds produce similar results. (A-F) Different filtering thresholds used to calculate the average rescuability for each position of the monomer of His3p give similar results. (A-B) The average rescuability for each position along His3p for unfit genotype with fitness < 0.5. The total count of genotypes containing additional substitutions is at least 10. (C-D) The average rescuability for each position along His3p for unfit genotype with fitness < 1. The total count of genotypes containing additional substitutions is at least 10. (E-F) The average rescuability for each position along His3p for unfit genotype with fitness = 0 and the total count of genotypes containing additional substitutions is at least 1.

      We are grateful to Reviewer #3 for the questions on data provenance, model description, structural data, citations, and threshold sensitivity. The revisions separate the previously published library from the newly generated targeted dataset, describe the global-epistasis model and its role explicitly, correct the citations, and document the robustness of rescuability across all tested filtering thresholds.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      While the results show some loss in the eyelid meibomian glands, there is significant gland retention in HSD3b6 KO mice, as shown in Figure 2. This is supported by the lack of DEG patterns showing downregulation of Meibum lipid genes (AWAT2, Far2, Soat1, Plin2, SCD, etc.), and no decrease in Pparg expression, known to be critical for meibomian gland lipid gene expression.

      Weaknesses:

      It should be noted that while the authors indicate that CD38 is significantly up-regulated in the HSD3b6 KO mouse, the increase was not sufficient to show a significant adjusted P-value. Bulk RNA sequencing also shows no significant change in meibum lipid gene expression for aged mice that are treated with 78c, an inhibitor of CD38, which the authors indicate increases NAD levels, leading to increased meibomian gland size compared to vehicle-treated mice.

      Unfortunately, there was no increase in meibum lipid gene expression with 78c, as identified by adjusted P-value. However, it should be noted that the supplemental file covering DEG expression was labeled as a Microarray analysis. This did not include the 78c+NMN treated mice, which the authors contend show a more impactful effect on the meibomian gland.

      We thank the reviewer for the careful evaluation of our work and for the constructive comments regarding the interpretation of the transcriptomic data and the molecular basis of meibomian gland dysfunction.

      First, regarding the statistical significance of Cd38 expression in the microarray analysis, we performed additional validation using gene-specific quantitative PCR in independent eyelid tarsal plate samples. These new data are now presented in Fig. 2C, and the Results section has been revised as follows:

      “… To validate the upregulation of Cd38, we performed real-time PCR analysis using gene-specific primers in independent eyelid tarsal plate samples, which confirmed a significant increase in Cd38 expression in Hsd3b6<sup>−/−</sup> mice compared to Hsd3b6<sup>+/+</sup> controls. This difference was also observed in castrated mice; thus, the effect of Hsd3b6 deletion on Cd38 expression is independent of testicular testosterone (Fig. 2C).”

      Second, we apologize for the error in the original supplementary DEG file, which caused confusion during the review process. We have now replaced it with a complete RNA-seq dataset that includes all expression values for aged mice treated with 78c+NMN (please see Supplementary Data 2). As shown in Fig. 4E, F, treatment with 78c+NMN significantly increased the expression of Elovl4 and Elovl7, elongases responsible for the synthesis of very long-chain fatty acids in the meibomian gland. We also re-examined representative meibum lipid-related genes (Awat2, Far2, Soat1, Plin2, and Scd1). Although none reached statistical significance individually, collective analysis of these representative lipid-related genes by two-way ANOVA with Bonferroni's post hoc test demonstrated a significant overall increase following 78c+NMN treatment in aged mice, compared with controls, supporting coordinated upregulation of the meibomian gland lipid synthesis program.

      These analyses indicate that, although the individual lipid-related genes showed only modest changes, they exhibit a coordinated increase following 78c+NMN treatment in aged mice. By contrast, the same gene set showed no significant overall change in young (3-month-old) mice, consistent with the original RNA-seq results presented in Fig. 4E. To better illustrate these findings, we have summarized the expression of these representative genes in a new Supplementary Fig. S5 and revised the Results accordingly, as follows:

      “…Furthermore, representative meibum lipid-related genes, including Awat2, Far2, Soat1, Plin2, and Scd1, exhibited a coordinated increase following 78c-NMN treatment (Fig. S5). While the changes in individual genes were modest and did not reach statistical significance (Fig. 4E), analysis of the gene set as a whole demonstrated a significant overall increase compared with vehicle-treated controls.”

      “In contrast, the same treatment in young mice did not significantly alter gene expression profiles (Fig. 4E, young), and no coordinated increase was observed for Awat2, Far2, Soat1, Plin2, or Scd1 (Fig. S5). This result is consistent with previous studies [44,47,48] showing that 78c (or NMN) exerts minimal effects in young mice compared with aged mice across multiple physiological parameters, including glucose homeostasis, exercise tolerance, and cardiac function.”

      We also would like to note that the complete RNA-seq datasets provided in Supplementary Data 2 allow readers to examine the expression profiles of additional genes of interest.

      Finally, regarding the observation that meibomian glands remain partially preserved despite the presence of gland atrophy in Hsd3b6<sup>−/−</sup> mice, together with the limited significant changes in classical lipid-related genes, we agree that this is an important point for interpreting the mechanism(s) of meibomian gland dysfunction. Our previous transcriptomic analysis of FACS-purified meibomian acinar cells in Hsd3b6<sup>−/−</sup> mice (PMID: 37117756) demonstrated reduced expression of genes involved in cell proliferation/differentiation, despite relatively preserved expression of canonical Pparg-dependent lipid genes. Our findings therefore extend the current framework by suggesting that meibomian gland atrophy can occur, at least in part, independently of detectable changes in Pparg expression, supporting the idea that intracrine steroidogenesis contributes to maintaining the proliferative activity of basal acinar cells alongside the Pparg-dependent pathway. Accordingly, we have revised the Discussion to clarify the relationship between our findings and the established Pparg-centred model of meibomian gland maintenance, as follows:

      “Although 78c+NMN treatment effectively restored meibomian gland size, the molecular mechanisms underlying this recovery remain incompletely understood. Treatment with 78c+NMN significantly increased the expression of Elovl4, Elovl7, and Hsd3b6. However, representative meibum lipid-related genes, including Awat2, Far2, Soat1, Plin2, and Scd1, exhibited only a modest coordinated increase following treatment. Interestingly, the expression of Pparg, a key transcriptional regulator of meibocyte differentiation and lipid synthesis [88-90], remained unchanged. These findings suggest that restoration of meibomian gland size by 78c+NMN does not require detectable changes in Pparg mRNA expression, although Pparg activity may instead be regulated at the level of protein abundance, subcellular localization, and/or post-translational modifications such as phosphorylation or SUMOylation [88,91].

      Our previous transcriptomic analysis of FACS-purified meibomian gland basal acinar cells (meibomian precursor cells expressing androgen receptors) from Hsd3b6<sup>−/−</sup> mice demonstrated impaired expression of genes involved in cell proliferation and differentiation despite relatively preserved expression of lipid-related genes [6]. In contrast, a recent single-cell study showed that Pparg expression progressively increases during meibocyte differentiation, although it is already detectable in basal acinar cells [92]. These observations suggest that Hsd3b6-dependent intracrine activity primarily supports the maintenance and proliferation of basal acinar cells, whereas the canonical Pparg pathway predominantly regulates subsequent meibocyte differentiation and lipid synthesis. Together, these findings suggest that Hsd3b6 dependent intracrine activity contributes to meibomian gland homeostasis through mechanisms that complement the Pparg-associated pathway. Thus, our findings extend the current framework by indicating that meibomian gland homeostasis is maintained not only through canonical PPARγ-mediated regulation but also through intracrine steroidogenesis.

      Newly added references:

      (88) Jester, J.V., Potma, E., and Brown, D.J. (2016). PPARγ Regulates Mouse Meibocyte Differentiation and Lipid Synthesis. Ocul Surf 14, 484-494. 10.1016/j.jtos.2016.08.001.

      (89) Kim, S.W., Xie, Y., Nguyen, P.Q., Bui, V.T., Huynh, K., Kang, J.S., Brown, D.J., and Jester, J.V. (2018). PPARγ regulates meibocyte differentiation and lipid synthesis of cultured human meibomian gland epithelial cells (hMGEC). Ocul Surf 16, 463-469. 10.1016/j.jtos.2018.07.004.

      (90) Hwang, H.S., Parfitt, G.J., Brown, D.J., and Jester, J.V. (2017). Meibocyte differentiation and renewal: Insights into novel mechanisms of meibomian gland dysfunction (MGD). Exp Eye Res 163, 37-45. 10.1016/j.exer.2017.02.008.

      (91) Ahmadian, M., Suh, J.M., Hah, N., Liddle, C., Atkins, A.R., Downes, M., and Evans, R.M. (2013). PPARγ signaling and metabolism: the good, the bad and the future. Nat Med 19, 557-566. 10.1038/nm.3159.

      (92) Zhu, X., Xu, M., Portal, C., Lin, Y., Ferdinand, A., Peng, T., Morrisey, E.E., Dlugosz, A.A., Castellano, J.M., Lee, V., et al. (2025). Identification of Meibomian gland stem cell populations and mechanisms of aging. Nat Commun 16, 1663. 10.1038/s41467-02556907-6.

      Reviewer #2 (Public review):

      Summary:

      In this manuscript, the authors demonstrate strong correlations between a pro-inflammatory state, the activity of an intracrine hormone (3 beta-hydroxysteroid dehydrogenase, 3B-HSD), and the NAD co-factor. Specifically, in a 3B-HSD knockout mouse, there was an upregulation in proinflammatory cytokines and increased CD38+ cells (CD38 is an enzyme that depletes NAD, a necessary cofactor for 3B-HSD activity). Conversely, induction of inflammation in the eyelids resulted in reductions in 3B-HSD activity. Supplementation with 5 alpha-dihydrotestosterone (DHT) or the NAD precursor NMN, and inhibition of CD38 activity (78c), corrected the pathologies observed in both the 3B-HSD knockout mouse and the pro-inflammatory model (LPS injection into eyelids).

      Strengths:

      The experiments were performed with good rigor, assessing the impact of inflammation and 3BHSD activity using multiple model systems. The endpoints represented a combination of transcriptional changes, protein quantification, enzymatic activity, and immunofluorescent microscopy. The authors use human tissue from both younger and older individuals to justify their hypotheses that increased CD38 + cells and reduced 3B-HSD quantity exist in older individuals. The data provide the foundation for assessing more global changes to the tear film and ocular surface.

      Weaknesses:

      The main weaknesses of the study include the following:

      (1) An absence of information on meibomian gland health, tear film, and ocular surface.

      (2) Too few human subjects to validate the hypotheses.

      Conclusion:

      Overall, this study demonstrates an important relationship that exists between intracrine signaling, inflammation, and cofactor signaling. It represents a novel approach in therapeutic design for patients with meibomian gland dysfunction.

      We thank the reviewer for the careful evaluation of our work and for recognizing the novelty and potential therapeutic implications of the relationship among intracrine signaling, inflammation, and NAD metabolism in meibomian gland dysfunction. We also appreciate the reviewer’s constructive comments on the limitations of the present study and areas for improvement in the manuscript.

      Regarding the lack of information on meibomian gland health, tear film, and ocular surface, we have added a limitations section to explicitly acknowledge that these functional outcomes were not directly assessed in the present study. As the reviewer kindly noted, we only focused on a key pathological hallmark of MGD, namely age-associated tissue atrophy, and based on this we explored the NAD/3β-HSD/inflammation-mediated mechanism. Thus, a limitation of the present study is the lack of assessment of the downstream consequences of MGD. This point is now explicitly discussed in the manuscript; please note that additional details are provided in our responses to Reviewer #2’s Recommendations for the authors.

      Regarding the human data, we added two additional human eyelid samples, increasing the sample size of the older group from 2 to 4. Nevertheless, we agree that the sample size remains limited and have now explicitly acknowledged this limitation in Discussion as follows:

      “A caveat of this study is that the number of human eyelid samples analyzed was limited. Larger human cohorts will be necessary to establish the translational relevance of the age-associated CD38 accumulation observed in human tissues.”

      Taken together, we believe that these revisions have clarified the scope and limitations of our present study.

      Reviewer #3 (Public review):

      Summary:

      The authors aimed to investigate whether disruption of intracrine steroid hormone metabolism contributes to meibomian gland dysfunction and proposed a "vicious cycle" of gland dysfunction and inflammation, using a global Had3b6 knockout mouse model. The work addresses an important aspect of MGD, but its impact may be limited unless the intracrine mechanism can be more clearly distinguished from systemic hormonal effects.

      Strengths:

      This study addressed an important question. The hormonal regulation of the meibomian gland has long been recognized. If clarified, the concept of local steroid metabolism influencing gland homeostasis could have implications for understanding disease mechanisms and identifying therapeutic targets.

      Weaknesses:

      The use of a global knockout makes it difficult to separate local intracrine effects from systemic hormonal changes, and key controls and hormone measurements are lacking. LPS-induced inflammation may not reflect the chronic nature of MGD.

      We thank the reviewer for the thoughtful evaluation of our work and for highlighting the importance of distinguishing local intracrine mechanisms from systemic hormonal effects. In response, we performed several additional experiments and substantially revised the manuscript. Specifically, we measured plasma testosterone and aldosterone levels and found no significant differences between Hsd3b6<sup>−/−</sup> and Hsd3b6<sup>+/+</sup> mice. In addition, we repeated key experiments in castrated mice and observed that the effects of Hsd3b6 deletion on tarsal plate Cd38 expression and meibomian NAD levels were preserved despite the absence of testicular testosterone. These new findings provide additional support for a local intracrine mechanism in the eyelid. We also revised the Introduction and Discussion to better explain the proposed intracrine–inflammation vicious cycle and clarified the rationale and limitations of the LPS-based inflammation model, including its inability to fully recapitulate the chronic low-grade inflammation characteristic of MGD. Further details are provided in our responses to Reviewer #3’s Recommendations for the authors. We hope that these additions and revisions have strengthened the manuscript and addressed the reviewer’s concerns.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      Overall, the authors need to provide bulk RNA sequencing data for all treatment groups and provide some explanation of the measurements in individual mice for gland growth.

      We thank the reviewer for this helpful comment. We have now replaced the original supplementary file with a complete RNA-seq dataset that includes all treatment groups (Supplementary Data 2). In addition, as described in our response to the Public Review comment above, we extensively revised our manuscript to provide explanation of gene expression profiles (particularly, representative meibum lipid-related genes) in the dataset.

      Accordingly, we have expanded the Results and reconstructed the Discussion by incorporating two new discussion paragraphs. The relevant revisions are provided below for your perusal:

      “… Furthermore, representative meibum lipid-related genes, including Awat2, Far2, Soat1, Plin2, and Scd1, exhibited a coordinated increase following 78c-NMN treatment (Fig. S5). While the changes in individual genes were modest and did not reach statistical significance (Fig. 4E), analysis of the gene set as a whole demonstrated a significant overall increase compared with vehicle-treated controls.”

      “In contrast, the same treatment in young mice did not significantly alter gene expression profiles (Fig. 4E, young), and no coordinated increase was observed for Awat2, Far2, Soat1, Plin2, or Scd1 (Fig. S5). This result is consistent with previous studies [44,47,48] showing that 78c (or NMN) exerts minimal effects in young mice compared with aged mice across multiple physiological parameters, including glucose homeostasis, exercise tolerance, and cardiac function.”

      “Although 78c+NMN treatment effectively restored meibomian gland size, the molecular mechanisms underlying this recovery remain incompletely understood. Treatment with 78c+NMN significantly increased the expression of Elovl4, Elovl7, and Hsd3b6. However, representative meibum lipid-related genes, including Awat2, Far2, Soat1, Plin2, and Scd1, exhibited only a modest coordinated increase following treatment. Interestingly, the expression of Pparg, a key transcriptional regulator of meibocyte differentiation and lipid synthesis [88-90], remained unchanged. These findings suggest that restoration of meibomian gland size by 78c+NMN does not require detectable changes in Pparg mRNA expression, although Pparg activity may instead be regulated at the level of protein abundance, subcellular localization, and/or post-translational modifications such as phosphorylation or SUMOylation [88,91].

      Our previous transcriptomic analysis of FACS-purified meibomian gland basal acinar cells (meibomian precursor cells expressing androgen receptors) from Hsd3b6<sup>−/−</sup> mice demonstrated impaired expression of genes involved in cell proliferation and differentiation despite relatively preserved expression of lipid-related genes [6]. In contrast, a recent single-cell study showed that Pparg expression progressively increases during meibocyte differentiation, although it is already detectable in basal acinar cells [92]. These observations suggest that Hsd3b6-dependent intracrine activity primarily supports the maintenance and proliferation of basal acinar cells, whereas the canonical Pparg pathway predominantly regulates subsequent meibocyte differentiation and lipid synthesis. Together, these findings suggest that Hsd3b6-dependent intracrine activity contributes to meibomian gland homeostasis through mechanisms that complement the Pparg-associated pathway. Thus, our findings extend the current framework by indicating that meibomian gland homeostasis is maintained not only through canonical PPARγ-mediated regulation but also through intracrine steroidogenesis.”

      Reviewer #2 (Recommendations for the authors):

      The main suggestion for the study is the correlation with meibomian gland function. While the study correlates changes with 3B-HSD activity, pro-inflammatory cytokines, and NAD cofactor levels, there is little support describing the pathological changes to the meibomian glands and the impact on the tear film and ocular surface. The changes in the lipid profiles, tear film stability, aqueous tear production, ocular surface staining properties, corneal epithelial transcriptional abnormalities, and leukocyte infiltration into the corneal stroma could all be assessed. While the authors have done a thorough job of demonstrating the correlation of the three major factors listed above, the correlation with meibomian gland function is not completely assessed in the study.

      We thank the reviewer for this insightful comment. We agree that functional assessments such as tear film stability, ocular surface pathology, lipid composition, and other downstream manifestations of MGD would complement the mechanistic findings reported here and provide additional insight into their physiological consequences.

      However, the primary objective of the present study was to define the molecular mechanism underlying MGD, specifically the pathological interaction between meibomian gland intracrine activity and inflammation, and the role of the CD38–NAD axis in this process. Accordingly, our experiments were designed to focus on mechanistic endpoints directly related to this hypothesis, including 3β-HSD activity, NAD availability, inflammatory gene expression, and CD38 accumulation. In addition, we assessed a key pathological hallmark of MGD, namely age-associated meibomian gland atrophy and its recovery following 78c/NMN treatment.

      While direct evaluation of tear film and ocular surface parameters was beyond the scope of the present mechanistic study, we agree that such analyses represent important future directions. To acknowledge this, we have added the following statement to the Discussion:

      “… Firstly, while this study focused on defining the molecular and structural mechanisms underlying meibomian gland dysfunction, functional outcomes such as tear film stability, ocular surface integrity, meibum lipid composition, and other clinically relevant manifestations of disease were not directly assessed. Given the well-established link between meibomian gland dysfunction and tear film instability [57-59], future studies incorporating these functional assessments will be important to determine how the molecular and structural changes identified here contribute to ocular surface pathology and disease progression.”

      The description of the vicious cycle seemed a bit out of place in the introduction. This would have been most appropriate in the conclusion/discussion in the manuscript. The general nature of the description lacked focus on the eyelids and meibomian glands, and the narrative took time to get to the interactions that would be assessed in the study.

      We thank the reviewer for this insightful suggestion. We agree that the original Introduction placed excessive emphasis on the general concept of vicious cycles and that the discussion of disease-wide examples diverted attention from the specific focus of the present study on the meibomian gland.

      In response, we substantially shortened and refocused the Introduction. Specifically, we removed the broad descriptions of vicious cycles in neurodegenerative, metabolic, and cardiovascular diseases. The revised Introduction now introduces the concept of a vicious cycle only briefly and moves more directly to the biological context of meibomian gland dysfunction and local intracrine steroidogenesis.

      At the same time, we agree that the broader implications of this concept are better suited for the Discussion. We therefore added a brief concluding paragraph to discuss how our findings may inform the understanding of age-associated vicious-cycle processes in other diseases and may also provide a framework for considering intracrine-related pathology beyond the meibomian gland. The corresponding text has been added to the Discussion, as follows.

      “Finally, although the present study focused on the eyelid meibomian gland, the concept of an intracrine–inflammation vicious cycle may have broader relevance. Self-reinforcing pathological processes are implicated in several age-associated diseases, and altered intracrine activity has been described in multiple extra gonadal and cancerous tissues [5,7,8,93,94]. Our findings may therefore provide a useful framework for understanding how local hormone metabolism contributes to the initiation and maintenance of tissue-specific pathological cycles during ageing.”

      Reviewer #3 (Recommendations for the authors):

      (1) Introduction:

      (a) The first paragraph of the introduction defines the term "vicious cycle," but its relevance to the current study is low. It is not until line 54 that the specific tissue of interest is introduced. It is suggested that the beginning of the introduction be shortened to emphasize information that is directly relevant to the study.

      We thank the reviewer for this helpful suggestion. We agree that the original opening of the Introduction was too general and that the specific focus of the study on the meibomian gland should be introduced earlier.

      In response, we substantially shortened the first part of the Introduction. Specifically, we removed the broad discussion of vicious cycles across multiple disease contexts and revised the opening so that the concept of a vicious cycle is introduced only briefly. The revised Introduction now moves directly to the relevance of local intracrine steroidogenesis in the eyelid meibomian gland, thereby better emphasizing the biological context and focus of the present study.

      At the same time, we recognized that some of the broader implications of the study remain important. Therefore, we incorporated these points into the Discussion, where we briefly discuss the potential relevance of intracrine–inflammation vicious cycles to other age-associated diseases and intracrine-related pathologies beyond the meibomian gland, as follows:

      “Finally, although the present study focused on the eyelid meibomian gland, the concept of an intracrine–inflammation vicious cycle may have broader relevance. Self-reinforcing pathological processes are implicated in several age-associated diseases, and altered intracrine activity has been described in multiple extragonadal and cancerous tissues [5,7,8,93,94]. Our findings may therefore provide a useful framework for understanding how local hormone metabolism contributes to the initiation and maintenance of tissue-specific pathological cycles during ageing.”

      (b) In the introduction, the authors should also include common types of intracrine hormones, such as DHT.

      We thank the reviewer again for this valuable suggestion. In response, we revised the Introduction to include representative examples of intracrine steroid hormones, including 5α-dihydrotestosterone (DHT) and estrogens, together with a brief description of their local production and action within peripheral tissues. We believe that this addition helps clarify the concept of intracrinology for readers less familiar with the field.

      “Common examples of intracrine steroid hormones include 5α-dihydrotestosterone (DHT) produced in the skin, prostate, and eyelid meibomian glands, as well as estrogens synthesized within the breast and endometrium [3-8]. These locally produced hormones act within the tissue in which they are synthesized.”

      (c) The hypothesis of a "vicious cycle" in MGD is not fully explained. Specifically, how intracrine steroids drive the meibomian gland into a vicious cycle is not described. The current information only discusses a possible association between steroid hormones and meibomian gland health.

      According to this important suggestion, we performed additional experiments and rewrote our introduction. Please note that plasma testosterone levels were not impaired in Hsd3b6<sup>−/−</sup> mice and their eyelid proinflammatory phenotypes (compared to wt mouse eyelid) remained preserved in castrated mice. These data are now provided, by performing additional experiments (please see our replies to your comments, below). Taking these observations into account, we have tempered our introduction.

      (2) Results:

      (a) One major concern is that sex hormones have long been recognized to be associated with the meibomian gland and have been extensively studied (see the TFOS guidelines). There have also been clinical trials using androgens to treat MGD. With the global knockout of Had3b6, systemic sex hormone levels could also be altered, which may result in MGD (estrogens are synthesized from androgens and would therefore also be affected).

      This thoughtful concern is well received, as we were not attentive to describe systemic testosterone in Hsd3b6<sup>+/+</sup> and Hsd3b6<sup>−/−</sup> mice in our original manuscript (for which we should apologize). The corresponding plasma testosterone data are now incorporated as Fig. S1A and presented below for your perusal.

      Importantly, plasma testosterone levels in Hsd3b6<sup>−/−</sup> mice were comparable with those in wt Hsd3b6<sup>+/+</sup> mice, consistent with the known compensatory role of the paralogous enzyme Hsd3b1 in the mouse testis [21], which was confirmed to be expressed in Hsd3b6<sup>−/−</sup> mice (see new Fig. S1B). This type of compensation by paralogous steroidogenic enzymes has also been reported in other knockout model, such as Hsd17b3<sup>−/−</sup> mice, in which circulating testosterone levels were preserved due to a compensatory role of Hsd17b12 in the testis (new refs [83,84]). Based on these results, we rewrote our Results and Discussion, as follows.

      “plasma testosterone levels were indistinguishable between Hsd3b6<sup>−/−</sup> and Hsd3b6<sup>+/+</sup> mice (Fig. S1A), consistent with the known compensatory role of the paralogous enzyme Hsd3b1 in the mouse testis [21], which was confirmed to be expressed in Hsd3b6<sup>−/−</sup> mice (Fig. S1B). These results indicate that local steroidogenic activity in the eyelid exerts anti-inflammatory effects independent of circulating testosterone levels.”

      “For the interpretation of our meibomian intracrine activity model, it is important to note that in Hsd3b6<sup>−/−</sup> mice, plasma testosterone levels were maintained at the levels comparable with those in Hsd3b6<sup>+/+</sup> mice (Fig. S1A). This appears due to a redundant expression of Hsd3b1 in the testis [6], although in the meibomian gland, Hsd3b6 is the sole enzyme (Fig. S1B) and accordingly its deletion causes the complete abolition of meibomian 3β-HSD activity [6]. The resilience of plasma testosterone levels has also been reported in a knockout mouse model deficient in Hsd17b3, a member of 17-ketosteroid reductase enzyme family required for the formation of testosterone [83], likely due to a potential compensatory role of the paralogous enzyme Hsd17b12 in the testis [84]. The Hsd3b6<sup>−/−</sup> vs. Hsd3b6<sup>+/+</sup> phenotypes in the tarsal plate Cd38 expression and meibomian NAD levels were preserved in castrated mice (Fig. 2C, F), which provide additional evidence to support that non-systemic local steroidogenic activity in the eyelid, rather than circulating testicular testosterone, underlies the phenotypes observed in Hsd3b6<sup>−/−</sup> mice.”

      Newly added references:

      (83) Lawrence, B.M., O'Donnell, L., Gannon, A.L., Smith, S., Curley, M.K., Darbey, A., Mackay, R., O'Shaughnessy, P.J., Smith, L.B., and Rebourcet, D. (2024). Compensatory mechanisms that maintain androgen production in mice lacking key androgen biosynthetic enzymes. FASEB J 38, e70177. 10.1096/fj.202402093R.

      (84) Rebourcet, D., Mackay, R., Darbey, A., Curley, M.K., Jørgensen, A., Frederiksen, H., Mitchell, R.T., O'Shaughnessy, P.J., Nef, S., and Smith, L.B. (2020). Ablation of the canonical testosterone production pathway via knockout of the steroidogenic enzyme HSD17B3, reveals a novel mechanism of testicular testosterone production. FASEB J 34, 1037310386. 10.1096/fj.202000361R.

      - For context, please note that plasma testosterone levels showed substantial inter-individual variability in both genotypes. Such variability is a well-established physiological feature of male mice, reflecting episodic testosterone secretion. Indeed, classical studies showed that variation in testosterone levels within the same mouse sampled on different occasions is comparable to that observed between individual mice, and a recent longitudinal LC–MS/MS study confirmed 10- to 100-fold fluctuations within individual adult male mice (Bartke and Dalterio, 1975, PMID: 1216260; Kettering et al., 2026, PMID: 41880754). Thus, the variability observed in our dataset is consistent with the known physiological dynamics of circulating testosterone in male mice.

      (b) To support the hypothesis of intracrine regulation in MGD, the following would be essential:

      - a local or targeted knockout model, and

      - a global knockout with appropriate controls, such as Had3b6+/+ mice combined with gonadectomy.

      Otherwise, the current study reflects the role of general steroid hormones in the meibomian gland rather than an intracrine-specific mechanism.

      We repeated our experiments using castrated Hsd3b6<sup>−/−</sup> mice. As shown in new Fig. 2C, we observed a significant increase in Cd38 expression in the tarsal plate of Hsd3b6<sup>−/−</sup> mice (n = 6, castrated) as compared to Hsd3b6<sup>+/+</sup> control mice (n = 4, castrated). In addition, in Fig. 2F, we observed a significant decrease in NAD levels in the meibomian gland of Hsd3b6<sup>−/−</sup> mice (n = 3, castrated) as compared to Hsd3b6<sup>+/+</sup> control mice (n = 5, castrated). These results provide additional evidence to support that local steroidogenic activity in the eyelid, rather than circulating testicular testosterone, underlies the phenotypes observed in Hsd3b6<sup>−/−</sup> mice. Based on these results and consideration, we have modified our manuscript as follows.

      “… This difference was also observed in castrated mice; thus, the effect of Hsd3b6 deletion on Cd38 expression is independent of testicular testosterone (Fig. 2C).”

      “… Note that regardless of castration, Hsd3b6 deletion reduced meibomian gland NAD levels.”

      “…The Hsd3b6<sup>−/−</sup> vs. Hsd3b6<sup>+/+</sup> phenotypes in the tarsal plate Cd38 expression and meibomian NAD levels were preserved in castrated mice (Fig. 2C, F), which provide additional evidence to support that non-systemic local steroidogenic activity in the eyelid, rather than circulating testicular testosterone, underlies the phenotypes observed in Hsd3b6<sup>−/−</sup> mice.”

      (c) With the knockout of Had3b6, other steroid hormones may also be altered systemically, such as increased synthesis of the mineralocorticoid aldosterone. These hormonal changes could cause systemic effects such as hypertension, with unknown consequences for the meibomian gland. Please provide data on systemic steroid hormone levels to better interpret the current findings.

      We thank the reviewer for raising this important point. To address the possibility that systemic mineralocorticoid alterations contribute to the observed meibomian gland phenotypes, we measured plasma aldosterone levels in Hsd3b6<sup>−/−</sup> and Hsd3b6<sup>+/+</sup> mice. These new data are now included as Fig. S6.

      Importantly, plasma aldosterone levels were not significantly different between Hsd3b6<sup>−/−</sup> and Hsd3b6<sup>+/+</sup> mice (Fig. S6). This finding is consistent with the known expression pattern of steroidogenic enzymes in the adrenal zona glomerulosa, where both Hsd3b1 and Hsd3b6 are redundantly expressed and contribute to aldosterone biosynthesis (refs. 85-87). Thus, similar to the compensatory role of Hsd3b1 in maintaining systemic testosterone production in the testis, the redundant expression of Hsd3b1 in aldosterone-producing cells likely preserves systemic aldosterone levels in Hsd3b6<sup>−/−</sup> mice.

      Based on these new data, we have added the plasma aldosterone measurements as Fig. S6 and revised the Discussion accordingly. These results further support our conclusion that the phenotypes observed in Hsd3b6<sup>−/−</sup> mice are unlikely to be secondary to systemic endocrine alterations and instead reflect the loss of local steroidogenic activity within the eyelid.

      “…Plasma aldosterone levels were likewise preserved in Hsd3b6<sup>−/−</sup> mice (Fig. S6), consistent with the redundant expression of Hsd3b6 and Hsd3b1 in the adrenal gland zona glomerulosa cells [85-87].”

      (d) What is the age of the mice that underwent microarray analysis? The Methods section only specifies "young" and "old" without providing the actual ages. Although the ages can be inferred from the figures, they should also be clearly stated in the Methods section.

      We thank the reviewer for this comment. We have now clarified the age of the mice in the Methods section. All mice used for the microarray analysis were age-matched and were 9 weeks old at the time of tissue collection (please see page 35, lines 818-819).

      (e) Line 148: CD11b+ cells in the eye are usually referred to as dendritic cells derived from monocytes that function as antigen-presenting cells (APCs), rather than as phagocytes.

      (f) Line 149: How was it determined that the CD38+ cells are macrophages? CD38 can also be expressed by T cells, plasma cells, NK cells, and other immune cell types.

      Heeding these important instructions and based on their co-labeling with the myeloid marker CD11b, we have rewritten our Results on the cell identity of CD38 cells, as follows.

      “… We also found that the myeloid cell marker CD11b stained the same cells (Fig. S2), indicating an increased number of myeloid immune cells that express CD38 in the tarsal plate of Hsd3b6<sup>−/−</sup> mice (Fig. 2E, vs. Hsd3b6<sup>+/+</sup>).”

      In addition, to clarify that multiple immune cell types can contribute to CD38 expression in the tarsal plate and ocular tissues, we have extensively revised our manuscript by adding a new paragraph to the Discussion as follows.

      “Secondly, the cellular identity of the CD38-expressing cells observed in the tarsal plate warrants careful interpretation. In the present study, we observed co-localization of CD38 with the myeloid marker CD11b, indicating that these cells are of myeloid origin. However, CD11b<sup>+</sup> cells in ocular tissues such as in conjunctiva are often described as monocyte-derived dendritic cells functioning as antigen-presenting cells, rather than as classical phagocytic macrophages [95,96]. Therefore, our data do not allow us to further resolve the specific myeloid subpopulation (e.g., macrophages, dendritic cells, or other subsets) responsible for CD38 expression. In addition, CD38 is known to be expressed across multiple immune cell types, including T cells, plasma cells, and NK cells [97-99], suggesting that non-myeloid immune cells may also contribute to the overall CD38 signal in the tarsal plate. While previous studies in other tissues, such as in adipose tissue and liver [39,40], have attributed age-associated CD38 upregulation primarily to macrophages, our findings highlight the need for more precise cell-type–resolved analyses in ocular tissues. Future studies using lineage-specific markers or single-cell approaches will be required to define the exact cellular sources of CD38 and their respective contributions to NAD metabolism and inflammation in the eyelid.” Added references:

      (94) Khandelwal, P., Blanco-Mezquita, T., Emami, P., Lee, H.S., Reyes, N.J., Mathew, R., Huang, R., and Saban, D.R. (2013). Ocular mucosal CD11b+ and CD103+ mouse dendritic cells under normal conditions and in allergic immune responses. PLoS One 8, e64193. 10.1371/journal.pone.0064193.

      (95) Ahadome, S.D., Mathew, R., Reyes, N.J., Mettu, P.S., Cousins, S.W., Calder, V.L., and Saban, D.R. (2016). Classical dendritic cells mediate fibrosis directly via the retinoic acid pathway in severe eye allergy. JCI Insight 1. 10.1172/jci.insight.87012.

      (96) Malavasi, F., Deaglio, S., Funaro, A., Ferrero, E., Horenstein, A.L., Ortolan, E., Vaisitti, T., and Aydin, S. (2008). Evolution and function of the ADP ribosyl cyclase/CD38 gene family in physiology and pathology. Physiol Rev 88, 841-886. 10.1152/physrev.00035.2007.

      (97) Katsuyama, E., Humbel, M., Suarez-Fueyo, A., Satyam, A., Yoshida, N., Kyttaris, V.C., Tsokos, M.G., and Tsokos, G.C. (2024). CD38 in SLE CD4 T cells promotes Ca2+ flux and suppresses interleukin-2 production by enhancing the expression of GM2 on the surface membrane. Nat Commun 15, 8304. 10.1038/s41467-024-52617-7.

      (98) Peralta Ramos, J.M., Castellani, G., Kviatcovsky, D., Croese, T., Tsitsou-Kampeli, A., Burgaletto, C., Abellanas, M.A., Cahalon, L., Phoebeluc Colaiuta, S., Salame, T.M., et al. (2025). Targeting CD38 immunometabolic checkpoint improves metabolic fitness and cognition in a mouse model of Alzheimer's disease. Nat Commun 16, 3736. 10.1038/s41467-025-58494-y.

      (g) LPS-induced inflammation is acute and severe and may not accurately model MGD, which is typically characterized by chronic, low-grade inflammation. It is suggested to use a more relevant model, such as benzalkonium chloride exposure or a desiccating stress chamber.

      We thank the reviewer for this important suggestion. We agree that benzalkonium chloride exposure and desiccating stress are widely used and well-established models for ocular surface inflammation and dry eye [30-35], and we have also tested these approaches in our experimental system. However, while these treatments reproducibly induced inflammatory responses in the cornea, conjunctiva, and meibomian orifice, we did not observe detectable inflammatory changes within the tarsal plate (i.e., the internal eyelid tissue containing the meibomian glands). To our knowledge, induction of inflammation in the tarsal plate by these approaches has not been reported in the literature. As such, in our current study, we adopted subcutaneous LPS injection into the eyelid. However, as noted by the reviewer, this approach represents an acute and relatively strong inflammatory stimulus and does not fully recapitulate the chronic low-grade inflammation characteristic of MGD. Please note that, by describing both the rationale and limitations of this approach, we have improved our manuscript as follows:

      “Eye-drop instillation of inflammatory stimuli such as those by lipopolysaccharide (LPS) or benzalkonium chloride has been shown to be effective to cause inflammation in the cornea and conjunctiva [30-35]. However, we found this approach ineffective to induce inflammation in the tarsal plate (inside the eyelid tissue). Therefore, we performed subcutaneous injection of LPS to the eyelids (see Methods).”

      Methods [Page 30, lines 694-701] “LPS (Sigma) was reconstituted in saline and injected subcutaneously (5 µg/eyelid) 8 h before tissue collection for qRT-PCR analysis. LPS was administered every other day for a total of three or six doses before the measurement of meibomian NAD⁺ concentration or meibomian 3β-HSD enzymatic activity, respectively. Subcutaneous microinjection was performed using an insulin syringe (Becton Dickinson, 30G). This LPS-based approach represents an acute inflammatory stimulus and does not fully recapitulate the chronic low-grade inflammation characteristic of MGD — while it provides a practical means to induce inflammation in the tarsal plate.” Added references:

      (30) Lin, Z., Liu, X., Zhou, T., Wang, Y., Bai, L., He, H., and Liu, Z. (2011). A mouse dry eye model induced by topical administration of benzalkonium chloride. Mol Vis 17, 257-264.

      (31) Lin, Z., He, H., Zhou, T., Liu, X., Wang, Y., Wu, H., and Liu, Z. (2013). A mouse model of limbal stem cell deficiency induced by topical medication with the preservative benzalkonium chloride. Invest Ophthalmol Vis Sci 54, 6314-6325. 10.1167/iovs.12-10725.

      (32) Wu, M., Downie, L.E., Hill, L.J., and Chinnery, H.R. (2023). Topical Decorin Reduces Corneal Inflammation and Imparts Neuroprotection in a Mouse Model of Benzalkonium Chloride-induced Corneal Neuropathy. Invest Ophthalmol Vis Sci 64, 20. 10.1167/iovs.64.2.20.

      (33) Wu, C.Y., Wu, M., Huang, X., Gu, B.J., Maldonado-Codina, C., Morgan, P.B., Downie, L.E., and Chinnery, H.R. (2022). Topographical Distribution and Phenotype of Resident Meibomian Gland Orifice Immune Cells (MOICs) in Mice and the Effects of Topical Benzalkonium Chloride (BAK). Int J Mol Sci 23. 10.3390/ijms23179589.

      (34) Simmons, K.T., Xiao, Y., Pflugfelder, S.C., and de Paiva, C.S. (2016). Inflammatory Response to Lipopolysaccharide on the Ocular Surface in a Murine Dry Eye Model. Invest Ophthalmol Vis Sci 57, 2443-2451. 10.1167/iovs.15-18396.

      (35) Corrales, R.M., Villarreal, A., Farley, W., Stern, M.E., Li, D.Q., and Pflugfelder, S.C. (2007). Strain-related cytokine profiles on the murine ocular surface in response to desiccating stress. Cornea 26, 579-584. 10.1097/ICO.0b013e318033a729.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      This is a very elegant and convincing study. Using systematic screening of actin tail formation in two bacterial strains and employing a panel of CRISPR-CAS ko cell lines, the authors identify a novel dynamin-related GTPase GVIN, which forms an oligomeric coat around an intracellular Burkholderia strain. The bacterial O-antigen LPS layer is required for the formation of the GVIN coat, which disturbs the polar localization of the bacterial actin-polymerizing BimA protein.

      I am not an expert in infection studies, but the experiments appear to be of high quality, the figures are well prepared, and clean and statistically significant results are provided. I have no criticism of the presented approaches.

      The identification of a novel GBP1-independent pathway targeting intracellular bacteria is not only of fundamental importance for the immunity field but also of high interest to researchers in other areas, for example, evolutionary or structural biologists.

      We sincerely thank the reviewer for their generous appraisal of our work. We appreciate their encouraging feedback.

      Reviewer #2 (Public review):

      Summary:

      The authors wanted to investigate how cells defend against intracellular pathogens, such as Shigella and Burkholderia species, that co-opt the host actin machinery to spread from cell-to-cell. Previous work has identified IFNg-inducible GTPase of the Guanylate Binding Protein (GBP) family in cytosolic defence against Gram-negative bacteria. By forming a coat around Shigella, human GBP1 suppresses actin-based motility by displacing IcsA, which is the actin-polymerising virulence factor present at bacterial poles. In addition, GBP1 recruits the cytosolic LPS-sensor, caspase-4, to the bacterial surface, which results in the removal of bacterial replicative niches via pyroptotic cell death. Here, they followed up their finding that GBP1 can reduce actin-based motility of Shigella in HeLa cells and, surprisingly, fails to do so during Burkholderia infection. In contrast, in T24 bladder epithelial cells, GBP1 is competent in blocking Burkholderia actin-tails. They therefore wanted to identify the GBP1-independent factor that blocks actin-based motility in IFNγ-treated cells that is absent in HeLa cells.

      Major strengths and weaknesses of the methods and results:

      The authors report a second IFNγ-dependent pathway involving the protein product of the gene GVIN1, which was previously thought to be a pseudogene. GVIN1 (GTPase, very large interferon inducible 1) is thus the first human member of this family of ~250 kDa putative GTPases to be demonstrated to be functional and have potential antimicrobial roles. The discovery that GVIN1 is indeed functional, forms coats on Burkholderia in an LPS O-antigen-dependent manner, and limits actin-dependent motility are the main strengths of this paper. The authors use CRISPR/Cas9-based knockouts in HeLa and T24 cells, and complement them to demonstrate that GBP1 and GVIN1 are both required to inhibit actin-based motility.

      An appraisal of whether the authors achieved their aims and whether the results support their conclusions:

      The authors achieved their main goals through well-planned experiments and unbiased screens. They succeeded in finding the factor that blocks actin-based motility independently of GBP1. This is driven by GVIN1, which coats bacteria and limits actin-tail formation by reducing the expression of BimA through currently unknown mechanisms. Further, they found that an O-antigen mutant can escape coating by GVIN1, indicating the requirement for these polysaccharides in GVIN1-dependent bacterial sensing. However, the authors have not investigated whether GVIN1, which has two GTPase domains, does indeed have GTPase activity and whether GVIN1 and GBP1 together completely block cell-to-cell spread by Burkholderia and thereby restrict bacterial numbers over the infection time course. They also do not show whether GBP1 and GVIN1 target the same bacterial cell or different populations of bacteria.

      A discussion of the likely impact of the work on the field, and the utility of the methods and data to the community:

      This work uncovers the antimicrobial actions of a member of yet another family of IFNg-induced GTPases, which potentially acts against other intracellular pathogens. GVIN1 appears to operate independently and in parallel to GBP1, pointing to the breadth and complexity of the IFNγ-inducible GTPase families.

      We thank the reviewer for their overall positive assessment of our work and their suggestions for additional studies. We addressed all the comments and in response we have added additional experimental data to the revised manuscript. However, while we agree that a detailed biochemical characterization of GVIN1 protein is warranted, we consider such experiments outside of the scope of the current work.

      Reviewer #3 (Public review):

      Summary:

      Here, Guo et al. (2025) propose that the IFN-induced GTPase GVIN1 forms a coat on cytosolic Burkholderia thailandensis, blocking actin tail formation through a mechanism analogous to GBP1-mediated restriction of Shigella motility.

      Their study was prompted by the intriguing observation that IFNγ priming and GBP1 coat formation fail to inhibit B. thailandensis actin-based motility in HeLa cells, yet IFNγ restricts the motility of Burkholderia in T24 cells. Further investigation revealed that IFNγ restricts B. thailandensis motility in T24 cells via both GBP1-dependent and -independent mechanisms, suggesting that HeLa cells lack a critical GBP1 co-factor required to inhibit actin tail formation.

      To identify the GBP1-independent mechanism, the authors performed an siRNA screen of interferon-stimulated genes (ISGs) and identified GVIN1, a large IFN-induced GTPase, as essential for restricting B. thailandensis motility. To identify the GBP1-independent mechanism, perform a knockdown screen for ISGs and find that the loss of GVIN, a very large IFN-induced GTPase, results in higher actin tail-positive B. thailandensis in T24 cells. They further demonstrate that GVIN forms coats on the surface of B. thailandensis, which prevent the polar localization of BimA and thus actin tail formation. In summary, the data reveal two independent IFNγ-induced pathways that restrict bacterial motility: one GBP1-dependent and the other GVIN1-dependent, each relying on distinct host co-factors.

      Global assessment:

      This is a well-executed study that convincingly demonstrates how GVIN1 restricts the actin-based motility of B. thailandensis through the assembly of coatomers. The results are clearly described, the manuscript is easy to follow, and the data are overall compelling and well presented. I have only a few suggestions on how the manuscript could be further improved.

      We thank the reviewer for a clear summary of our findings, and we appreciate the reviewer’s thoughtful suggestions on our manuscript, which we addressed in our revised manuscript.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      GVIN/VLIG was previously described in the mouse, mostly. Why was it considered a pseudogene in humans? Some more background should be provided.

      Major genome annotation projects (Ensembl, GENCODE, and RefSeq) rely on automated pipelines that flag loci as pseudogenes when they contain features incompatible with a single canonical open reading frame. These pipelines score in-frame premature stop codons, frameshifting indels, or the absence of a full-length matching transcript or protein in reference databases. The human GVINP1 locus displays several such features when compared against a naive single-ORF model of the mouse Vlig1 mRNA, and on that basis GVINP1 was likely categorized as a pseudogene by all three consortia, an assignment that has propagated through UniProt, HGNC, GeneCards, and OMIM ever since (UniProt Q7Z2Y8; GeneCards GVINP1). Importantly, these pipelines are not designed to detect loci that are expressed from more than one ORF or that produce a full-length protein through non-canonical translation, and they do not incorporate mass-spectrometry peptide evidence, ribosome profiling, or interferon-inducible expression data. Therefore, these automated pipelines can draw incorrect conclusions, as is the case here. We have added to the Introduction to provide a bit more background, as requested.

      Is GVIN restricting the proliferation of the Burkholderia strain in the tested human cell line(s)? Is it restricting the intra-host mobility of the bacteria?

      GVIN1 limits intracellular bacterial replication, albeit only modestly (see new data in Fig. S5B). We found that although GBP1 and GVIN1 block actin tail formation through independent, non-overlapping mechanisms, control of intracellular B. thailandensis burden required both proteins: IFN-γ failed to restrict bacterial replication in either GBP1KO or GVIN1KO T24 cells, and the loss-of-restriction phenotypes were quantitatively similar between the two knockouts (Fig. S5B). Together, these data identify GBP1 and GVIN1 as the effectors of two cooperating IFN-γ–induced defense pathways that jointly control B. thailandensis.

      P 10: Remarkably, GVIN1 coatomers formed only infrequently on the surface of the O-antigen-deficient delta wbpm B. thailandensis mutant (Figure 5F). This information is not included in Figure 5F (only the quantification in E) and could be added.

      We have added representative images of the corresponding microscopy data for both WT and DwbpM in a new Figure S8B.

      Reviewer #2 (Recommendations for the authors):

      Major points:

      (1) The finding of GVIN1 as a protein is important and deserves further characterisation. For instance, it would be useful to investigate the transcripts they find in RNAseq, start sites, length of transcript, etc. There are two GTPase domains in this protein, but is either of them active as a GTPase if key GTP-binding and/or hydrolysis residues are mutated?

      We agree that biochemical and enzymatic characterization of the GVIN1 protein is an important future direction. Similarly, careful investigations of GVIN1 expression, ribosome profiling, etc. ought to be conducted. However, these represent substantial, self-contained lines of investigation, and we will address them in a dedicated follow-up studies.

      (2) Throughout the paper, the authors have only investigated the proximal steps of actin-tail formation. They do not go on to measure the impact of bacterial targeting by GBP1 or GVIN1, specifically in terms of bacterial spread cell-to-cell and replication (e.g., CFU measurements over time) and the impact on pyroptosis. Does GBP1 and/or GVIN1 targeting reduce bacterial CFUs over time?

      re: 1) bacterial burden (CFU data); 2) host cell death (pyroptosis), and 3) cell-to-cell spread: 1) Our revised manuscript now provides CFU data (Fig. S5B) that identifies a modest impact on bacterial burden by GVIN1 expression – please, see also our response to Reviewer #1. 2) We already provided data in our original submission (Fig. S2D) demonstrating that IFNγ priming of either T24 WT or GBP1<sup>KO</sup> cells did not appear to change the degree of host cell death in infected cells, as measured by Lactate Dehydrogenase (LDH) release assays. Accordingly, no further studies into host cell death pathways seem warranted at this time. 3) B. thailandensis is unusual among cytosolic bacterial pathogens in that it can spread between host cells not only through actin tail–driven propulsion but also via flagellar motility (PMID: 21730143). Therefore actin-based motility is not essential for cell-to-cell spread for this specific organism (PMID: 21730143). Consistent with this dual-mode dissemination, IFN-γ priming of WT T24 cells had no measurable impact on plaque-based cell-to-cell spread (new data in Fig. S5A), despite sharply reduced actin tail formation inside IFN-γ primed WT T24.

      (3) The enumeration of microscopy could be improved by providing the % of GBP1+ve or GVIN1+ve bacteria that are actin-ve.

      We added those data presentations as new panels Fig. S2G for GBP1 and Fig. S7B. As expected, these data show that under IFN-γ primed conditions GBP1-coated or GVIN1-coated bacteria fail to form actin tails.

      (4) The authors show a schematic of GBP1 and GVIN1 targeting the same bacterial cell, but they have not demonstrated this experimentally. For many of their claims, it is important to show GVIN1 and GBP1 co-staining during infection with WT and the wbpM mutant Burkholderia.

      The schematic depicted GBP1 and GVIN1 on opposite sides of the same bacterium purely for illustrative clarity and was not intended to convey that GBP1 and GVIN1 necessarily coat the same bacterial cell. We agree, however, that whether GBP1 and GVIN1 coatomers can co-decorate a single bacterium is a mechanistically interesting question, and we have now addressed it experimentally. Dual immunostaining in IFNγ-primed cells showed that most targeted bacteria were encased by either a GBP1 or a GVIN1 coatomer, but not both (Fig. S7C). A small subpopulation of GBP1/GVIN1 double-positive bacteria was nonetheless detectable (Fig. S7C–D), indicating that the two coat types are largely, but not strictly, mutually exclusive. The rarity of dual-coated bacteria reinforces our conclusion that the two coatomers operate as predominantly independent effector systems, consistent with their ability to restrict actin tail formation independently of one another.

      (5) The authors make points about GBP1 and GVIN1 as being independent pathways and the need for a cofactor. To be certain about these conclusions, have they co-expressed both GBP1 and GVIN1 together in double knockout HeLa & T24 and assessed outcomes? They started out to look for a GBP1 cofactor that is required in HeLa cells, but they found GVIN1, which seems to operate independently of GBP1 (which is not inherently an issue, but I feel this needs to be clarified better). In T24 cells, expression of (mCh-)GBP1 alone without IFNg priming does reduce Actin+ve bacteria (Figure 2C, green bars), so GBP1 can use a factor that is expressed in naïve cells? But the authors have not shown that this factor is GVIN1. The same is true for GVIN1 expressed without IFNγ in T24-GVIN1-/- (Fig 5C). What happens in a similar experiment with an O-antigen mutant?

      We believe the individual experiments the reviewer proposes have, in fact, already been performed in some fashion and are presented in the manuscript. Because these experiments are distributed across several figures, we have taken this opportunity to summarize the logic here and to point the reviewer to the relevant panels.

      First, we would like to clarify the origin of GVIN1 in our study, as the reviewer's framing suggests that we set out to identify a GBP1 co-factor and instead landed on GVIN1. Our siRNA screen (Fig. 4A–B) was in fact designed to identify ISGs required for the GBP1-independent anti-actin-tail pathway and was therefore conducted in a GBP1<sup>KO</sup> T24 background. GVIN1 emerged as a factor whose depletion restored actin tail formation in the absence of GBP1, and it is therefore, by design of the screen, an effector of a GBP1-independent pathway rather than a candidate GBP1 co-factor.

      Second, we show that single deletion of either GBP1 or GVIN1 produces a partial and quantitatively similar de-restriction phenotype, whereas only the DKO fully abolishes IFNγ-mediated restriction of actin tail formation (Fig. 4C). Thus, we are seeing the classical additive signature of two non-redundant pathways acting on the same phenotype. In the gain-of-function direction, ectopic re-expression of GVIN1 in the DKO background restores IFNγ-dependent restriction to a level indistinguishable from the GBP1<sup>KO</sup> single knockout (Fig. 5D). A reciprocal experiment co-expressing both GBP1 and GVIN1 in the DKO would only test for additivity of two effects we have already shown to occur independently and would not provide an orthogonal test of independence beyond what Fig. 4C and Fig. 5D already establish.

      Third, we do not think GVIN1 is a likely candidate for the basal GBP1 co-factor that the reviewer infers from Fig. 2C. GVIN1 is IFNγ-inducible and effectively absent from unprimed T24 cells (the putative co-factor, while IFNγ-inducible, would be expected to be expressed at appreciable levels in naïve cells). Indeed, GVIN1 entered our screen precisely because of that inducibility (Fig. 4A and RNA-seq data in Fig. S3A–B). More decisively, we show that IFNγ-primed HeLa cells allow for ectopically expressed GVIN1 but not for ectopically expressed GBP1 to restrict actin tail formation. In other words, the ISG co-factor for the GVIN1 pathway must be distinct from the ISG co-factor for the GBP1 pathway. Lastly, we now show that GBP1 and GVIN1 coatomers are largely mutually exclusive, further arguing against GVIN1 acting as the GBP1 co-factor or vice versa in blocking actin tail formation.

      Fourth, the O-antigen mutant experiment the reviewer asked about has also been performed and provides another point of mechanistic separation between the two pathways. Ectopically expressed GVIN1 assembles a coatomer on WT B. thailandensis but only rarely on the ΔwbpM O-antigen-deficient mutant (Fig. 5F). This observation parallels (and thus mechanistically explains) why ΔwbpM is resistant specifically to the GBP1-independent (i.e., GVIN1-dependent) branch of IFNγ defense (Fig. 3E). GBP1, by contrast, engages both B. thailandensis WT and the O-antigen ΔwbpM mutant efficiently (new Fig. S8C).

      Taken together, four convergent lines of evidence (additive genetics in the DKO (Fig. 4C), cross-complementation of GVIN1 in the GBP1-null background (Fig. 5D), non-overlapping co-factor requirements in HeLa versus T24 cells (Fig. 2, Fig. 5), and distinct O-antigen dependencies for the two coatomers (Fig. 5E, Fig. 8C)) establish that GBP1 and GVIN1 constitute two parallel, independently operating antimicrobial modules, each likely with its own set of IFN-inducible co-factors.

      (6) The discussion does not currently discuss GBP1/Caspase-4-driven pyroptosis as a host-defence mechanism, which should be included. The authors should also discuss why Shigella and Burkholderia are differentially targeted, given the differences in the mechanism of actin polymerisation by IcsA and BimA.

      We previously showed that a GBP1 polybasic motif mutant that is unable to form coatomers on bacteria remains able to activate Caspase-4-driven pyroptosis and thus demonstrated that coatomers are not strictly required for GBP1-dependent Caspase-4 activation (PMID: 37023136). We now provide this information in the Discussion of the revised manuscript.

      We provide new data showing that GVIN1 forms coatomers on BimA-deficient and WT B. thailandensis with similar efficiency (new Fig. S8A) and we previously demonstrated that icsA plays no role in GBP1 coatomer formation (PMID: 33885766). Therefore, actin polymerization appears to play no role in either GVIN1 or GBP1 coatomer formation.

      Minor points:

      (1) Have the authors used anti-actin antibodies or phalloidin staining? Please clarify.

      We used phalloidin staining and this information is now also provided in the Results section (lines 118-119) in addition to the Materials and Methods section of the paper.

      (2) Provide the Gene ID, Ensembl ID, etc., for GVIN1 at first mention.

      We inserted the text: “Because automated annotation pipelines flag predicted in-frame stop codons, GVIN1 has long been catalogued as the pseudogene GVINP1 (GTPase, Very large IFN-Inducible Pseudogene-1) by Ensembl, GENCODE, and RefSeq (HGNC 25813; NCBI Gene 387751; OMIM 616121).” in the Introduction (lines 104 – 107)

      (3) The bond linking the core sugars with the O-antigen is missing in the schematic of LPS in Figure 3A. Please mention which sugars these are, if it is known for Burkholderia.

      We have corrected the schematic (Fig.3A) to include the bond linking the core sugars with the O-antigen.

      (4) RNA-seq datasets should be deposited to GEO or similar public databases, and project IDs provided.

      The RNA-seq datasets was deposited to the NCBI Gene Expression Omnibus (GEO), and the project accession IDs are is cited in the Data Availability statement.

      (5) The description of the transcriptomics analyses was not clear - are the heatmaps in Figure S3 of genes that were induced by IFNg in these cell lines, but not HeLa or A594, but the description states fold-change over naïve cells?

      The reviewer is correct and we apologize for the error in the figure legends, which we edited to clarify that the heatmap compares gene expression across IFNγ-primed cell lines.

      Reviewer #3 (Recommendations for the authors):

      Major comments:

      (1) It would be nice to include some additional analysis on GVIN: GBP1 and GVIN1 seem to recognize different structures and need different cofactors. Are they structurally similar (alignment)? Can you map functionally important GBP1 regions on GVIN1, such as a polybasic motif, similar to motifs found in GBP1? Or does GVIN have a lipidic membrane anchor or a CAAX box? In other words, is GVIN binding directly to the outer membrane or through the unknown cofactor? Is GVIN an effector of another protein that binds to the OM?

      Detailed structural studies including the mapping and biochemical characterization of GVIN1's membrane-targeting domain(s) represent substantial, self-contained lines of investigation that are beyond the scope of this study and that we hope to present in a future follow-up study.

      (2) In T24 cells, GVIN1 and GBP1 (and their cofactors) get induced upon IFNg priming. Upon B. thailandensis infection, is it possible to see mixed or double coats? Does GBP1 have a higher affinity for Shigella and GVIN for B. thailandensis? Is GVIN1 B. thailandensis-specific? It would be a nice addition to discuss other virulent Burkholderia species that make actin tails (such as B. pseudomallei) to further enhance the possible relevance of GVIN1.

      Please see our response to reviewer #2: dual immunostaining in IFNγ-primed cells showed that most targeted bacteria were encased by either a GBP1 or a GVIN1 coatomer, but not both (Fig. S7C). A small subpopulation of GBP1/GVIN1 double-positive bacteria was nonetheless detectable (Fig. S7C–D), indicating that the two coat types are largely, but not strictly, mutually exclusive. Re: the measurement of GBP1/ GVIN1 affinities for different bacteria – we agree that this is an area of future exploration but not within the scope of this study. Extending research on GVIN1 to other bacterial organisms including other Burkholderia species is indeed among our future research goals. We more broadly speculate on the potential importance of GVIN1-mediated host defense targeting other Burkholderia species in the Discussion (see lines 363 ff)

      (3) In panel F of Figure 6, It appears that GVIN forms full coats in the absence of IFNγ priming, but relocalizes to the bacterial poles upon IFNγ treatment. Is this shift in localization a representative and consistent observation, or could it be an artifact of the specific image selected? Additionally, could this relocalization be driven by the presence of IFNγ-induced cofactors? For example, might GVIN interact directly with BimA, or could an IFNγ-dependent cofactor mediate its recruitment to the poles?

      We believe the author is commenting on Figure 5F instead of 6 based on the question. The perceived shift in GVIN1 localization to the bacterial pole under IFNγ-primed conditions was not something we routinely observe and the original image shown in Fig. 5F is likely an outlier. We therefore replaced the original image with a more representative image.

      (4) The authors conclude that BimA is eliminated from the outer membrane, but it is unclear what evidence this conclusion is based on. Could it be that BimA is not eliminated, but rather becomes diffusely distributed in the membrane in the presence of GVIN1, and is therefore more difficult to detect by microscopy? One way to test this hypothesis would be to delete BimC. If BimA localization is indeed dependent on BimC, its signal should become diffuse. If a BimA signal can be detected in BimC-deficient bacteria, but not in GVIN-positive bacteria, it would indeed strengthen the claim that BimA is removed from the membrane.

      Prior literature demonstrates that on a bimC mutant, BimA remains detectable on the bacterial surface in a dispersed manner and that this dispersed BimA localization correlates with an "actin cloud" surrounding the bacteria. In our GVIN1-coated bacteria, we do not detect an actin cloud or residually localized BimA signals. We have now mentioned this in the Results section line 305 - 308 referencing this published phenotype to strengthen our argument that BimA is likely cleared from the membrane rather than merely redistributed.

      (5) The siRNA mini-screen would benefit from appropriate controls demonstrating that the targeted genes were effectively knocked down. Without this, it's difficult to interpret negative results with confidence. It remains possible that the co-factor of GVIN1 is among the ISGs tested, but that the knockdown was insufficient to produce a detectable phenotype.

      We now acknowledge this limitation. We have updated the text on lines 221-223 to explicitly state that our mini-screen does not rule out potential false negatives due to varying knockdown efficiencies.

      (6) The authors convincingly demonstrate that GVIN1 coats prevent actin tail formation by B. thailandensis, but they do not explore the broader biological consequences of this observation. An important next step would be to assess whether GVIN1 coating restricts B. thailandensis cell-to-cell spread. By 8 hours post-infection, a clear difference in spread should be observable if actin-based motility is impaired. Additionally, it would be valuable to determine whether GVIN1-coated bacteria are still capable of intracellular replication. These functional assays would provide important insight into the biological relevance of GVIN1-mediated coating.

      We have now assessed the effect of GVIN1 on intracellular bacterial replication (see new CFU data in Fig. S5B) and cell-cell motility (see new data in Fig. S5A). Please, also refer to our comments in response to Reviewer 1 for more details.

      (7) As far as I am aware, the exact function of the GBP1 coat remains unclear. The authors refer to their earlier work (Kutsch et al., 2020) and claim to have demonstrated an "emulsifying activity." However, this overinterpretes the findings of that publication, since Kutsch et al. (2020) showed that the GBP1 coat disrupts the barrier function of the O-antigen, rather than compromising the integrity of the outer membrane itself. This disruption increases bacterial susceptibility to polymyxin B, but does not show an 'emulsifying effect'. Furthermore, the same group later reported that GBP1 exhibits an "aggregating" activity on LPS micelles (Dickinson et al., 2023), which seems to contradict the notion of an emulsifying function. I would recommend tempering the current claims about GBP1's activity. The precise impact of the GBP1 coat on the bacterial outer membrane remains unresolved and should be presented as an open question.

      Our previous work demonstrated GBP1 coatomers on the bacterial surface disrupt the membrane-stiffening and membrane-shielding activities of O-antigen. We stand by the interpretation of our results and think it is likely that GBP1 coatomers act like surface-active agents or emulsifiers. However, we agree with the reviewer that more biophysical studies are needed to definitively test this model. Accordingly, we have revised some of the language and clearly articulated that GBP1 coatomers acting as a surfactant is a model that we are proposing.

      As the reviewer correctly stated we have also shown that GBP1 can aggregate “free” LPS, i.e. to act more like a flocculant. Substances that are both flocculants and surfactants exist (e.g. long-chain fatty acid soaps). However, these substances typically do not act as flocculants and surfactants simultaneously under the exact same conditions. Similarly, we propose that GBP1’s role depends on context: we propose that GBP1 coatomers on the bacterial surface act as surfactants, while polymerizing GBPs bound to LPS acts a flocculant.

      Minor comments:

      (1) Figure 3: Can a GBP1 coat assemble on the delta wbpM mutant of B. thailandensis? The authors suggest GBP binds to the O-antigen, but other publications suggest that the O-antigen is dispensable in certain bacteria.

      We conducted these experiments – see also our response to reviewer #2. Briefly, ectopically expressed GVIN1 assembles a coatomer on WT B. thailandensis but only rarely on the ΔwbpM O-antigen-deficient mutant (Fig. 5F). GBP1, by contrast, engages both B. thailandensis WT and the O-antigen ΔwbpM mutant efficiently (new Fig. S8C). We do not argue that GBP1 requires O-antigen binding for coatomer formation on Burkholderia. However, direct or indirect interactions between GVIN1 and O-antigen may be required for GVIN1 coatomer formation.

      (2) Figure 4: GBP6 appears as a hit in the T24 screening but turned out to be a false positive. How does that look in the other cell lines that were part of the screen (U937, THP1)?

      the characterization of T24 GBP6<sup>KO</sup> cells clearly demonstrated that GBP6 is dispensable for either the GBP1 or the GVIN1 pathway in these cells. While we cannot formally rule out that GBP6 would be required for the GBP1/GVIN1 pathways in other cell lines, there are no compelling arguments in favor of this model – as far as we can tell - and we therefore did not investigate this further.

      (3) Figure 5F: Please show the blots confirming exogenous GVIN expression.

      We have provided an immunoblot showing the expression of exogenous GVIN1in HEK293T cells in new Fig. S7A

      (4) Figure 6: Can you induce GVIN expression after actin tails have been formed and stop disassembling them?

      This is an interesting idea and will require a technically challenging video microscopy approach that we will consider for future investigations.

      (5) Figure 6: Are the bacteria showing no BimA signal GVIN1-coated? Eventually, stain for LPS to see if bacteria are lacking BimA also lack LPS.

      Our preliminary studies indeed support this and thus indicate that the elimination of BimA from the bacterial surface requires the concerted effort of the GVIN1 coatomer and its putative co-factor (or the GBP1 coatomer and its putative co-factor, respectively). A detailed characterization of the mechanism by which BimA is removed from the bacterial surface will be part of future studies.

    1. Author response:

      The following is the authors’ response to the previous reviews.

      Public Reviews:

      Reviewer #2 (Public review):

      Summary:

      This paper attempts to examine how rare, extreme events impact decision-making in rats. The paper used an extensive behavioural study with rats to evaluate how the probability and magnitude of outcomes impact preference. The paper, however, provides limited evidence for the conclusions because the design did not allow for the isolation of the rare, extreme events in choice. There are many confounding factors, including the outcome variance and presence of less-rare, and less-extreme outcome in the same conditions.

      Strengths.

      (1) The major strength of the paper is the significant volume of behavioural data with a reasonable sample size of 20 rats.

      (2) The paper attempts to examine losses with rats (a notoriously tricky problem with non-human animals) by substituting time-outs as a proxy for losses. This allows for mixed gambles that have both gain and loss possible outcomes.

      (3) The paper integrates both a behavioural and a modelling approach to get at the factors that drive decision-making.

      (4) The paper takes seriously the question of what it means for an event to be rare, pushing to less frequent outcomes than usually used with non-human animals.

      Weaknesses:

      (1) The primary issue with this work is that the primary experimental manipulation fails to isolate the rare, extreme events in choice. As I understand the task, in all the conditions with a rare extreme event (e.g., 80 pellets with probability epsilon), there is also a less-rare, less-extreme event (e.g., 12 pellets with probability 5). In addition, the variance differs between the two conditions. So, any impact attributable to the rare, extreme event could be due to the less rare event or due difference in the variance (or other statistical moments, like skew or kurtosis). That the distributions can be shown to be different under specific assumption to value maximizing agents (e.g., with Jensen Gaps and Table 2) is not really relevant to what rats are sensitive and what drive their behaviour. The design here does not support the conclusions. Finally, by deliberately confounding rarity and extremity, the design does not allow for assessing the impact of either aspect on rat behaviour.

      This is a repetition almost word for word of point (1) appearing in your previous report, which we have addressed at length in our first-round reply. Therefore, we do not reiterate here to save space.

      (2) The RL modelling work also fails to show a specific impact of the rare extreme event. As best as I can understand Eq 2, the model provides a free parameter that adds a bonus to the value of either the two options with high-variance gains (A and V in the paper) or to the two options with high-variance losses (F and V in the paper). Or equivalently to the ones with "Jackpots" vs the ones with "Black Swans" (see Point 1 above as to how these different aspects are all confounded in this design). This parameter seems to only depends on whether this option could have possibly yielded the rare, extreme outcome (i.e., based on the generative probability) and was not connected to its actual appearance. [This point is unclear as the text says this, but the rebuttal states otherwise; plus some options never received the REE, see Table S11]. That makes it a free parameter that just bumps up (or down) the probability of selecting a pair of options. That may be due to presence of the REE or the other rare event or just the variance difference. Moreover, in the case of the "black swan" or high-variance loss conditions, this seems very much like a loss aversion parameter, but an additive one instead of a multiplicative one. Is there a theoretical claim here that "extreme losses" need an additive loss-aversion parameter?

      This is a repetition almost word for word of point (2) appearing in your previous report, which we have addressed at length in our first-round reply. Therefore, we do not reiterate here to save space.

      (3) The paper presented the methods and results with lots of neologisms and fairly obscure jargon (e.g., fragility, total REE sensitivity). That might it very hard to decipher exactly what was done and what was found. For example, on p. 4, the use of concave and convex was very hard to decipher; the text even has to repeat itself 3 times (i.e., "to repeat" and "in other words") and is still not clear. It would be much clearer (and probably accurate) to say that the options varied along the variance dimension, separately for gains and losses. Option A was low-variance gains and losses. Option B was low-variance losses and high-variance gains. Option C was high-variance losses and low-variance gains, and Option D was high-variance losses gains. That tells much more clearly what the animals experienced without the reader having to master a set of new terminologies around fragility and robustness, which brings a set of theoretical assumption unnecessarily into the description of the experimental design. Alternatively, if the authors are wary of using the term "variance" because other moments of the distribution also differ, they could use "high-value gains" or "high-value losses" or something else which does not obscure the experimental design with jargon. Again, this goes back to point 1 above, whereby the different options differ on so many dimensions (as is made even more apparent in the rebuttal) that the design cannot isolate the impact of the variables of interest.

      This is a repetition almost word for word of point (3) appearing in your previous report, which we have addressed at length in our first-round reply. Therefore, we do not reiterate here to save space. The new words that we use are an attempt at reflecting the novelty of the approach and design.

      (4) Were the probabilities shuffled or truly random (seem to be fixed sequences, so neither)? What were the experienced probabilities? Given the fixed sequences, these experienced ("ex-post") probabilities, could differ tremendously from the scheduled ("ex ante") probabilities. It's quite possible than an animal never experienced the rare, extreme event for a specific option. From Table S11, that is guaranteed to have happened in that 4 animals only ever experienced the "black swan" outcome once. It's even possible (if they only picked a specific option on the 10th/60th choices by chance), that they only ever experienced that rare extreme event. This point still cannot be known given the information provided, which does not break down outcomes by options. The Supplemental in Table S11 only gives overall numbers but does not indicate what the rats experienced for each choice/option-which is what matters here. A simple table that indicates for each of the 4 options, how often they were selected, and how often the animals experienced each of the 6-8 possible outcome would make it much clearer how closely the experience matched the planned outcomes. In addition, by restricting the rare outcome to either the 10th or 60th activations in a session, these are not random. Did the animals learn this association? The text states that they did not, but no evidence is provided.

      This is a repetition almost word for word of point (4) appearing in your previous report, which we have addressed at length in our first-round reply. Therefore, we do not reiterate here to save space.

      (5) The choice data are generally presented in an over-processed fashion with a sum and a difference (in both figures and tables). The basic datum (probability/frequency of selecting each of the 4 options) is not provided directly in the main text, even if it can theoretically be inferred from the sum and the difference. New right side of Table S4 is probably the most valuable piece in terms of explaining what rats did and should be highlighted a lot more. Inspection of that table reveals some interesting (and potentially worrying) results. Most notably, the vast majority of responding happens on the "anti-fragile" and "robust" option, often totalling around 90% of all selections, especially amongst the most common blue rats. Alas, those were all those the two options that were deliberately assigned to the two most preferred holes in the training phase (see p. 26). Does this reflect genuine preference for reward distributions or does this reflect a spatial hole bias? The assignment strategy makes this impossible to tell apart.

      This is a repetition almost word for word of point (5) appearing in your previous report, which we have addressed at length in our first-round reply. Therefore, we do not reiterate here to save space. In addition, in Figure 8 of Material and Methods, we report the changes in behavior between the training and final sessions. The related discussion stresses that half of the rats changed more than 30% of their choices in the final experimental sessions compared to the training sessions. See also our previous reply to point (8).

      (6) There is insufficient detail provided on the inferential statistical tests (e.g., no degrees of freedom or effect sizes), and only limited information on exactly what tests were run and how (bootstrapping, but little detail). Without code or data (only summary information is provided in the supplement), this is difficult to evaluate. In addition, the studies seem not to pre-registered in any way, leaving many research degrees of freedom. Not all studies need to be pre-registered and sometimes discovery of new things requires exploratory work, but preregistration does provide additional safeguards against overemphasizing post-hoc detected patterns-a serious issue in behavioural science. Moreover, this promotes transparency in reporting results and analyses, allowing for a better assessment of the strength of evidence for a claim. For example, here, were any alternative analysis pipelines attempted? Also, there were many sub-groupings of the animals and subsequent comparisons between them which all seemed post-hoc. On what grounds were these divisions made-were other divisions examined as well?

      This is a repetition almost word for word of point (6) appearing in your previous report, which we have addressed at length in our first-round reply. Therefore, we do not reiterate here to save space.

      (7) On p. 12 (Fig 4), there is an attempt to look at the impact of a rare, extreme event by plotting a measure of preference for the 10 trials before/after the rare, extreme event. In the human literature, the main impact of experiencing a rare, extreme event is what is known as the wavy recency effect (See Plonsky et al. 2015 in Psych Review for example, now cited). What this means is that there tends to there tends to be some immediate negative recency (e.g., avoiding a rare gain) followed by positive recency (e.g., chasing the rare gain). Typically, this refers to the specific option that yielded that outcome. First, as the other analyses do, the current analysis combines choice of the option that yielded the rare outcome with choice of other options, so that cannot directly assess the impact of the rare, extreme event on choice. Also, using a 10-trial window would thus obscure any impact of this rare, extreme event. There is mention of the very next trial, but an analysis that looks at the 10-trial time course trial-by-trial could reveal any impact that might be predicted from the human literature.

      This is a repetition almost word for word of point (7) appearing in your previous report, which we have addressed at length in our first-round reply. Therefore, we do not reiterate here to save space.

      (8) As I understood the method (p. 31), the assignment of options to physical locations was not random or counterbalanced, but deliberately biased to have one of the options in the preferred location. This would seem to create a bias towards a particular option and a bias away from the other options, which confounds the preference data in subsequent analyses. Table S4 reinforces this concern where the vast majority of response are clustered in the two most preferred options from training.

      This is a repetition almost word for word of point (8) appearing in your previous report, which we have addressed at length in our first-round reply. Therefore, we do not reiterate here to save space.

      (9) Are delays really losses? This is a big assumption. Magnitude and delay are different aspects of experience, which are not necessarily commensurable and can be manipulated independently. And, for the model, how were these delays transformed into outcomes for the model. Eq 1 skips over that. Is there an assumption of linearity? In addition, I was not wholly clear if the delays meant fewer trials in a session or if the delays merely extended the session and meant longer delays until the next choice period.

      This is an exact repetition of point (9) appearing in your previous report, which we have addressed at length in our first-round reply. Therefore, we do not reiterate here to save space.

      Other points:

      (1) I think the authors still misunderstand the concept of "hot-stove effects". The idea is that the experience of a very bad outcome can lead to avoiding the situation again (i.e., not sampling that option) and can provide the appearance of oversensitivity to that bad outcome. Here, that might be more thought as "black-swan avoidance". Imagine if, to the rat, all options are equal in value, then some initial bad luck in encountering the black swan might make the animal avoid that option, even though with enough experience, then it would have been equal in value.

      This point is reminiscent of recommendation (5) appearing in your previous report, which we have addressed at length in our first-round reply. Therefore, we do not reiterate here to save space.

      (2) I am still not convinced that the Jensen inequalities add to this paper in terms of understanding the rat behaviour. That may be more suited for a different paper about the statistical and mathematical properties of certain generative distributions, but not here given what rats actually choose and experience.

      This point is reminiscent of recommendation (8) appearing in your previous report, which we have addressed at length in our first-round reply. Therefore, we do not reiterate here to save space.

      (3) Providing the data open access is very good. The code, however, should be equally available and not just upon request. Code needs to be available for assessment during peer review and for reproducibility checks. There are substantial enough problems with reproducibility in the field that code availability should be a minimum criterion for publication (see Miske et al., 2026 in Nature for the most recent large-scale evaluation of this problem).

      This point is reminiscent of recommendation (9) appearing in your previous report, which we have addressed at length in our first-round reply. Therefore, we do not reiterate here to save space.

      (4) The paper still somewhat mischaracterizes the literature on rare events, posing it as a series of "exceptions", rather than recognizing that a huge chunk of the literature uses rare events rarer than 10%. Also, there is even existing terminology in that literature for exactly the situation that is being created here-rare treasures (aka jackpots here) and rare disasters (aka Black Swans here).

      This is reminiscent of point (10) appearing in your previous report, which we have addressed at length in our first-round reply. Therefore, we do not reiterate here to save space.

      (5) Defining the observed behaviour in terms convexity, instead of stating choices more plainly obscures what is done/found. This is especially the case here because convex and concave mean different things when applied to gains/losses in terms of whether or not that option can lead to the REE. The use of the terms obscures rather than clarifies and probably is best left for the discussion (and maybe the intro) when mapping from theoretical distributions to the experiment at hand. In the paper, even the bottom of p.5 seems to incorrectly define "Total Sensitivity" as the combined proportion of selecting convex options in either domain, which does not map how convex is defined in Fig 1B or elsewhere in the text.

      This is reminiscent of point (3) appearing in your previous report, which as stated above we have addressed at length in our first-round reply. Therefore, we do not reiterate here to save space.

      (6) Fig 1C is baffling. Why are probabilities drawn moving away from the origin? The standard scientific plotting convention is for numbers to grow when moving away from the origin. That would be vastly clearer. Also, the color coding is confusing. Green-red maps onto convex-concave, but that would naturally seem to indicate gains vs losses, not convex vs concave. And why are probabilities growing larger in both directions from the origin? Much more sensible to communicate the procedure would likely be a standard plot of magnitude vs probability.

      As explained in the main text of the article, panel (c) in Figure 1 reveals an important and novel feature of the design: gains and losses are either convex or concave in decreasing probabilities, meaning that the gain/loss gets more rare, it becomes larger (if convex) or smaller (if concave) in a nonlinear fashion.

      (7) Discussion: I think the main difference between the human situations discussed and this experiment is that humans have not experienced those rare "black swan" outcomes. Rather, they hear about the disasters that are possible and do not incorporate that information, as discussed in the description-experience literature already cited in this paper (though not in that context).

      We thank the referee for pointing this out. However, it is not clear to us that the various trauma experienced in real life by humans do not share properties with Black Swans in our experimental design.

      Recommendations for the authors:

      Reviewer #2 (Recommendations for the authors):

      Small points:

      - p. 4. Options are not strategies. Picking two out of the 4 options more often, is not picking two strategies. That's picking two options (also on p. 7, but really throughout).

      This has been changed in the text.

      - The sums don't add up in probability of outcomes. How were they 0.9, 0.1, 0.01? What were they exactly? What exactly is epsilon?

      Exact probabilities, which of course add up to one, are given in Material and Methods (page 29).

      - The term "one-sided sensitivity" to refer to the selection of options include rare-extreme outcomes is also confusing. There are many other words that might work better here, including "encounter", "choice", "selection", or even "preference".

      One-sided Sensitivity if a proposed measure of the choice asymmetry, as explained in the text (pages 5-6, including caption of Figure 1).

      - I don't think that Figure 3 is more intuitive. It's still a summed measure, with rats sub-divided into post-hoc groups. Also, aren't the groups divided precisely in part by the selections that are being shown in this plot?

      There is no claim that Figure 3 is more intuitive. As explained in Material and Methods (pages 33-34), it provides an alternative way to represent behaviors (BSA/JPS vs TSREE/OSREE).

      - Fig 3 has no black or dark and light grey. There is no one asterisk in the figure. The light grey is irrelevant because all bars must sum to 1. No error bars or equivalent on the plot.

      Dark and grey bars sum to one but have a different interpretation, as explained in the text (pages 10-11). We have dropped the one asterisk reference.

      - p. 14. Technicality, but alpha need not be bound at 1 for a convergent equation. It only needs to be bound at 2 (real maximum value). Above 1 (but below 2) would be a type of overcompensation that would also converge at same Q value.

      The assumption that alpha is positive and bounded by one is common in the literature and is important for stochastic convergence. Assuming that alpha is between one and two has undesirable implications, beyond possible non-convergence, in particular that Q values may fluctuate.

      - p. 24. What was the generative frequency (not experienced frequency). Not adequately explained. Less than half a percent of all outcomes? Of all times that the relevant choice was made. This is not explained.

      The sequences used to generate gains and losse are detailed in the Supplementary Material.

      - p. 4. Says 41 sessions, but methods say 40 (e.g., Fig 7 and surrounding text)

      This has been corrected in the text.

      - My understanding of Tables S5 and S6 is that the best models did not include REE in Q sub-values. That seems to be opposite to the textual conclusion.

      As stated in Table 1 (page 15), which summarizes results in Tables S5-S6, the selected models for rats 3, 11, and 12 do not integrate REE while the selected models for rats 4, 16 and 20 integrate REE though Q values and REE decision weights. For most rats, REE are integrated in the selected models through the latter only.

      - What are the parameters in Table S7? The full 8-parameter model? But how are these the ones selected by BIC as per caption? Also, there are a number of anomalous values-lots of 1s and 0s, plus a +40 on the value of the losses for Rat 20. Columns are always gain then loss except first column.

      We report in Table S7 all estimated parameters for each rat, but only for the model selected by the BIC criterion (see Table S5). Admissible values for alphas include 0 and 1. All estimates have been checked for identification. The first and second columns have been switched to have gain first.

      - Table S11 does not subdivide by option selected. So, we cannot tell if the rats actually experienced the outcome distribution associated with some options.

      Given the large number of nosepokes generated by each rat, reporting all actual gains and losses would consume too much space. On the other hand, given that each option has only three frequent and rare values, it is expected that each will be experiences by each rat, in view of the choice frequencies reported in Table S2 (page 52).

    1. Author response:

      The following is the authors’ response to the original reviews.

      eLife Assessment:

      The study provides an important advance towards understanding how spatial and temporal transcriptional programs are integrated to regulate lineage-specific chromatin and enhancer activation. The functional evidence is currently incomplete, but the current data provide a solid correlative and conceptual foundation. Functional experiments directly linking Gsb occupancy to chromatin state and regulation of some lineage-specific targets would further strengthen the causal interpretation of the model. Clarifying the scope of conclusions and explicitly acknowledging the technical limitations of current chromatin assays would provide a more balanced interpretation of the manuscript.

      We thank the reviewers and editors for their comments on our manuscript. We address here the concerns raised by them.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      It has long been known that Drosophila embryonic ventral nerve cord neuroblasts incorporate both spatial and temporal transcription factor expression to generate 30 distinct neuroblasts and lineages per hemisegment. This manuscript aims to elucidate the mechanism by which this integration of spatial and temporal transcription factors occurs through "direct regulation" or "epigenetic regulation". Direct regulation is defined as both spatial and temporal factors binding to open chromatin and working together to dictate specific lineages. Epigenetic regulation is defined as a spatial factor priming the chromatin in a neuroblast-specific manner to allow for the integration of temporal factors to generate specific lineages. The authors conclude that there is a two-step model in which a spatial transcription factor code "primes" the chromatin in terms of accessibility and then recruits temporal factors to ensure lineage-specific enhancer activation.

      We thank the reviewer for this clear and succinct summary and for accurately capturing the central idea of the model we propose. In particular, we appreciate that the reviewer highlights the distinction between the previously proposed “direct regulation” and “epigenetic regulation” models, which our work suggests may operate together within neuroblast lineages through a combinatorial spatial transcription factor code — a model we refer to as the “distributed STF code model”.

      Strengths:

      The authors tested two models, "direct regulation" vs "epigenetic regulation" in a well-defined pool of neural stem cells during normal development.

      We thank the reviewer for recognizing this aspect of the study.

      Weaknesses:

      The data in this study cannot clearly substantiate these two models.

      Overall, there are a number of issues that are inconsistent and not supportive of the model proposed in this manuscript. Firstly, there is no evidence of pioneer factor activity in any of the NB lineages described - i.e., any changes in chromatin accessibility being shown over time. The authors must show chromatin conformation changes during the window of spatial transcription factor expression in order to convince the readers of this phenomenon.

      Thank you for raising this point. We agree that a developmental time course of chromatin accessibility would be very informative. The difficulty is that, in this system, the relevant sequence unfolds extremely rapidly and across two cellular contexts. Spatial transcription factors such as Gsb are expressed in the neuroectoderm; NBs then delaminate, and Hb expression begins almost immediately — on the order of minutes to tens of minutes. Before delamination there is no NB that can be targeted with lineage-specific drivers, whereas after NB formation the temporal program is already under way. This transition therefore cannot currently be resolved using lineage-restricted Dam profiling.

      In most studies, however, pioneer or chromatin-priming activity is inferred from a transcription factor’s ability to bind regions of relatively low accessibility and alter accessibility in a heterologous cellular context, rather than from direct developmental timecourse measurements. Our study provides both types of evidence: Gsb occupies accessible and relatively less-accessible regions in NB5-6 (Figure 4), while ectopic Gsb expression in NB7-4 causes bidirectional chromatin remodelling, with corresponding changes in Hb occupancy (Figure 6 and Figure 6—figure supplement 2).

      In light of this technical constraint, and in response to the reviewer’s broader concern, we have revisited our original interpretation. We now emphasise Gsb’s ability to alter chromatin accessibility bidirectionally and use the term “chromatin priming” rather than “pioneering.” We also make clear that Gsb does not act alone to establish the NB5-6 chromatin landscape, but functions within a broader, distributed STF code.

      Some examples of relevant manuscript changes are:

      - “We found, however, that Gsb’s role in chromatin remodelling was more complex: ectopic Gsb remodelled chromatin bidirectionally with regions both losing and gaining accessibility upon Gsb misexpression.”

      - “Thus, Gsb’s chromatin-remodelling capacity is not equivalent to autonomous opening of lineage-appropriate enhancers. Rather, these data support a model in which Gsb contributes to chromatin priming as part of a broader NB-specific STF code…”

      - “Thus, Gsb can engage loci and directly restrict chromatin accessibility at bound sites, but its ability to promote accessibility and Hb recruitment likely requires additional NB5-6-specific inputs.”

      Secondly, the phenotypic data do not align with the sequencing data - the story would be more cohesive if the sequencing data and phenotypic data were in the same NB subtypes. On one hand, we are shown that Gsb misexpression induces loss of chromatin accessibility in NB 7-4, however in the widespread loss model, we are not shown a phenotype in these NB7-4 - which suggest that the chromatin accessibility at these sites (sites that have already been distinguished as SoIs for that NB subtype) does not play an important role in distinguishing NB 7-4 identity. However, the authors report loss of NB3-5 identity but have no evidence as to how the chromatin has changed (or if it has at all) in that subtype, leaving the readers to wonder how the loss of identity occurred

      Thank you for raising this point regarding the alignment between the chromatin and phenotypic analyses. The reviewer’s comment made us realise that the rationale for these experiments may not have been sufficiently clear in the original manuscript and could therefore be perceived as misaligned. We therefore explain the logic of the experimental design here and have edited the manuscript to clarify this point for readers.

      The chromatin experiments were designed to test whether Gsb is capable of remodelling chromatin when introduced outside its endogenous domain. NB7-4 provided a convenient heterologous context with clean genetic access for TaDa/CATaDa profiling.

      Importantly, although NB7-4 was selected primarily for this technical reason, Gsb misexpression did affect NB7-4’s identity readout: at higher induction levels, the NB7-4-specific Gal4 reporter was lost. Because this same driver was required for lineage-restricted chromatin profiling, we titrated Gsb misexpression to a lower level that preserved reporter activity while still allowing us to assay chromatin accessibility and Hb occupancy. This calibration is documented in the new Figure 6—figure supplement 1. Thus, the calibrated profiling condition should not be interpreted as evidence that Gsb has no effect on NB7-4 identity; rather, it was necessary to retain genetic access to the lineage.

      The phenotypic experiments addressed a different question: the developmental requirement for Gsb within its endogenous spatial domain. Our analysis was therefore centred on NB5-6. Gsb depletion caused loss of the NB5-6-specific Lbe reporter and the NB5-6 neuronal markers Ap and Eya, whereas Gsb misexpression produced a partial gain of these markers (Figures 7 and 8). The accompanying changes in row-3/NB3-5 markers emerged as an additional reciprocal phenotype, consistent with Gsb established role in specifying row-5/6 identity while repressing row-3 fates, rather than as an independent endpoint that we had selected.

      Thus, the chromatin and phenotypic experiments are complementary: the NB7-4 experiment tests Gsb’s capacity to remodel chromatin in a convenient heterologous context, whereas the NB5-6 experiments establish its developmental function within its endogenous domain. We have revised the manuscript to make this distinction explicit.

      Relevant edits made to manuscript:

      “Having shown that ectopic Gsb remodels chromatin and alters Hb occupancy in the NB7-4 lineage, we next asked whether altering Gsb function changes NB lineage identity. The misexpression experiments described above had already shown that, when induced at high levels, Gsb misexpression turned off the NB7-4-lineage Gal4 reporter, consistent with Gsb suppressing NB7-4 identity at sufficient levels. In the chromatin-profiling experiments above, this was addressed by inducing lower Gsb misexpression levels that preserved Gal4 expression. Together, these observations suggested that Gsb misexpression can influence lineage identity as well as chromatin state. However, since NB7-4 is not an endogenous Gsb-expressing context, we turned to NB5-6 to test the developmental consequences of altering Gsb function.”

      Reviewer #2 (Public review):

      Summary:

      This article by Bhattacharya et al. investigates how neural stem cells (NSCs, NBs) in Drosophila integrate spatial and temporal cues to activate neuron-specific terminal selector (TS) genes. Prior to this work, it was understood that NSCs utilize spatial transcription factors (STFs) and temporal transcription factors (TTFs) to determine lineage identity and birth order, but the mechanisms of integration were not fully elucidated. The authors employed chromatin profiling techniques to analyze the binding of STFs and TTFs in two specific neuroblast lineages, NB5-6 and NB7-4. They found that Gsb (an STF) binds both accessible and less-accessible chromatin in NB5-6, while En (another STF) binds only to pre-accessible chromatin in NB7-4. The findings support an "STF code" where the combination of pioneer and non-pioneer spatial factors, along with temporal factors, triggers neuroblast-specific enhancer activation and determines lineage identity.

      We appreciate the reviewer’s careful summary of our findings and their clear articulation of the STF-code framework that emerges from the work.

      Strengths:

      The experiments are well-executed, the interpretations are generally sound, and the figures are clear and elegant. However, some conclusions are drawn too broadly without essential functional data. Therefore, additional work is needed to more effectively convey the central message.

      We thank the reviewer for their positive assessment of the experiments, interpretation, and figures, and we respond to their specific concerns below.

      Weaknesses:

      (1) Integration of TaDa and functional data on Gsb for the STF model

      The authors demonstrate that TaDa profiling maps Gsb binding across the genome and identifies candidate chromatin-priming sites in NB5-6. Gsb LOF/GOF experiments reveal effects on NB identity. Combining TaDa data with LOF and GOF analyses indicates that Gsb influences NB5-6 specification by binding to both open and relatively closed chromatin, helping maintain NB5-6 identity while limiting NB3-5 fate.

      However, the study does not establish a direct link between specific LOF/GOF phenotypes and particular genomic targets. For instance, analyzing Gsb occupancy at lineage-specific identity factors or terminal selector genes (such as Lbe, Ap, or Eya for NB5-6; and Ems, etc., for NB3-5) in wild-type and manipulated conditions (Gsb misexpression) would directly connect chromatin binding to the regulation of fate determinants. These investigations would strengthen the mechanistic connection between the correlative TaDa profiles and the observed identity changes, supporting the idea that Gsb functions as a context-dependent chromatin-priming factor within the STF code, rather than as a generic transcription factor.

      We thank the reviewer for this suggestion. We agree that examining Gsb occupancy at known lineage determinants helps connect the genome-wide TaDa profiles to the developmental phenotypes. We have therefore added browser profiles showing endogenous Gsb occupancy at several loci associated with NB5-6 identity and its neuronal output, including lbe, ap, and eya (new Figure 2E). These are the same markers that are lost following Gsb depletion and partially gained following Gsb misexpression (Figures 7 and 8), providing a locus-level connection between Gsb binding and the observed changes in NB5-6 identity.

      The precise comparison suggested by the reviewer is difficult because the binding and misexpression experiments were necessarily performed in different contexts. Gsb occupancy was measured in NB5-6, where Gsb is normally expressed, whereas the effect of Gsb misexpression on chromatin was measured in the heterologous NB7-4 context where Gsb is not normally expressed. We therefore did not measure Gsb occupancy following its misexpression in NB7-4 and so cannot compare Gsb binding before and after misexpression at individual loci in NB7-4.

      We have nevertheless added genome-browser examples showing how Gsb misexpression affects accessibility and Hb occupancy at lineage-associated loci (new Figure 6M). The ems locus provides one such example: ectopic Gsb reduces both accessibility and Hb occupancy at ems in NB7-4, while broad Gsb misexpression causes loss of Ems expression and of the independent NB3-5 reporter R59E09>GFP in the phenotypic experiments (Figure 8).

      (2) Gsb misexpression reveals bidirectional chromatin remodelling

      Experiments with ectopic Gsb expression demonstrate bidirectional chromatin remodelling in NB7-4, showing decreases in accessibility at some binding sites and increases at others. While the authors show that Gsb can disrupt chromatin upon misexpression, interpreting its "pioneer-like" or chromatin-priming activity is complex due to several factors: the misexpression occurs in a non-native lineage, the direct versus indirect effects rely on whole-embryo Dam-Gsb peaks instead of NB7-4-specific binding, and heat-shock-induced chromatin changes are not fully accounted for. These issues make it challenging to definitively determine Gsb's role in chromatin priming.

      A complementary approach would be to perform Gsb knockdown/loss-of-function in its native NB5-6 lineage and profile chromatin accessibility (TaDa or CATaDa). This would allow a cleaner, more physiologically relevant assessment of Gsb's contribution to priming, SoI establishment, and Hb recruitment. Such an experiment would strengthen the causal link between Gsb occupancy and chromatin state and clarify whether Gsb truly acts as a context-dependent pioneer in vivo, rather than producing indirect effects due to ectopic misexpression.

      We thank the reviewer for this thoughtful comment. The reviewer raises four related but distinct issues, which we address separately below.

      (1) Gsb was misexpressed in a non-native lineage

      As discussed in our response to Reviewer 1 regarding pioneer activity, expression in a heterologous cellular context is a standard experimental strategy for testing whether a transcription factor has the capacity to engage and remodel chromatin outside its endogenous setting. The use of NB7-4 was therefore deliberate: this experiment tested the sufficiency of Gsb to alter chromatin, rather than attempting to reproduce its physiological activity in NB5-6. Nevertheless, because Gsb produced bidirectional changes rather than autonomous chromatin opening, we have revised our interpretation. We now describe this experiment as demonstrating chromatin remodelling capacity and use “chromatin priming” rather than claiming a classical pioneer for its activity.

      Relevant edits made to the manuscript: Results, Figure 7 and Figure 7—figure supplements 1 and 2.

      (2) Direct and indirect effects were inferred using whole-embryo Gsb occupancy

      We have not profiled Gsb occupancy directly in NB7-4 following its misexpression. However, we have now performed an unbiased genome-wide analysis using two independent Gsb-binding datasets: stage-matched Gsb occupancy from NB5-6 and whole-embryo Gsb occupancy. Since Dam methylation is cumulative across the window of Gal4 activity, the whole-embryo dataset serves as a proxy for embryowide sites that are compatible with Gsb occupancy. Across both datasets, the result was strikingly consistent. The set of 1,340 loci that lost accessibility upon Gsb misexpression showed strong Gsb occupancy in both datasets, whereas the 606 loci that gained accessibility showed little or no Gsb occupancy in either dataset (Figure 6E,H). Thus, two independently generated Gsb-binding maps systematically distinguish the loci that close from those that open.

      This reproducibility — across many sites and two datasets — provides strong evidence that accessibility loss occurs at loci that Gsb can bind and is therefore likely to reflect a direct consequence of Gsb activity. Conversely, lower Gsb occupancy at sites that gain accessibility suggests that these gains are more likely to be indirect. The corresponding changes in Hb occupancy further strengthen this interpretation (Figure 6C–G).

      In summary, we find it particularly compelling that two independently generated Gsb-binding maps, obtained at different developmental stages and in different cellular contexts, identify the same systematic distinction: loci that close upon Gsb misexpression are Gsb-bound, whereas loci that open are not. We therefore consider this a strong and unbiased result supporting a direct role for Gsb in chromatin closing.

      Relevant edits made to the manuscript: (Results; Figure 6E, H)

      “Although we did not directly profile Gsb occupancy in NB7-4 upon misexpression, we asked whether the sites that lose or gain accessibility differ in their propensity to be bound by Gsb. To do this, we mapped independent Gsb occupancy datasets onto these two classes of remodelled sites: stage-matched Dam: Gsb from NB5-6, where Gsb is normally expressed, and whole-embryo Dam: Gsb, which provides a broader map of Gsb-compatible loci. In both datasets, sites that lost accessibility upon Gsb misexpression in NB7-4 showed strong Gsb occupancy, whereas sites that gained accessibility showed little or no Gsb signal. Thus, the most direct consequence of ectopic Gsb is likely accessibility loss at loci that Gsb can bind, and this loss is accompanied by reduced Hb occupancy. By contrast, accessibility gains occur mainly at loci with little evidence of Gsb binding in independent datasets, suggesting that these gains are more likely indirect consequences of Gsb misexpression.”

      (3) Heat-shock-induced chromatin changes were not fully accounted for

      We agree that, because heat shock is required to induce Gsb, a contribution from the induction regime cannot be completely excluded. However, several observations argue that the chromatin changes are not dominated by a non-specific heat-shock response. First, the accessibility changes were reproducible across biological replicates (Figure 6—figure supplement 2). Second, as described above, sites that lost accessibility were consistently occupied by Gsb in two independent datasets and showed a corresponding reduction in Hb occupancy, whereas sites that gained accessibility showed little or no Gsb occupancy (Figure 6C–H). This structured relationship would not be readily explained by a general heat-shock response.

      As an additional test, we performed a Gene Ontology analysis of genes associated with sites that gained accessibility. The enriched terms were predominantly related to development and cell-fate specification, including neuroblast differentiation and segment specification, while heat-shock and stress-response terms were not enriched (Author response image 1). Although none of these observations alone formally excludes an effect of heat shock, together they argue that the observed pattern reflects structured, Gsb-associated chromatin remodelling rather than a general stress response. We nevertheless interpret the accessibility gains cautiously as likely indirect effects of Gsb misexpression.

      Author response image 1.

      Gene ontology analysis of sites showing gain in accessibility upon Gsb misexpression in NB7-4. Genes overlapping the 606 sites showing at least 2-fold increase in accessibility (DamOnly signal) were annotated using the UCSC Table Browser (dm6). The resulting gene list was analysed for associated gene ontology (GO) terms using Metascape (Zhou et al. 2019). The top 20 enriched GO terms are represented as a bar chart, coloured by p-values.

      (4) Chromatin accessibility following Gsb loss in NB5-6 would provide a more physiological test

      We agree that this would be an informative experiment, and we explored several ways of perturbing Gsb early enough to address its endogenous function. A NB5-6-specific RNAi approach could not be used because the available NB5-6 Gal4 driver becomes active only after the period in which Gsb specifies the lineage.

      The difficulty with conventional gsb mutants is different but equally limiting. Homozygous embryos would have to be identified during the brief developmental window in which Hb is expressed, while each TaDa/CATaDa replicate requires at least 30 mg of precisely staged embryos. The available fluorescent balancer markers are either not detectable at these early stages or become reliably detectable only towards the end of the window. It is therefore not feasible to identify and collect sufficient homozygous embryos — either manually or by fluorescence-assisted whole-embryo sorting — within the required time frame.

      We therefore generated a gsb guide-RNA line and used Vasa-Cas9 to deplete Gsb in the early embryo. This strategy produced a high rate of Gsb editing, embryonic lethality and the expected axonal defects (Figure 7—figure supplement 1). When we examined NB5-6 in these embryos, we found that the Lbe-K reporter and the NB5-6 neuronal markers Ap and Eya were lost, confirming the requirement for Gsb in specifying this lineage (Figure 7).

      Unfortunately, this also meant that we could not take the experiment forward for TaDa/CATaDa. Lbe-K-Gal4 is the driver we use to target NB5-6, and its expression was lost following early Gsb depletion. Without the driver, we can no longer restrict Dam expression to NB5-6 and therefore cannot obtain a lineage-specific chromatin profile. Thus, although the early CRISPR strategy allowed us to examine the developmental consequences of Gsb loss, the same experiment could not be used to assay chromatin accessibility in NB5-6. We have made this limitation explicit in the revised Discussion.

      Relevant edits made to the manuscript: (Result, Figure 7 and Figure 7— figure supplement 1). We also now state explicitly in the “Scope and future directions” section that the current tools did not allow us to profile the chromatin consequences of Gsb loss directly in NB5-6 (Discussion).

      (3) En is not a pioneer factor

      The authors conclude that Engrailed (En) is not a pioneer factor, based on the observation that En binding correlates with accessible chromatin and that En is not enriched at NB5-6-specific SOIs. However, this conclusion is not sufficiently supported by the functional data.

      First, the absence of En binding at NB5-6-specific SOIs does not necessarily indicate an inability to engage closed chromatin. These regions were not selected for the presence of En consensus motifs, so their lack of occupancy may simply reflect the absence of En binding motifs rather than a lack of pioneering capacity. A systematic motif analysis at NB5-6-specific SOIs is needed to determine whether En binding sites are present but unoccupied.

      Second, the claim that En lacks pioneer activity relies solely on a single steady-state TaDa/DamID occupancy assay at one developmental stage. Because pioneer factor interactions can be transient, low-affinity, and stage-specific, such binding may not be detected by TaDa, which also depends on local GATC density and methylation kinetics and may yield false negatives. Given these technical limitations, the absence of En binding at less accessible regions does not definitively rule out a priming role.

      In the absence of direct functional assays (En LOF/GOF), the authors should explicitly acknowledge these technical and conceptual limitations and tone down the claim that "En lacks pioneer activity".

      We thank the reviewer for raising this point. We agree that the statement “En is not a pioneer factor” could be read as a general conclusion about En activity across developmental contexts. Our conclusion is more specific: in NB7-4 during the Hb-competence window, En occupancy is strongly biased towards pre-accessible chromatin and does not display the chromatin-engagement pattern expected of a pioneer factor. We have revised the manuscript throughout to make this context-specific interpretation clear. Below, we also address each of the reviewer’s points.

      (1) The absence of En at NB5-6-specific SoIs could reflect an absence of En-binding motifs

      We agree that the absence of En occupancy at NB5-6 SoIs would not be informative if these loci lacked En-binding motifs. We therefore performed the suggested motif analysis. En motifs were present at comparable frequencies in NB5-6- and NB7-4-specific SoIs (88.0% and 86.5%, respectively), with both enriched relative to matched shuffled controls (new Figure 3—figure supplement 1L). Thus, NB5-6 SoIs are motif-compatible but remain unoccupied by En in NB7-4. Their lack of En occupancy cannot therefore be explained simply by motif absence and instead points to additional determinants such as chromatin accessibility or cofactor context.

      Relevant edits made to the manuscript: Result, Figure 3B–C and new Figure 3—figure supplement 1L)

      “As expected, En was enriched at NB7-4-specific SoIs, where Hb uniquely binds in this lineage. However, there was no detectable En signal in NB7-4 at sites known to be NB5-6-specific SoIs, which remain relatively less accessible and Hb-free in NB7-4. This difference is unlikely to be explained simply by En motif availability, since En motifs are similarly represented at NB7-4- and NB5-6-specific SoIs. Thus, at SoIs, En occupancy is associated with the cognate, accessible NB7-4 SoIs, with little detectable occupancy at the non-cognate, relatively less-accessible NB5-6 SoIs.”

      (2) TaDa may fail to detect transient, low-affinity or stage-specific En binding

      We agree that no occupancy assay can exclude interactions below its detection threshold. However, TaDa is cumulative rather than a steady-state snapshot: Dam methylation accumulates during the expression window, allowing transient interactions to leave a detectable signal. Genome-wide, En occupancy was strongly weighted towards accessible chromatin, and accessibility predicted En binding with an AUROC of 0.74 (Figure 3E–I, Figure 3—figure supplement 2 and new Figure 3— figure supplement 3E).

      Gsb provides an internal comparison using the same experimental framework. Gsb binding was detected at both accessible and relatively less-accessible chromatin, and accessibility did not predict Gsb occupancy better than chance (AUROC = 0.41; Figure 4E–I and new Figure 3—figure supplement 3E). This argues that the En pattern is not caused by a general inability of TaDa to detect binding at less-accessible loci. We nevertheless acknowledge that rare interactions, interactions below the detection threshold or binding outside the assayed window cannot be excluded. The resolution and cumulative nature of TaDa are now also described explicitly in the revised manuscript.

      Relevant edits made to the manuscript: Result section for the genome-wide analysis and Discussion section for the TaDa limitations; Figure 3E–I, Figure 4E–I, Figure 3—figure supplement 2 and new Figure 3—figure supplement 3E).

      (3) Direct functional assays of En were not performed

      We agree that determining whether En actively establishes or maintains chromatin accessibility would require En loss- or gain-of-function experiments combined with chromatin profiling. These experiments were not performed in this study, and we have therefore removed the categorical statement that “En is not a pioneer factor.”

      The revised manuscript now states the more specific conclusion supported by our data: En occupancy in NB7-4 during the Hb-competence window is strongly biased towards pre-accessible chromatin. We also acknowledge that the current experiments cannot exclude rare or transient interactions below the detection threshold, or chromatin-remodelling activity by En at other loci, developmental stages or cellular contexts. The factors that establish the NB7-4 accessibility landscape therefore remain unresolved.

      Relevant edits made to the manuscript: (Result; Figure 3)

      “Taken together, these results show that En occupancy is strongly biased toward preaccessible chromatin in NB7-4, including at NB7-4-specific SoIs. Thus, En is well placed to integrate spatial and temporal information through direct regulation at preaccessible enhancers. However, because NB7-4 has a distinct accessibility landscape, the factors that establish this landscape remain unresolved. We therefore propose that NB7-4 may use a combinatorial STF-code logic, in which other lineage-specific factors help establish NB7-4-specific SoIs, while En occupies this pre-accessible landscape and likely collaborates with Hb to activate lineage-specific enhancers.”

      (4) Clarity of STF-code Model and Central Message

      The manuscript begins by presenting two models, direct and epigenetic, but the central takeaway of the paper is not clear. Specifically, the nuanced roles of the spatial factors Gsb and En as chromatin-priming versus stabilizing/effector factors within an STF code, and the resulting division of labor, are not clearly illustrated. The distinction between Gsb as a chromatin-priming factor and En as a cofactor-dependent activator/stabilizer should be explicitly presented in a stepwise model for better clarity. The authors could strengthen this by providing a schematic with two sequential stages illustrating how neuroblast identity factors (STF code) change chromatin states to drive lineage-specific enhancer activation. The schematic can be shown from the neuroectoderm to individual NB lineages to make it more panoramic.

      We thank the reviewer for this suggestion. This comment, together with related points raised below, made us realise that the manuscript did not bring out strongly enough that our data lead us to propose a third model: the distributed STF-code model. Rather than treating direct and epigenetic regulation as mutually exclusive alternatives, this model distributes these activities across different members of a NB-specific STF code. We have now revised the manuscript to reflect this transition. For example, we now state this explicitly in the Abstract, at the end of the Introduction and at the beginning of the Discussion.

      Relevant edits made to the manuscript: Abstract, Introduction, Discussion, and have added a new summary schematic (new Figure 9).

      (5) Identification of Priming Factors in NB7-4

      While the authors suggest that an unknown priming factor might be responsible for establishing sites of integration in NB7-4, they do not identify or explore potential candidates for this role. Further investigation into what factors might be involved in chromatin priming in NB7-4 could provide a more complete understanding of the mechanisms at play.

      We thank the reviewer for this suggestion. We agree that identifying the factors that establish the NB7-4 accessibility landscape is an important next step. Our current data do not identify such a factor, and doing so would require systematic perturbation of candidate STF-code members together with lineage-specific chromatin profiling.

      We have nevertheless made this question more concrete in the revised Discussion. We identify Msh as a candidate shared input in NB5-6 and NB7-4, highlight additional candidates suggested by motif enrichment at NB7-4 SoIs, and propose NB6-4 — which coexpresses Gsb and En — as a useful context in which to test the division of labour between STF-code members. We present these as testable candidates rather than established priming factors.

      (6) Functional Validation of STF Code Components

      The study proposes an STF code for each neuroblast lineage, but the specific components of these codes, beyond Gsb and En, are not fully explored. Identifying and validating additional factors that contribute to the STF code in each lineage could strengthen the conclusions.

      We thank the reviewer for this point. We agree that the complete composition of the NB5-6 and NB7-4 STF codes remains to be established, and we now make this explicit. The present study proposes a mechanistic framework based on the different chromatin-engagement properties of Gsb and En, rather than claiming to have defined or validated every component of either code.

      As noted in our response above, the revised Discussion identifies Msh, Iroquois-complex members and TF families enriched at NB7-4 SoIs as candidate additional components. Testing these factors individually and in combination, with chromatin, Hb-occupancy and lineage-identity readouts, will be required to define the minimal functional code for each lineage. We present this as an important direction for future work (lines 759–770).

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      (1) The reviewers appreciate the content shown in Figure 1, which is helpful for people who are unfamiliar with the system as a whole. One key issue is that later in the manuscript, the authors look at Gsb and describe it as a factor that works to close chromatin, making the model depicted in panel E misleading when reading the first half of the manuscript and leading to confusion/whiplash when getting to Figure 6, where a spatial transcription factor is thought to play a role in closing chromatin.

      Thank you for pointing this out. Figure 1 was intended to present the two models currently proposed in the field and as the starting hypotheses for the study. It was not intended to present the conclusions from our study. We realise, however that this distinction was not clear and since we did not present the updated model, it made the later finding appear contradictory.

      We have now made substantial edits to the text and have made the transition from the original models to our revised interpretation explicit in the Introduction and Discussion. We have also added a new summary model (new Figure 9), which shows that chromatin opening, chromatin closing and STF–Hb engagement can be distributed across different members of an NB-specific STF code.

      (2) It is unclear what "less accessible" actually means. The reviewers would like to see quantitative standardization to define the degree of chromatin accessibility when using the Dam expression alone.

      We thank the reviewer for this point. The comment made us revisit how we defined accessibility, which we had previously treated too much as a binary distinction between accessible and inaccessible chromatin. We have now revised our analyses to represent chromatin accessibility as a continuum of states.

      We defined a common set of 27,119 DamOnly-marked regions across both NBs, ranked them by mean DamOnly signal and divided them into deciles from least to most accessible. The construction and validation of this continuum are shown in new Figure 2G and new Figure 2—figure supplement 2A–D. We also use this framework to examine STF occupancy and Gsb-dependent chromatin remodelling across the accessibility spectrum (new Figure 3— figure supplement 2A and new Figure 6—figure supplement 2E–F).

      Where a discrete lineage-specific comparison was required, we applied a minimum two-fold difference in DamOnly signal between the NBs. This identified 845 NB5-6-preferential and 1,067 NB7-4-preferential regions. A region preferentially accessible in one NB is therefore described as relatively less accessible in the other, rather than as completely inaccessible.

      Relevant edits made to the manuscript: Results, new Figure 2G and new Figure 2—figure supplement 2A–D.

      (3) A key takeaway in Figure 3 is that En is binding already accessible chromatin. Another key point that this manuscript makes is that spatial-temporal factors (and codes) are responsible for this opening. We have not yet been shown that chromatin accessibility of this neuroblast identity actually changes upon spatial-temporal factor expression. I suggest including data of the dam-only control as a time course. Showing chromatin accessibility just before temporal factor expression and then after to validate that pioneer factor activity appears to be likely.

      We appreciate this suggestion and agree that, conceptually, the model implies a temporal sequence in which spatial factors first act during neuroectoderm patterning and temporal factors such as Hb subsequently engage the chromatin after neuroblast formation. In practice, however, these events occur in very rapid succession during development. Spatial transcription factors are expressed in the neuroectoderm, neuroblasts are specified and delaminate, and Hb expression begins almost immediately after neuroblast formation — all within a short developmental window on the order of minutes to tens of minutes.

      This makes it difficult to directly test chromatin accessibility changes across these stages using lineage-restricted Dam-based approaches. Before delamination there is no neuroblast to target with the available drivers, and once the neuroblast forms the temporal program is already underway. As a result, the sequential changes in accessibility that the reviewer is suggesting cannot currently be resolved with the available tools.

      We agree that directly visualizing how chromatin accessibility changes during this brief developmental transition would be very interesting, but doing so would likely require approaches with much higher temporal resolution, such as live imaging-based methods for monitoring chromatin accessibility.

      (4) Similar to the comment for Figure 3, showing chromatin accessibility changes in the NB subtype via a time course that includes both before and after spatial transcription factor expression begins.

      This point is closely related to the reviewer’s previous comment regarding a temporal analysis of chromatin accessibility. Please refer to our response above describing the developmental timing and technical limitations that make such an experiment difficult in this system.

      (5) It is difficult to reconcile the conclusion in Figure 5 that regions bound by both En/Hb or Gsb/Hb are considered the highest accessibility. Can the authors touch on the logic for this, given that in the next figure, they are going to suggest that Gsb works as a factor that is primarily responsible for closing chromatin? It is unclear how Gsb is closing chromatin, but it is also binding Hb, and in those regions, chromatin is most accessible.

      We thank the reviewer for raising this point. The findings in Figures 5 and 6 may initially appear difficult to reconcile, but we think that they both actually point to the same conclusion: that Gsb’s effect on chromatin is context-dependent.

      An important point is that Gsb binding is not restricted to a single chromatin state. In its endogenous NB5-6 context, it occupies both accessible and relatively less-accessible regions (Figure 4B–C, E–F). Its presence at accessible chromatin does not establish that Gsb opened that chromatin nor that it closed it because these occupancy data do not reveal the direction of chromatin change. From these data we can only conclude that sites co-bound by Gsb and Hb are more accessible than sites bound by Gsb alone, suggesting that the outcome of Gsb binding depends on the surrounding regulatory context. In the presence of Hb — and likely other members of the NB5-6 STF code — Gsb can participate in a highly accessible, productive regulatory state (Figure 5C–E).

      The misexpression experiment helps us interpret these relationships in the endogenous context. When Gsb is introduced into NB7-4, sites that lose accessibility are strongly Gsb-bound in two independent datasets, and this loss is accompanied by reduced Hb occupancy (Figure 6C–H). Some Gsb-bound sites also gain accessibility, consistent with bidirectional remodelling, but Gsb occupancy is negligible at these gain sites. Thus, outside its normal NB5-6 regulatory environment, the more direct effect of Gsb binding is likely chromatin closing.

      This provides a possible explanation for the endogenous (NB5-6) data in Figure 5. The lower accessibility of sites bound by Gsb alone may reflect this closure-biased activity, whereas the highly accessible state at Gsb–Hb co-bound sites is likely to arise from the broader NB5-6 regulatory context. We do not conclude that every Gsb-only site is actively closed, or that Gsb itself opens the co-bound sites. Rather, our data suggest that Gsb can participate in different chromatin states, with the outcome of its binding shaped by Hb and other members of the STF code.

      We have revised the Results and Discussion to make this interpretation clearer.

      (6) The most striking piece of data from Figure 6 is that it appears the physiological role of Gsb is to reduce chromatin accessibility and that opening chromatin is an indirect effect. I am not sure that the field widely recognizes closing as chromatin as "pioneer-like" activity. Moreover, this finding seemed very out of place given the way the story has been sold thus far - discussing "priming of chromatin" and referring to this as opening in figure 1 and discussion of binding of these factors at open and less accessible.

      Thank you for raising this issue, which overlaps with the reviewer’s previous point. We were equally struck by the result from Figure 6: the sites that lose accessibility are more consistent with a direct effect of Gsb, whereas the sites that gain accessibility are more likely to represent indirect effects. This suggests that Gsb can remodel chromatin bidirectionally.

      We agree that the field does not generally describe chromatin closing as pioneer activity. We therefore no longer refer to Gsb as a pioneer factor. Instead, we describe Gsb as having bidirectional chromatin-remodelling capacity and refer to it as “chromatin priming” activity.

      Finally, we agree that the original presentation made this progression difficult to follow. Figure 1 presents the two existing models as the starting point, whereas our data lead us to propose a third, distributed STF-code model. We now make this transition explicit throughout the revised manuscript and have added a new summary schematic (new Figure 9; See Results and Discussion).

      Reviewer #2 (Recommendations for the authors):

      Minor comment:

      (1) Have the authors validated the specificity of the Lbe-GAL4 and 19B03AD;18F07DBD drivers? It is important to clarify whether these drivers label only NB5-6 and NB7-4 neuroblasts or also their progeny. Since the interpretation of chromatin dynamics is in the context of neuroblasts, reads from differentiated neurons could affect the conclusions.

      We thank the reviewer for raising this point. These driver lines were extensively characterised in our previous study and are highly specific to the NB5-6 and NB7-4 lineages, respectively. Importantly, as the reviewer points out, they are not neuroblast-exclusive and also label progeny. Because our profiling is restricted to the early Hb competence window, this contribution should be limited to a small number of GMCs and the earliest-born neurons.

      On rereading the manuscript, we realised that there were several instances where we used “NB-specific” too loosely when referring to these datasets. We have therefore revised the manuscript throughout to make clear that the TaDa/CATaDa profiles represent the NB5-6 and NB7-4 lineages during the Hb window and are not exclusively derived from the neuroblast itself. We have also added this explicitly as a limitation in the Scope and Future Directions section. Importantly, this does not change the essence of our conclusions, which are based on comparisons between these two defined lineages and on perturbations examined within the same lineage-restricted framework.

      Relevant edits made to the manuscript:

      - “The driver lines were previously validated as being specific to these lineages”.

      - “First, the lineage-specific Gal4 drivers also label the immediate progeny of each NB; thus, although profiling was restricted to the early Hb competence window, when only a small number of GMCs and early-born neurons are present, the resulting profiles are not exclusively derived from the NB itself.”

      (2) The lineage NB6-4 co-expresses both Gsb and En and represents an informative intermediate case. This context supports a cooperative STF-code model in which Gsb provides chromatin priming while En acts as an effector or stabilizer, without requiring autonomous pioneer activity. The authors should briefly discuss how NB6-4 fits into their model and whether Gsb priming in this lineage enables En-Hb co-occupancy and enhancer activation.

      We thank the reviewer for this comment. We agree that NB6-4 is an especially interesting case in the context of our model, because it co-expresses both Gsb and En and therefore may provide a lineage in which both aspects of the proposed two-step mechanism can be examined together: Gsb could contribute to chromatin priming and En could function at already primed enhancers together with Hb. We now include this explicit example in the Discussion section.

      (3) The authors' data support a role for Gsb in lineage-specific chromatin priming, but the functional experiments reveal important limitations. Gsb alone does not efficiently open closed chromatin, install NB5-6-specific SOIs, or recruit Hb, and ectopic Gsb often antagonizes native chromatin states. Thus, the results do not support Gsb as a classical standalone pioneer factor, as implied in the discussion. The authors should replace the term "pioneer-like potential or activity" with "context-dependent pioneer activity" in the results, as they have rightly mentioned in the discussion.

      We agree with the reviewer. As discussed in our responses to the related comments above, our data do not support describing Gsb as a classical pioneer factor. Gsb remodels chromatin bidirectionally, with both gains and losses of accessibility, whereas pioneer activity is traditionally associated with chromatin opening. We have therefore gone further than the reviewer’s suggested change: throughout the manuscript, we have replaced “pioneer-like potential/activity” and “context-dependent pioneer activity” with “context-dependent chromatin remodelling” or “chromatin priming.” The Results and Discussion now make it clear that Gsb’s activity depends on the surrounding STF and cofactor context rather than representing autonomous pioneer activity.

      (4) The use of ectopic expression systems may introduce artifacts or off-target effects that could affect the interpretation of the results. These potential limitations are not extensively discussed.

      We agree that ectopic expression can produce indirect or non-physiological effects. The Gsb misexpression experiment was designed to test whether Gsb is sufficient to remodel chromatin in the heterologous NB7-4 context, rather than to reproduce its endogenous function in NB5-6. We therefore do not interpret every change in accessibility in the misexpression experiment as a direct or physiological role for Gsb in NB5-6. However, the changes are not random. Sites that lose accessibility are strongly associated with Gsb occupancy in two independent datasets and they also lose Hb occupancy, whereas sites that gain accessibility show little Gsb occupancy and are therefore more likely to reflect indirect effects (Figure 6C–H). The changes were reproducible between replicates, and genes associated with accessibility gains were not enriched for heat-shock or stress-response terms (Author response image 1). These analyses do not remove the limitations of ectopic expression, but they help distinguish the more likely direct effects from indirect ones. We now make both the purpose and the limitations of this experiment explicit in the Results and Discussion.

      (5) The moderate correlation (0.7-0.82) between Dam-En and Dam-only reflects the expected overlap of En binding with accessible chromatin, but it also underscores a limitation: TFs that prefer open regions may show high baseline similarity to Dam-only, potentially masking low-affinity or transient interactions. The authors should acknowledge this when concluding that En lacks pioneer activity.

      We thank the reviewer for bringing this up. We want to clarify that our conclusion that En preferentially occupies accessible chromatin is not based only on the moderate genome-wide correlation between Dam: En and DamOnly. We also examined En binding at defined SoIs and at differentially accessible loci across the genome. In both analyses, En is strongly enriched at accessible NB7-4 sites but shows little detectable enrichment at the corresponding less-accessible sites (Figure 3B–F). We have now extended this analysis across 27,119 regions ranked along the full accessibility spectrum. Here too, En signal remains low across the less-accessible bins and increases principally in the most accessible bins (new Figure 3— figure supplement 2E).

      A useful comparison here is Gsb. Using the same experimental and analytical framework, we readily detect Gsb binding at both accessible and relatively less-accessible chromatin in NB56 (Figure 4B–F; new Figure 3—figure supplement 2E). Thus, the method is able to detect binding at less-accessible chromatin when it occurs. Consistent with this, accessibility predicts En occupancy but not Gsb occupancy in the corresponding ROC analysis (new Figure 3—figure supplement 3E). We also refer the reviewer to our response to the related comment above, where we discuss this comparison in more detail.

      Finally, we want to point out that TaDa is not a snapshot assay. Dam-mediated methylation accumulates over the expression window and across many cells, so repeated weak or transient interactions should, in principle, contribute to the signal. We agree, however, that very rare interactions below the detection threshold cannot be excluded. We have therefore tempered our conclusion throughout the manuscript: rather than stating that En lacks pioneer activity, we now conclude that En occupancy during the NB7-4 Hb window is strongly biased towards pre-accessible chromatin.

      (6) The schematic illustrating the NB 5-6 and NB 7-4 SOIs (Figures 3A, 4A, and S2A) should be made clearer. When Hb is bound, sites that are accessible serve as SOIs for a specific lineage, whereas Hb-unbound, inaccessible sites do not. The authors can visually represent this by showing that, in the case of Hb binding, the accessible region functions as a resident SOI for the NB7-4 lineage, while the same region in NB5-6, being Hb-free, is inaccessible. This distinction could be indicated with a shaded or shadowed area from top to bottom in Figures 3A and 4A.

      We thank the reviewer for pointing this out. We have revised these panels to make the visual distinction between lineage-specific SoIs and the corresponding Hb-free, less-accessible loci in the other lineage more explicit.

      (7) At 472, change "Fig.S6C-F" to "Fig.S6C-D".

      Thank you for spotting that!

    1. Author response:

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      In this manuscript the authors study the distribution of the KMT2A methyltransferase across the human ribosomal gene loci (rDNA) and the effects of its depletion on rDNA chromatin modification using a KMT2A conditional cell line. They used ChIP mapping data and claim to show that KMT2A depletion does not affect H3K4me3 levels but does reduce acetylation of H3K9 and reduces PCAF (KAT2B) binding. They further claim that KMT2A depletion causes stalling of RNA Polymerase I at the upstream "Spacer" promoter duplication on the rDNA.

      Weaknesses:

      I found the manuscript very confusing. In particular, I found it short on short on experimental detail and I found the data in general to be unconvincing. It is my opinion that the authors overinterpret their data, leading to unrealistic and unsupported claims. The manuscript also avoided discussing relevant recent studies on the regulation of the rDNA and of rDNA chromatin, most citations being to data 15 to 20 or more years old. This is most apparent when discussing the factors such as UBTF and SL1 that determine preinitiation complex assembly and the status of active versus inactive rDNA chromatin. Both have seen significant advances in recent years, and these should be thoroughly discussed.

      Specific comments:

      The authors do not describe the generation of the KMT2A conditional HEK293T cells or their treatment. Since these cells form the basis for subsequent experiments, they must be explained fully. I found that the conditional cell line had already been used in a previous unrelated publication "Chinchole et al. 2022". This manuscript explained that the KMT2A knockout is induced via Dox-controlled Cas9 in a HEK cell clone constitutively expressing guide RNAs to KMT2A. The KMT2A knockout requires a 7-day treatment with Dox, leaving wide open the question of direct versus indirect effects of KMT2A loss, and perhaps explaining some of the discrepancies with published data.

      We thank the Reviewer for their comment. As the Reviewer correctly states, these KMT2A knockouts have been used in previous studies: Chinchole et al., 2022; PMID: 36111497 and Malik et al., 2023; PMID: 37379335. In both cases, the generation of KMT2A inducible knockout was described in detail in the Methods section; hence, in this manuscript we referred to these publications. However, if the Reviewer feels that details should still be provided, we will do so again here.

      As the Reviewer is aware, KMT2A is an essential chromatin-bound protein, which is quite stable in its heterodimer form. As we described in our publication, Malik et al., 2023, the inducible knockout clones were obtained after extensive screening and thoroughly characterized. While the protein diminishes in the WB after 3 days, we thought it necessary to confirm that it does not persist on the chromatin in ChIP assays.

      We are pasting the excerpt from the manuscript describing the relevant section below.

      “Our initial attempts to generate MLL knock-outs in several different cell lines were not successful. Therefore, keeping in mind that MLL is essential for cell viability and growth [26,27], we generated and successfully obtained knock-outs in HEK-293 cell lines using doxycycline-inducible Cas9 expression vectors ([52]; Fig 3A). MLL levels were drastically reduced in the 2 independent MLL-knock-out clones shown here (MLL iKO#11 and iKO#20) and both KOs showed cell cycle profile similar to Control cells (S3A Fig). In the case of chromatin-binding proteins, often cellular levels show reduction but not the chromatin-bound fraction. We, therefore, confirmed that MLL chromatin binding was indeed reduced in our inducible knock-out cell lines by ChIP assays (Figs 3B and S3B), both on centromere and HOXA9 promoter”.

      Inducible Cas9-mediated knockout provides an opportunity to generate irreversible knockouts, allowing sufficient time to deplete stable proteins and reveal delayed phenotypes or compensatory responses [PMID: 29036671]. However, this advantage has to be balanced with the potential secondary effects arising from prolonged depletion. Indeed, inducible Cas9 knockouts have been generated after similar induction periods by other laboratories to deplete chromatin-bound proteins [PMID: 28216383; PMID: 37702151], especially for members of the KMT2 family [PMID: 40846851, PMID: 27535106; PMID: 37535603 ]. Further, we have not observed any discrepancy with published data for KMT2A.

      In mapping the interactions of KMT2A across the rDNA by ChIP they use 18 PCR amplicons, some of which the authors inaccurately state as targeting specific rDNA elements. For example, they state Primers (that is, Amplicons) #1-3 target the spacer and core 47S promoters. In fact, amplicon #2 overlaps neither of these promoters and lies centrally within the 1kbp of enhancer repeats between them. Exactly why emphasis is put on KMT2A chipping at these two promoters is anyhow questionable since KMT2A levels (Figure 1) appear equally high at multiple IGS amplicons.

      As the enhancer repeats (ER) are clearly shown in the schematic of Fig. 1A and SF1B, and the same is stated in the legend of SF1B, rather than an inaccuracy, it is a matter of oversight. We thank the Reviewer for noticing this and bringing it to our attention. We will correct it in the text.

      We thank the Reviewer for raising this point regarding our focus on the promoters in the present study and the binding of KMT2A to the IGS region. KMT2A’s role in regulating RNA polymerase II transcription by regulating gene promoters is well established. However, its role in regulating RNA polymerase I transcription at the rDNA promoter has not been characterized. In this study, we provide evidence for a previously unrecognized role of KMT2A in regulating rDNA transcription and hence extend its function to regulation of RNA polymerase I.

      We agree that our ChIP data show KMT2A occupancy at multiple regions within the IGS, in addition to the promoter regions. For this reason, we felt it was important to present these data and perform ChIP-seq analyses of the rDNA locus to reveal the complete picture.

      Our emphasis on the promoter regions is aimed at understanding the potential role of KMT2A in regulating RNA polymerase I transcription initiation. However, we recognize that the enrichment of KMT2A at multiple IGS regions raises the possibility that it may have additional functions beyond promoter regulation. We are currently investigating the role of KMT2A at the IGS, and in our future studies we hope to address the functional significance of this occupancy in greater detail.

      Discrepancies with published data are particularly apparent in their mapping of H3K4me2, H3K4me3 and H3K9ac, all directly relevant to their conclusions. These modifications have been shown in several publications to map to a single major site a few hundred bp upstream of the spacer promoter in multiple human and mouse cell types. Since the authors fail to monitor H3K4 methylation and H3K9 acetylation at this dominant site they also fail to provide significant evidence that KMT2A in fact affects H3 methylation or H3 acetylation on the rDNA.

      We thank the reviewer for raising this important point about the distribution of histone modifications at the rDNA locus and how they depend on KMT2A. Previous studies have established that active histone modifications are enriched at specific regions of rDNA. In particular, landmark studies from two groups have pioneered the use of genome assemblies to map these histone modifications. The Scacheri group [Zentner et al. 2011, PMID: 21355038] reported enrichment of H3K4me2, H3K4me3, and H3K9ac at the human rDNA promoter, along with additional active-chromatin-associated enrichment within the intergenic spacer. Subsequently, the same group demonstrated that the distribution of histone modifications in mouse embryonic stem cells differs from that in human embryonic stem cells and other differentiated mouse cell types [Zentner et al. 2014, PMID: 24347625]. These findings underscore the importance of examining the relevant regulatory regions in the appropriate biological system.

      Similarly, studies from the Moss group radically redefine our understanding of how histone modifications are distributed across rDNA in mammals. They demonstrated that active histone modifications (including H3K4me2/3, H3K9ac, H3K27ac, and H3K36me3) are not present at the core 47S promoter or along the transcribed gene body of active rDNA repeats, but are instead strictly sequestered to a highly localized "Enhancer Boundary Complex" located a few hundred base pairs upstream of the spacer promoter. Consequently, this precise upstream hub represents the sole site of active histone modifications on active rDNA genes [Herdman et al., 2017, PMID: 28715449 ; Mars et al., 2018, PMID: 29158335]. These findings challenge the classical models of histone modification distribution at rDNA.

      However, an extensive body of classical literature presents a complementary view where active histone modifications directly decorate the core 47S promoter and proximal transcribed regions to dynamically coordinate RNA Polymerase I transcription. Work from the Grummt and Santoro laboratories established that unmethylated, active rDNA repeats possess prominent H3K4me3 and hyperacetylated histones directly at the core 47S promoter, serving as a functional "poised" platform for pre-initiation complex (PIC) assembly [Santoro and Grummt, 2002, PMID: 12368916; Santoro and Grummt, 2005, PMID: 15767661; Mayer et al., 2006, PMID: 16678107; Schmitz et al., 2010, PMID: 20952535]. Furthermore, tracking chromatin remodelling complexes—such as the CSB-PCAF complex investigated by the different groups—has shown that active depletion of histone acetyltransferases leads to a direct loss of H3K9ac specifically at the primary 47S initiation site, causing a failure in Pol I loading [Shen et al., 2013, PMID: 23667505; Vintermist et al., 2011, PMID: 21559432]. Besides these reports, a wealth of independent functional data highlights that key chromatin regulators dynamically target and modulate the core 47S promoter region to dictate ribosomal transcription initiation. Some examples are referred to here [Xei et al., 2012, PMID: 22570494; Wang et al., 2011, PMID: 21960006; Zhu et al., 2010, PMID: 20531378; Frescas et al., 2007, PMID: 17994099].

      Our investigation of KMT2A directly builds upon this functional promoter-centric model. While we appreciate that mapping variations exist between custom rDNA reference models in the literature, our data show clear and reproducible levels of H3 methylation and acetylation dynamics across the primary regulatory sites (including the 47S promoter and adjacent transcribed unit) upon KMT2A depletion. These changes correlate directly with functional changes in 47S pre-rRNA output, supporting a model where KMT2A-mediated histone modifications operate directly at the core transcription initiation machinery to regulate overall nucleolar output.

      We acknowledge that the distribution of histone modifications across the rDNA repeat and their functional dependence on KMT2A represent distinct questions. Accordingly, we interpret the ChIP-seq profiles in conjunction with our site-specific ChIP-qPCR and functional experiments rather than relying exclusively on the genome-wide mapping data. We therefore conclude that our results support a role for KMT2A in regulating the acetylation-associated chromatin environment and transcriptional activity of the rDNA promoter, without claiming that KMT2A depletion reduces all active histone modifications across the locus.

      We will clarify the relevant analysis and the scope of our conclusions in the revised manuscript.

      The KMT2A deletion drastically reduces PolI and UBF (UBTF) engagement across the rDNA, and consistent with this, SL1 and RRN3 engagement is reduced as are 47S levels. Thus, whatever the 7-day KMT2A deletion is doing to the cells it is certainly inducing a very significant shut-down of active rDNA. How such an extreme experimental model can tell anything of KMT2A functions is unclear.

      We feel that this concern is on similar lines as that stated in comment 1. We have already explained our inducible knockout model above. The cell-cycle profile of KMT2A-inducible knockout (iKO) cells reported in Malik et al. (2023), PMID: 37379335. provides relevant context for interpreting these effects.

      We further wish to highlight that contrary to expectation, the H3K4me2/3 levels are largely unaffected on the rDNA in KMT2A iKO cells, which is surprising but not unexpected given the role of KMT2A in selectively trimethylating specific gene loci (PMID: 19703992). However, the loss of acetylation on H3 is very specific to the study at hand.

      Unchanged H3K4me2/3 levels, along with selectively decreased acetylation, have not been reported for a general shutdown of active rDNA under extreme conditions like serum starvation etc. In case of a non-specific effect, both active methylation and acetylation marks are expected to go down. The presence of the H3K4me2/3 mark in our iKO cells acts as an internal control, confirming that the loss of H3 acetylation is a direct consequence of KMT2A depletion.

      Furthermore, in the current manuscript, the effects of KMT2A deletion on the Pol I transcriptional machinery can be rescued by the KMT2A catalytic point mutant carrying the N3906A mutation but not by the mutant with TAD deletion. This rescue provides important evidence that the phenotype is linked to a specific function of KMT2A rather than being a nonspecific consequence of KMT2A deletion.

      Our findings, considered alongside Lone et al. (2026) PMID: 42096476, support distinct roles for KMT2A and KMT2F in regulating rDNA transcription. In particular, the effects of KMT2A loss occur without a substantial reduction in rDNA H3K4me3, distinguishing its role from the H3K4me3-dependent function of KMT2F in promoting Pol I pre-initiation complex formation.

      In the last results section, the authors further claim "Loss of KMT2A results in a stalled RNA Pol I complex at the spacer promoter" (Figure 4 and S4). To support this the authors try to map spacer promoter transcripts but mistakenly claim that the amplicon #1 can detect these transcripts. In fact, this amplicon overlaps the Spacer Promoter initiation site and so could not detect transcripts coming from this promoter. Published data, not cited, have demonstrated that PolI stalling at the spacer promoter occurs as a normal phenomenon on the active rDNA. Its loss is associated with suppression, not the opposite as inferred in this manuscript.

      We thank the Reviewer for raising this point. We have double-checked that amplicon #1 is downstream of the spacer promoter start site. However, since the reviewer has raised this point, we will look into it in greater detail and remap our amplicons. We will also revisit the previous literature and compare our results with the published findings.

      Reviewer #2 (Public review):

      Summary:

      This important manuscript presents solid evidence that the major contribution of KMT2A to ribosomal gene transcription is through promoting histone acetylation rather than H3K4 methylation. It is suggested this occurs in part through interactions of KMT2A with PCAF.

      Strengths:

      This manuscript advances an important concept that chromatin-modifying enzymes can also function to promote transcription through interactions with other transcriptional regulators independently of their catalytic functions. The data are overall supportive of this conclusion for KDM2A.

      Weaknesses:

      (1) Care needs to be taken regarding interpreting the lack of effect of depleting KMTs or HATs on histone acetylation or methylation levels. There are several overlapping HATS or KMTs that generate these modifications. The most that can be said from these negative results is that the depleted HAT or KMT is not the sole enzyme generating these modifications at these loci.

      We thank the Reviewer for this important comment. We agree that histone modifications are regulated by multiple enzymes with overlapping or partially redundant activities, and that the absence of a detectable change following depletion of an individual KMT or KAT does not exclude a contribution from that enzyme to the regulation of the modification.

      Specifically, the lack of a detectable reduction in H3K4me3 following KMT2A depletion indicates that KMT2A depletion alone is insufficient to produce a detectable decrease in H3K4me3 under the conditions examined. The persistence of this mark may reflect the activity of other KMTs and hence functional redundancy. In contrast, our observation that KMT2A depletion reduces H3K9 acetylation, together with our findings implicating PCAF in KMT2A-dependent rDNA transcription, supports a role for KMT2A in regulating an acetylation-associated mechanism at this locus.

      Nevertheless, we acknowledge that these findings do not, by themselves, establish that PCAF is the sole enzyme responsible for H3K9 acetylation or that it accounts for all KMT2A-dependent effects on rDNA transcription. We will revise the interpretation of our results to avoid attributing the maintenance or loss of a histone modification exclusively to a single enzyme.

      (2) The biochemistry supporting an interaction between KDM2A and PCAF is under-developed and not strong enough to support this conclusion at this point.

      We thank the reviewer for their comment. Based on these comments and those from Reviewer 3, we plan to add more experiments to strengthen the KMT2A-PCAF interaction, including a reverse pull-down.

      (3) It is concluded that acetylation causes increased rDNA transcription. However, acetylation may be a consequence of transcription instead, especially over transcribed regions.

      We thank the reviewer for raising this important point regarding the relationship between histone acetylation and rDNA transcription. We agree that increased histone acetylation over transcriptionally active regions may either contribute to transcriptional activation or result from ongoing transcription. These possibilities are not mutually exclusive.

      Our study provides several lines of evidence supporting a functional relationship between KMT2A and PCAF-associated histone acetylation, which indicate that acetylation is the cause and not a consequence of rDNA transcription. KMT2A depletion reduces rDNA transcription and is accompanied by a reduction in H3K9 acetylation. In addition, we present a model in which KMT2A facilitates the transfer of RNA Pol I PIC from the spacer promoter to the 47S promoter following its assembly at the spacer promoter by recruiting PCAF to rDNA through its TA domain. Together, these observations support that acetylation supports efficient rDNA transcription

      Nevertheless, we acknowledge that these findings do not completely exclude the possibility that some of the observed reduction in histone acetylation occurs downstream of reduced transcription and will modify the discussion accordingly.

      (4) Some conclusions, for example implicating PCAF, are based on overexpression experiments that are very artificial and difficult to draw conclusions from.

      We thank the reviewer for their comment. We agree that overexpression experiments can produce non-physiological protein levels and potentially influence experimental readouts. However, our interpretation of PCAF involvement is based on a broader set of observations presented in this study, including the effects of KMT2A depletion on rDNA transcription and histone acetylation, together with our experiments examining the contribution of individual histone acetyltransferases to rRNA synthesis. These findings identify PCAF as a key co-activator of KMT2A-dependent transcriptional activation.

      Therefore, the overexpression experiments have been used to provide mechanistic support rather than definitive evidence that endogenous PCAF is the sole or essential mediator of this process.

      (5) Several figures are generated using publicly available data sets that were reanalyze using updated reference genomes, sometimes from different cell lines/types. This seems to be a useful exercise but the methods should include information regarding the robustness of these data sets.

      We thank the Reviewer for their concern; we will update this information in the Methods.

      Reviewer #3 (Public review):

      Summary:

      This manuscript examines a key mechanism by which KMT2A regulates RNA polymerase I transcription at ribosomal DNA. The authors suggest that KMT2A facilitates the recruitment of PCAF to rDNA. This process enhances histone acetylation and supports assembly of the RNA polymerase I transcription machinery. The study addresses an intriguing question by proposing a catalytic-independent role for KMT2A in rDNA transcription, potentially linking the KMT2A-dependent pathway to histone acetylation. However, several aspects of the proposed mechanism require further experimental validation. Notably, while the current evidence demonstrates associations among KMT2A, PCAF occupancy, histone acetylation, and rRNA transcription, it does not fully support the proposed objectives.

      Strengths:

      This could be the first report of a lysine methyltransferase regulating an acetyltransferase in Pol I-mediated gene expression.

      Weaknesses:

      (1) The causal relationship between KMT2A and the recruitment of PCAF needs to be demonstrated. Simply showing reduced PCAF occupancy after depleting KMT2A does not, on its own, prove direct recruitment. The authors should investigate whether KMT2A and PCAF physically interact, and whether this interaction depends on DNA or RNA.

      As we have shown that KMT2A and PCAF interact by endogenous IP (Fig. S4D) and pull-down (Fig. S4E) experiments with the KMT2A C-terminal fragment containing the TAD domain, does the Reviewer mean in vitro interaction? Both proteins are large and may be difficult to produce in bacteria.

      We do plan to perform reverse IP as suggested by Reviewer 2, and during these experiments, we can plan to test if this interaction is promoted by DNA or RNA by testing it in the presence or absence of DNase or RNase.

      (2) The main prediction of the model is that restoring PCAF activity should reverse the molecular effects caused by the depletion of KMT2A. The authors should test whether PCAF restoration can mitigate the consequences of KMT2A loss. They should also assess PCAF occupancy, H3K9 acetylation levels, Pol I occupancy, and nascent rRNA synthesis.

      We agree with the Reviewer that this is the central hypothesis of our study. Ideally, a simple global restoration or overexpression of PCAF should be able to rescue the effects caused by the depletion of KMT2A. However, based on our model and existing literature, we expect the following issues:

      (1) We propose that KMT2A serves as a recruiter, a physical scaffold, to target PCAF to the rDNA. Therefore, mere overexpression of PCAF, in the absence of KMT2A, will not be able to ensure its localisation to the rDNA locus.

      (2) Transcription activation by KMT2A involves tight synergy between its TA domain and specific KATs (PMID: 24253305; PMID: 31515273). The KMT2A TAD contains intrinsically disordered regions that must directly engage co-activator docking sites—specifically interacting with domains like the KIX domain of p300/CREB-binding protein acetyltransferase complexes—to transition into a stable secondary structure and drive downstream chromatin remodelling. Because this functional synergy requires the physical presence of both the KMT2A TAD and the KAT complex at the promoter, in our opinion, restoring PCAF activity in a KMT2A-depleted background cannot rescue localized H3K9 acetylation at the rDNA promoter. While we are not sure how PCAF engages with the KMT2A TAD domain, based on the above literature, the physical presence of KMT2A may be required.

      We will test this hypothesis by overexpressing PCAF in the absence (or presence) of KMT2A, monitoring rRNA expression, and then plan to undertake future experiments accordingly.

      (3) The catalytic-independent function of KMT2A should be directly investigated. The absence of a significant change in H3K4me3 levels following KMT2A depletion does not confirm that KMT2A's catalytic activity is not essential. Rescue experiments comparing wild-type KMT2A with a catalytically inactive variant would provide a much stronger assessment of the proposed non-catalytic mechanism.

      We thank the reviewer for their comment. We completely agree that it is important to rule out whether catalytic activity of KMT2A is essential for rRNA transcription. We have shown in Fig. 4G that the catalytic point mutant carrying the N3906A mutation is able to recruit PCAF and RNA Pol I to the rDNA but not the KMT2A∆TAD mutant. This rescue experiment supports our hypothesis that the catalytic activity of KMT2A is not involved in mediating transcription at rDNA, but TA domain-dependent recruitment of PCAF is critical.

      (4) The manuscript highlights H3K9ac; however, various acetyltransferases and histone acetylation marks are linked to active rDNA. The authors should investigate whether KMT2A specifically regulates H3K9ac or leads to broader changes in histone acetylation at rDNA.

      We thank the reviewer for their comment. This is indeed an insightful suggestion. As shown in Fig 3. Multiple histone acetylation marks decorate the rDNA, and it is not possible for us to test them all. We propose to test some of these marks during revision to gain insight into the range of KMT2A-mediated regulation.

      (5) Due to the highly repetitive nature of rDNA, the manuscript must include detailed information about the reference assembly, mapping strategy, management of multimapping reads, normalisation processes, and biological replicates. The authors should demonstrate that any observed changes in occupancy are not due to technical differences in rDNA mapping or variations in copy number.

      We thank the reviewer for their comment. As indicated in the manuscript, we have used the pipeline from George et al. al, 2023, PMID: 37121547, which describes all these parameters in detail. Hence, we have omitted a repetition here but added a brief sentence in the Methods now.

      (6) KMT2A regulates a wide range of transcriptional programs, and its depletion can affect proliferation, cell-cycle distribution, or nucleolar function. The authors should include appropriate controls to demonstrate that the rDNA phenotype is not a result of changes in cellular proliferation or a generalised response to transcriptional or nucleolar stress.

      We thank the reviewer for highlighting this important point. The transcriptional profiling recently published by our lab [Lone et al. (2026), PMID: 42096476; Malik et al., 2023, PMID: 37379335] provides clear evidence that helps distinguish direct regulatory effects from generalized stress responses. Our global transcript analysis indicates that KMT2A depletion specifically downregulates transcription at the rDNA repeats without inducing hallmark markers of nucleolar stress or broad cell-cycle arrest.

      (7) The CSB and B-WICH complex have previously been linked to the recruitment of PCAF and the acetylation of H3K9 at active rDNA. The authors should investigate whether KMT2A operates independently of these factors or if KMT2A functions within an established pathway for remodeling rDNA chromatin.

      We agree with the Reviewer that CSB and the B-WICH complex, PCAF recruitment, and H3K9ac deposition are indeed a well-documented axis at active rDNA. In the present study, our focus is on establishing the functional role of KMT2A at the rDNA locus. Given that KMT2A traditionally acts as a histone methyltransferase that often precedes or cooperates with acetyltransferases like PCAF, it is highly plausible that KMT2A operates sequentially or in concert with the B-WICH pathway to remodel chromatin.

      However, mapping these biochemical interactions is beyond our current aims. Nonetheless, we agree this is a crucial conceptual link, and we will expand this link in our Discussion.

      (8) The distinction between active and silent rDNA should be taken into account. The authors need to determine whether KMT2A/PCAF occupancy is preferentially associated with active rDNA copies. Sequential ChIP analysis or the use of established markers for active, poised, and silent rDNA would help clarify the chromatin context in which the proposed mechanism operates.

      We appreciate the Reviewer’s suggestion to determine if KMT2A/PCAF occupancy is restricted to active rDNA copies. While this is an important factor to consider, making a clear distinction is currently not possible due to several constraints. First, the highly repetitive nature of rDNA repeats makes it difficult to differentiate active from silent fractions both experimentally and bioinformatically. Second, performing sequential ChIP to definitively map this co-occupancy is technically challenging and establishing and optimising this protocol within the revision timeframe will be extremely difficult.

      Furthermore, the exact histone landscapes defining active, poised, and silent rDNA are not yet fully characterized; much of the existing consensus in epigenetic literature relies heavily on observations drawn from RNA Polymerase II systems rather than Pol I repeats. As demonstrated by Xie et al., 2012 [PMID: 22570494], rDNA promoters frequently feature bivalent marks—bearing both active H3K4me3 and repressive H3K27me3 modifications—that characterize a poised, non-transcribing state. This biological ambiguity makes absolute active/silent categorization extremely difficult in our case.

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    1. Author response:

      The following is the authors’ response to the original reviews.

      eLife Assessment:

      The study by Izquierdo and colleagues provides important insights into the field of genomic and transcriptomic prediction of traits across multiple environments. The rationale and analyses conducted to integrate the two types of ~omics datasets across two environments are solid. However, some clarification would be appreciated in the presentation of the results, and adding some statistical control to clarify how the predictors were selected, or assessing their importance using the SHAP framework, would further consolidate the findings.

      We appreciate the positive feedback and the constructive evaluation of our work. In response, we have added further clarification to the Results section and provided additional detail on the feature selection procedure to facilitate understanding of how predictors were identified within the modeling framework.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      P. Izquierdo et al. investigated the genetic determinism of various traits of interest in switchgrass using large-scale genomic and transcriptomic data. More specifically, they worked on a diversity panel comprising 426 genotypes evaluated in common-garden experiments at two locations (Michigan and Texas). The phenotypic and genomic data were already published. In this work, they produced transcriptomic data for each of the 426 genotypes at each site, and they carried out phenotype predictions using genomic and transcriptomic data separately or together. While they were moderately correlated at each location, both omic information appeared to be complementary for the prediction of phenotype. To further exploit the fact that they have data across two locations, they computed differences for phenotypes and transcripts between locations as indicators of trait and transcript plasticity, respectively. They built predictive models of trait plasticity using genomic information and transcript plasticity, which proved to be quite accurate for traits affected by GxE. Finally, they made use of SHAP values from predictive models of flowering time and biomass at each location, as well as for their plasticity, to gain insight into their genetic determinism. These SHAP values provide the importance of the predictive features (SNP and/or transcripts) for trait prediction. This allowed them to confirm some candidate genes and to propose new candidates for both traits.

      We appreciate the reviewer's thorough and constructive summary of our work. We would like to clarify that while the genomic data were previously published, the transcriptomic and phenotypic data were generated as part of the present study. We have revised the text to make this distinction explicit.

      Strengths:

      I found this study interesting and rich. I think the sample size (426 genotypes) is large enough to support the findings. The use of a modern machine-learning approach (XGBoost) together with SHAP indices to find interesting features and get insights into the biological mechanisms underlying flowering time and biomass production is quite original. The methodology employed is globally sound. I also like the fact that the authors accounted implicitly for the population structure by providing a baseline prediction using the first 5 PCs.

      Weaknesses:

      While the methodology is globally sound, I sometimes had difficulties following exactly what was done. This is partly due to the fact that the authors used 2 omics (SNPs and transcripts) to predict phenotypes, and sometimes, in the results, it is not clear which of the 2 is the focus. This was especially the case for the importance of the features and the interpretability of the models, where I found it sometimes hard to tell whether the analysis was done on SNPs or transcripts.

      We have revised the text throughout to clarify when models using SNP, transcript (T), or both data types (S+T) were the focus of the analysis.

      Also, regarding the methodology, I did not understand why the authors needed to perform a feature selection approach. Maybe it was required to perform the interaction analysis, which could not be deployed on all the features? But regarding the importance of the features, I do not get the added value of the selection over the direct use of SHAP indices when using all features. Maybe this is because I am not a specialist in this kind of approach, but maybe the authors could add more details to explain the rationale behind the feature selection.

      Feature selection was performed to identify the subset of features that optimized predictive accuracy while reducing model complexity. By retaining only the most informative features, the resulting models achieve higher predictive accuracy than models trained on all features, and model interpretation is simplified. The rationale and procedure are described.

      Regarding SHAP interactions specifically, the number of features used to estimate SHAP interaction scores was limited to 5,000 due to the high computational demands of this analysis. Interaction scores are estimated for each individual in the training population, producing a 5,000 × 5,000 interaction matrix per individual. With 306 individuals in the training population and 10 independent model runs, this corresponds to 3,060 matrices of this size.

      Reviewer #2 (Public review):

      Summary:

      The authors aimed to evaluate whether integrating genomic (SNP) and transcriptomic information with machine learning can improve phenotypic prediction of polygenic traits across environments. The manuscript explored not only the predictability across models and predictor feature sets, but also attempted to identify meaningful genes and interactions underlying trait variation.

      Strengths:

      The main strength of the manuscript is its integration of SNP, transcriptomic, and phenotype datasets for 426 sorghum genotypes between Texas and Michigan. It provides a systematic comparison of predictor types (SNP versus transcriptomic abundance) and model strategies to integrate them.

      Weaknesses:

      (1) Experimental Design

      The experimental design raises several concerns that should be clarified before strong biological conclusions are drawn from the transcriptomic analyses.

      First, the transcriptomic sampling is not well aligned with the developmental stages most relevant to the phenotypes being modeled. Leaf tissue was collected at a single time point in each environment, whereas traits such as flowering time, biomass, tiller count, and panicle height arise from developmental processes occurring over extended and potentially distinct temporal windows. Consequently, the measured expression profiles are likely to reflect physiological states specific to the sampling dates (May 5-6 in Texas and June 22-24 in Michigan) rather than the regulatory processes underlying the target phenotypes.

      We selected the pre-flowering stage because it represents a critical developmental transition during which plants remain largely vegetative while initiating reproductive development. Gene expression at this stage is therefore expected to capture regulatory processes associated with flowering initiation while also reflecting pathways involved in vegetative growth and biomass accumulation. In our previous work in maize (Azodi et al., 2020), we demonstrated that transcriptomic profiles obtained at a single developmental stage can contain information predictive of complex traits. Although the expression profiles analyzed here do not capture the full temporal dynamics underlying traits such as flowering time and biomass, they provide a biologically meaningful snapshot of molecular variation relevant to these traits. We have revised the manuscript to acknowledge this limitation and to clarify that our findings should be interpreted as associations between gene expression measured at the pre-flowering stage and the phenotypes of interest, rather than as evidence that all identified genes directly regulate these traits throughout development.

      Second, the phrase "haphazardly randomized" is questionable for a field experiment. It is unclear whether the design included formal randomization, blocking, row/column structure, or spatial correction. Without explicit accounting for spatial field heterogeneity, environmental variation within sites may confound genotype and transcriptomic effects.

      We thank the reviewer for this comment and agree that the original wording was unclear. The text has been revised to more precisely describe the experimental design. The establishment and management of the common gardens are described in detail in Lovell et al. (2021). Briefly, the diversity panel was established as a single-block planting at each location, with genotypes distributed throughout the field and arranged in a honeycomb design in which each individual had four nearest neighbors located 1.5 m apart. We have removed the phrase "haphazardly randomized," which was imprecise.

      Because only a single replicate of each genotype was established at each site, formal spatial correction was not performed, as genotype and within-site spatial effects cannot be estimated independently in this design. We acknowledge that additional replication would have improved our ability to account for fine-scale environmental heterogeneity.

      However, several aspects of the experimental design reduce the likelihood that spatial variation substantially confounded the results. The diversity panel is part of a coordinated common garden network spanning ten field sites across the United States, designed primarily to evaluate genotype-by-environment interactions across contrasting environments rather than within-site spatial variation. In addition, the AP13 reference genotype was distributed throughout the experimental plots and did not show evidence of substantial spatial heterogeneity at the Michigan site, suggesting that within-site environmental variation was limited. We have added text acknowledging this limitation and its implications for interpreting genotype and genotype-by-environment effects.

      Third, the Methods do not clearly describe biological replication for RNA-seq. If each genotype-by-environment combination were represented by a single transcriptomic sample, then within-genotype expression variance cannot be estimated. This is important because transcript abundance is highly sensitive to microenvironment, sampling time, tissue status, developmental stage, and technical variation. The absence of replication significantly weakens confidence in gene-level feature importance and gene-gene interaction claims.

      We appreciate this thoughtful comment and fully acknowledge that the absence of biological replication for RNA-seq within each genotype-by-environment combination is an important limitation of this study. Because the diversity panel consisted of a single plant per genotype at each field site, transcriptomic data were generated from one biological sample per genotype-by-environment combination, and within-genotype expression variance could not be directly estimated. We recognize that transcript abundance can be influenced by microenvironmental conditions, developmental stage, tissue status, sampling time, and technical variation, all of which may affect confidence in gene-level feature importance and inferred interaction effects.

      The scale of the experiment, involving 426 genotypes evaluated across contrasting common gardens, made biological replication for RNA-seq financially and logistically impractical. This experimental design was established to maximize representation of genetic diversity and environmental variation across a large multi-environment common garden network rather than to obtain replicated transcriptomic measurements within individual sites. To minimize uncontrolled variation, tissue was collected at both locations at approximately the same pre-flowering developmental stage, and standardized protocols for tissue collection, library preparation, sequencing, and data processing were applied across all samples.

      Although individual genotype-by-environment combinations were not biologically replicated, the analyses leverage substantial replication at the level of alleles and population structure, as individual alleles and transcripts are represented across many genetically distinct accessions spanning multiple ecotypes. This is analogous to many human population-scale transcriptomic studies, where each genotype is typically represented by a single biological sample and inference is made across genetically diverse individuals rather than replicated measurements of the same genotype.

      Importantly, the goal of this study was to identify transcriptomic patterns that are predictive of phenotypic variation across genotypes and environments, rather than to establish causal regulatory relationships. Accordingly, the genes and interaction patterns identified through model interpretation should be viewed as candidate predictive associations and hypothesis-generating signals that warrant validation in future studies with replicated sampling and controlled experiments. We have revised the manuscript to more clearly acknowledge these limitations and to align the interpretation of gene importance and interaction analyses with the predictive scope of the study. 

      Four, the analysis of expression differences across environments is based on a simple subtraction (TX - MI) followed by correlation with genetic similarity. This approach is not standard in transcriptomic analysis and does not account for variability, replication, or statistical uncertainty. Conventional methods for assessing differential expression and genotype-by-environment interactions rely on model-based frameworks that explicitly estimate variance components and test for interaction effects. Without such modeling, the observed expression differences may reflect noise or confounding factors rather than genotype-driven responses.

      We appreciate this comment. Our approach to estimating expression differences across environments was intended to quantify transcriptomic plasticity and evaluate whether variation in gene expression responses across environments could help explain and predict phenotypic plasticity. While this is not a conventional differential expression framework, our objective was not to identify differentially expressed genes or formally test genotype-by-environment interaction effects at the transcript level.

      Expression differences were calculated as TX − MI using log-transformed expression values. On the logarithmic scale, this difference is equivalent to the log expression ratio between environments and therefore provides a straightforward measure of the magnitude and direction of transcriptomic responses across locations. We used this metric as a descriptive measure of transcriptomic plasticity that could be related to genetic similarity and incorporated into predictive models of phenotypic plasticity. Consistent with this rationale, models based on expression differences across environments were able to predict differences in phenotypic performance between locations.

      (2) SHAP contribution values

      Although SHAP is a well-established framework for decomposing model predictions into feature-level contributions, its use in this manuscript raises several concerns regarding interpretation, statistical validity, and biological inference.

      First, SHAP values quantify the contribution of features within the fitted model, conditional on the joint distribution of inputs and the model structure. They do not represent causal effects or direct biological importance. 

      We agree that SHAP values do not represent causal effects or direct measures of biological importance. Rather, SHAP quantifies the contribution of features to model predictions within the context of a fitted model and the observed input distribution. Our rationale for using SHAP was not to infer causality, but to identify features that are consistently informative for predicting phenotypic variation. The underlying hypothesis is that features contributing strongly to accurate predictions may be associated with biological processes influencing the trait and can therefore serve as candidate genes or genomic regions for further investigation. This strategy has been widely adopted in genomics and plant biology, where interpretable machine learning methods are used to extract biological insights from predictive models. Accordingly, the genes and interactions highlighted by SHAP should be interpreted as predictive associations and candidate mechanisms requiring validation through independent experiments and functional studies. We have revised the manuscript to more clearly distinguish predictive importance from causal biological effects.

      There is a difference where SHAP values are often in log-odds and the regression model uses absolute units. 

      We thank the reviewer for this comment. We believe there may be a misunderstanding regarding the scale of the SHAP values reported in this study. The models analyzed here are regression models predicting continuous traits, not classification models. Consequently, SHAP values are expressed in the same units as the predicted phenotype and represent the additive contribution of each feature to individual predictions. The interpretation of SHAP values in log-odds units is specific to certain classification models where predictions are generated on the log-odds scale. We have revised the manuscript to clarify this point and avoid potential confusion.

      Without a fair evaluation of model fit, the interpretation of SHAP values needs to take a cautious step because a model could fit poorly when a feature shows very high SHAP values.

      We agree that SHAP values should be interpreted in the context of model performance. For this reason, model performance was evaluated prior to feature interpretation. Figure 1 presents the predictive performance of all models, and we focused our biological interpretation on flowering time and biomass because these traits are agronomically important and showed relatively stronger predictive performance compared to other traits, providing a more reliable basis for interpreting feature importance. We have revised the manuscript to emphasize that model interpretation should be considered in conjunction with model accuracy.

      In genomic data, where features are highly correlated due to linkage disequilibrium and co-expression, SHAP values can distribute contribution values across correlated variables in ways that are not uniquely identifiable. As a result, features highlighted as "important" may reflect correlation structure rather than true functional relevance.

      We agree that multicollinearity can complicate the interpretation of feature importance, as correlated features may share predictive information, resulting in importance being distributed among them or assigned preferentially to one feature over another. This issue is particularly relevant in genomic datasets due to linkage disequilibrium among SNPs and co-expression among genes. To reduce redundancy among genetic markers, SNPs were filtered using a linkage disequilibrium threshold of r<sup>2</sup> < 0.1 prior to model training, substantially reducing the number of highly correlated markers. We acknowledge, however, that correlation among features, particularly among co-expressed genes, remains present and may influence SHAP-based feature attribution. 

      To improve the robustness of feature interpretation, models were trained across 10 independent runs and SHAP values were averaged across runs, reducing sensitivity to individual model fits and providing more stable estimates of feature contributions. Nevertheless, SHAP values should not be interpreted as uniquely identifying the most functionally relevant feature within a correlated group of predictors. The genes and genetic variants highlighted by SHAP should therefore be viewed as candidate predictive features associated with trait variation rather than definitive evidence of causal biological relevance.

      This correlative structure can be exacerbated in this manuscript because of the use of TPM-normalized transcript abundances as predictor variables without biological replicates. Assume the estimates of transcript abundances are robust, TPM values are compositional, with a constant-sum constraint that creates dependencies among all genes that induce negative correlations. This issue is particularly relevant for the interpretation of gene importance and interaction effects, where correlated predictors can lead to unstable and non-unique attributions. This biological interpretation of transcript-based features remains uncertain.

      We agree that TPM-normalized expression values are compositional and may introduce dependencies among genes due to the constant-sum constraint. TPM normalization was selected because it facilitates comparisons of transcript abundance across samples by accounting for differences in sequencing depth and transcript length. Expression values were further transformed using log<sub>10</sub>(TPM + 1), which reduces skewness and stabilizes variance, making the data more suitable for machine learning analyses. We acknowledge that compositional effects and gene co-expression may influence feature attribution and the interpretation of gene importance. However, the primary objective of this study was predictive rather than inferential. In this context, log-transformed TPM values provide a standardized and comparable representation of transcript abundance across genotypes and environments, serving as consistent input for predictive models. Consequently, genes identified through SHAP analyses should be interpreted as candidate predictive features associated with trait variation, rather than as definitive evidence of direct causal biological importance.

      (3) Result interpretation

      For example, in page 11, "plasticity SNP- and transcriptomic-based models generally outperformed single-environment models for traits with low cross-environment correlation, such as green-up (Fig. 2c, r = -0.13, p < 8.3 × 10<sup>-3</sup>) and tiller count (Fig. 2f, r = -0.08, p = 0.1) (Supplementary Fig. S1)." is too broad. For green-up, the Diff model appears much better than MI, but not clearly better than TX.

      We thank the reviewer for this observation and agree that the original wording was too broad. We have revised the text to more accurately reflect the observed pattern, noting that difference-based models showed relatively stronger predictive performance for traits with low cross-environment correlation, while generally performing worse than single-environment models for traits with high cross-environment correlation. We believe this pattern is biologically meaningful, as transcriptomic differences across environments are expected to be most informative when phenotypic responses differ substantially between locations. We have revised to more accurately characterize these results.

      And, same page 11, "...Diffexp was more predictive than SNPs for trait plasticity in biomass, flowering time, and tiller count..." only holds true for biomass, not flowering time, or tiller count.

      We thank the reviewer for this observation and agree that the original statement was too strong. Diffexp models showed higher predictive performance for biomass and tiller count, whereas performance for flowering time was comparable between Diffexp and SNP models. We have revised to more accurately characterize these results.

      The aspect of "complementary information" between SNP and transcriptomic models in page 12 is stronger than what is supported by Figure 2. Figure 2 shows different predictive performance, but it does not by itself demonstrate complementarity. Establishing complementarity requires evidence that combining SNP+T improves prediction consistently or captures distinct, non-overlapping signals. Yet the preceding section says SNP+T outperformed either single data type in only 15% of cases, with modest gains. This is confusing. Also, there was not G+T in Figure 2; it is SNP+T.

      We agree that the term "complementary" was stronger than what the results in Figure 2 directly support. We have revised the text to describe these findings more cautiously, emphasizing that SNP and transcriptomic models may capture partially distinct aspects of biological variation. In the following section, we further address this point by showing that the two model types identify largely distinct sets of predictive features, suggesting that they reflect different sources of information relevant to trait prediction. We also thank the reviewer for noting the SNP+T vs. G+T inconsistency, which has been corrected throughout the manuscript.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      (1) I found that the title does not properly reflect the content of the paper. The term "artificial intelligence" is a bit misleading: I was expecting deep learning-based predictions. GxE and plasticity are clear strengths of the paper that are not present at all in the title. The same holds for multi-omic integration. Maybe you could consider revisiting the title.

      We thank the reviewer for this suggestion and have revised the title to: "Multiomic integration using interpretable machine learning reveals genetic mechanisms of trait variation and phenotypic plasticity in switchgrass." This revision highlights the integration of genomic and transcriptomic data, explicitly mentions phenotypic plasticity, and replaces "artificial intelligence" with "interpretable machine learning," which more accurately describes the modeling framework employed.

      (2) In general, the quality of the figures is very poor, and it did not allow me to perform a deep assessment of their content, which is sometimes hardly visible.

      We agree that figure quality in the submitted PDF was suboptimal. The reduction in image resolution occurred during conversion from the original Word document to PDF. We have uploaded a revised manuscript with higher-resolution figures to ensure all elements are clearly visible.

      (3) To estimate plasticity in phenotypes and transcripts, you use differences between locations. Other options have been proposed in the literature, like ratios, for example. I think the choice of the difference is probably a good one, but maybe you could justify it in the introduction.

      We chose to estimate phenotypic and transcriptomic plasticity using differences between locations because this metric preserves both the magnitude and direction of environmental responses while avoiding the instability associated with ratio-based measures, particularly when values are small. Furthermore, because transcript abundance values were modeled using log<sub>10</sub>(TPM + 1)-transformed data, differences between environments are conceptually equivalent to log expression ratios, as log(A) − log(B) = log(A/B). This justification has been added to the manuscript.

      (4) Figure 1. I wonder why you computed correlation matrices between genotypes for transcriptomic data instead of simply covariance matrices, which would be closer to the genomic relationship matrix.

      Our intention in Figure 1 was to visualize overall similarity among samples based on transcriptomic expression profiles across genes. We used Pearson correlation because it is widely applied in transcriptomic analyses to capture relative expression patterns while remaining independent of absolute expression magnitude and scale differences among samples. Covariance matrices, by contrast, are strongly influenced by feature variance and scale, which can complicate interpretation of overall transcriptomic similarity in high-dimensional expression datasets.

      (5) Figure 1. You calculate correlations between phenotypic distance and genomic distances for the different traits, but I think this is somehow related to the genomic heritability estimation. Could you please elaborate on this or provide the rationale under your analysis?

      We agree that the correlation between genomic relationships and phenotypic similarity is conceptually related to genomic heritability, as both analyses evaluate the extent to which genetic similarity is associated with phenotypic variation. However, their objectives differ. The correlation analysis between SNP, eCor, and phenotypic distance was intended as an exploratory assessment of whether genetically or transcriptomically similar genotypes tend to exhibit similar phenotypic responses across traits and environments. Genomic heritability estimation, in contrast, provides a formal variance component framework to quantify the proportion of phenotypic variance explained by genome-wide marker information. While related conceptually, these analyses address complementary but distinct aspects of the relationship between genomic, transcriptomic, and phenotypic variation.

      (6) L163-164: "Because genotypes with similar genetic information are expected to exhibit similar trait value": this is the definition of the heritability, so I would say that this is true to the extent of the heritability of the trait... Maybe you could consider modifying this sentence.

      Thank you for this suggestion. Our intention was not to invoke heritability directly, but rather to assess the associations among kinship, eCor, and phenotypic similarity within each environment and to compare the patterns captured by these different data types. We agree that the original wording could be interpreted as implying a deterministic relationship between genetic similarity and phenotypic resemblance. We have revised the text to focus on the association between genetic relatedness and similarity in expression and phenotypic profiles.

      (7) Figure 2. For the prediction with transcriptomic data, I understood that you matched data by site for the prediction, which is OK. But I wonder what would happen if you had used transcriptomic data from the other site and vice versa for the prediction, how much predictability you would have lost? I guess that this would somehow be related to the extent of GxE for each trait. Maybe it would be something interesting to look at?

      We thank the reviewer for this thoughtful suggestion. While cross-environment prediction is an interesting avenue for future research, our primary objective was not to maximize prediction across environments, as predictive ability would be expected to decrease substantially under strong G×E effects. Instead, we focused on single-environment models to: (1) identify transcriptomic features associated with trait prediction within each environment, and (2) evaluate which features were consistently important across environments. Furthermore, because G×E effects were observed, we developed TX − MI difference models to identify transcriptomic features associated with phenotypic plasticity. We therefore believe that the within-environment and plasticity-focused analyses were more closely aligned with the objectives of this study than cross-environment prediction would have been.

      (8) The calculation of local SHAP values for each genotype mentioned L331 and the clustering of genotypes based on such values, as presented in Figure 4, are not presented in the method section. Could you please provide more details?

      The estimation of SHAP values is described in the Methods section. Briefly, local SHAP values were calculated for each genotype, and genotypes were subsequently clustered based on these values using hierarchical clustering with Euclidean distance.

      (9) Gene-by-gene interactions paragraph: I am a bit confused here regarding which omic was used for looking at the interaction. Naively, I would have gone with the SNPs, but maybe you would rather use the transcripts instead? This would explain why in Figure 5 c-h, the x axes seemed to correspond to transcripts rather than SNPs. Could you please clarify and explain why you focused here on transcripts rather than SNPs?

      We thank the reviewer for this comment. To clarify, gene–gene interactions were assessed using transcriptomic models. This choice was motivated by three observations: (1) transcriptomic features were enriched among the most important predictors in the multi-omic models; (2) transcriptomic models identified a greater number of benchmark genes than SNP-based models; and (3) gene expression data provide a more biologically interpretable framework for assessing gene–gene interactions, as transcripts more directly reflect gene activity and regulatory processes than individual genetic variants. We have revised the manuscript to make this rationale explicit.

      (10) Materials and Methods:

      - Were there replicates of the genotypes within each site?

      This diversity panel is part of a multi-institutional project maintaining 10 common gardens across the United States. Given the scale of the experiment and the large number of genotypes evaluated, the design included a single plant per genotype at each site rather than within-site replication. We acknowledge this as a limitation and have discussed it explicitly in the revised manuscript.

      - Have the data (phenotypic/transcriptomic) been corrected for spatial effects?

      Because only a single replicate per genotype was evaluated at each site, genotype and local spatial effects could not be estimated independently. Applying a spatial correction under these conditions could inadvertently remove true biological variation. The randomized honeycomb design was intended to minimize systematic spatial confounding; however, we acknowledge that residual environmental heterogeneity may still contribute to phenotypic and transcriptomic variation.

      - L502-503: Could you please write the model formally instead of R code?

      The model has been written formally.

      - Genomic heritability estimates: I wonder how useful they really are? I suppose you could have used the model L502-503 to estimate genomic heritability in general across the 2 sites.

      We agree that the mixed model described in the revised manuscript could be used to estimate genomic heritability jointly across both sites. In this study, however, genomic heritability was estimated within individual environments to evaluate trait predictability within each location and to assess the heritable component of phenotypic plasticity. Genomic heritability also provides an important benchmark for interpreting prediction results, as the theoretical upper limit of prediction accuracy is approximately proportional to the square root of heritability under quantitative genetic theory.

      - L523: I am not sure what LD> 0.1 means. Could you please give more details, e.g., which measure of LD, which software, and which parameters?

      We have clarified this point in the Methods. LD pruning was performed using the +prune plugin in BCFtools, with pairwise LD measured as the squared Pearson correlation coefficient (r<sup>2</sup>). SNPs with r<sup>2</sup> > 0.1 within a 5 Mb sliding window were removed to retain a set of more independent markers.

      - L526: How many leaves were sampled per plant? Or maybe a particular leaf was chosen?

      For each plant, we collected the fully expanded leaves at the highest point on each tiller. The proximal ~4 cm (length of microcentrifuge tube) of that harvested leaf was then flash-frozen in liquid nitrogen for subsequent RNA extractions.

      - L592-597: I understand that training and test sets were stratified according to biomass (log-transformed) in TX. Could you please explain why this trait/location was chosen for the stratification?

      Training/test stratification: We chose log-transformed biomass in TX for stratification because biomass is the primary agronomic trait of interest in switchgrass and exhibits greater phenotypic variation in TX compared to MI, allowing stratification to better preserve the full range of values in both the training and testing sets. The same training/testing split was subsequently applied to all analyses to ensure consistent and fair comparisons across traits, environments, and data types.

      (11) Data availability: Maybe the read counts could also be provided on top of the raw RNA sequences. This would ensure, to some extent, reproducibility of the analyses, especially because the code for processing RNA-seq reads does not seem to be released in the GitHub repository.

      The RNA-seq pipeline used in this study is described in the revised manuscript. The pipeline code is maintained in an internal GitLab repository at JGI and is therefore only accessible within JGI systems. To facilitate reproducibility, we have deposited the TPM count matrix used in our analyses in the following Zenodo repository: https://zenodo.org/records/21781035

      (12) Code availability: The code to run Bayesian regression models does not seem to be released.

      The code for the Bayesian regression models has been added to the manuscript repository.

      Reviewer #2 (Recommendations for the authors):

      The manuscript will benefit the most from additional biological replicates for RNAseq, as well as the phenology alignment with data collection. Further recommendations for improving the clarity in experimental design and alignment between claims and evidence.

      We agree that additional biological replication for RNA-seq and transcriptomic sampling across multiple developmental stages would further strengthen the study. However, given the scale of the experiment, 426 genotypes evaluated across contrasting field environments, generating replicated transcriptomic datasets at multiple developmental stages was not logistically or financially feasible. Despite these constraints, the experimental design enabled characterization of transcriptomic and phenotypic variation across a large natural diversity panel and the identification of predictive patterns associated with trait variation across environments. We have revised the manuscript to more clearly describe the experimental design, sampling strategy, and study limitations, and to ensure that conclusions are appropriately aligned with the evidence presented.

      Minor corrections:

      (1) MAF threshold in Line 522, page 27. It should be > 0.05?

      Corrected to > 0.05. 

      (2) SNP+T versus G+T.

      Revised to SNP+T consistently throughout the manuscript. 

      (3) Include FDR-adjusted p-value thresholds.

      FDR-adjusted p-value thresholds: For the Pearson correlations reported in this study, each represents a single pre-specified comparison rather than a family of simultaneous tests, and raw p-values are therefore appropriate. For the benchmark gene enrichment and Wilcoxon rank-sum tests, where multiple comparisons were performed across models and traits, FDR correction has been applied using the Benjamini– Hochberg procedure and the reported p-values have been updated accordingly. 

      (4) Avoid ambiguous phrasing like "generally consistent" and "generally outperformed".

      Revised throughout the manuscript. 

      (5) The mention of artificial intelligence in the Abstract is largely conceptual and reads more like discussion material rather than the main finding of the manuscript, per eLife's Abstract requirements.

      The mention of artificial intelligence has been revised in the Abstract in accordance with eLife's guidelines.

    1. Author response:

      We thank the reviewers for their careful evaluation of our manuscript and their constructive feedback. We appreciate the points raised and will take them into consideration when revising the manuscript.

      We plan to clarify and refine certain aspects of the interpretation and discussion, particularly regarding the relationship between Samp1, chromatin organization, and myogenic differentiation. We will also aim to strengthen the study with additional experiments and analyses where feasible, addressing the reviewers’ suggestions to the extent possible within the scope of the study.

      We believe these revisions will help improve the clarity and strength of the manuscript.

    1. Author response:

      The following is the authors’ response to the original reviews

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      In this work, the authors study the migration of isolated cells and of cells in ensembles. They quantify several aspects of the corresponding migration patterns and investigate how these quantities depend on molecules that are known to play an important role in migration. Furthermore, they study the effect of external cues on these migration processes.

      Strengths:

      The authors provide a clean and uniform setting for comparing the migration of isolated cells and of cells in an ensemble in control and mutant conditions, and in the presence and absence of external cues. This allows for a meaningful comparison between different conditions. In this way, the authors obtain useful data that link the migration of isolated cells to that of cells in collectives.

      Weaknesses:

      A major weakness of the manuscript is that the authors do not properly introduce the quantities and concepts they are working with. In this way, it is hardly accessible for a reader who does not have a thorough background in cell migration and anomalous transport. In addition, the manuscript uses some notions that are not standard, for example, vinculin or FA stability, which are not properly introduced. Most strikingly, "collective directional memory" is not defined.

      We thank the reviewer for pointing this out. We have now added the definition of collective directional memory in the introduction:

      “... cells that migrate collectively acquire long-term directional memory, which specifically requires α-catenin in AJs and results from coordination of velocities between neighboring cells. For this reason, we define it as a collective directional memory.” and in the results section:

      “... the transition in directional memory observed at confluence are the results of bona fide AJ-mediated intercellular adhesion, but independently of the cadherin subtype. Consequently, we define as a collective directional memory this long-term directional memory that arises from neighbor interactions.”

      The definition of anomalous transport is given in the results section too:

      “we found that the average Mean Square Displacement as function of lag time ∆t (MSD, see Materials and Methods) was better described by a persistent random walk (Fürth et al. 1920, Uhlenbeck et al. 1930) than anomalous diffusion: the MSD transitioned from ballistic (MSD ∼ ∆t<sup>2</sup>,∆t → 0) to pure diffusion (MSD ∼ ∆t,∆t → ∞) with a persistence time P of the order of 10min, rather than scaling as ∆t<sup>𝛼</sup> with α ̸\= 1” and in the Materials and Methods:

      "MSD(∆t) curves were fit with the Fürth equation MSD = 4_D_(∆t−P(1_−exp(−∆_t/P))) where D is the coefficient of diffusion and P the persistence time, as a model of persistent random walk, or with MSD ∼ ∆t<sup>𝛼</sup> (straight line of slope α in ln−ln scale), as a model of anomalous diffusion, with anomalous exponent α > 1 for super-diffusion."

      The definition of vinculin and FA stability, which we now specify as “molecular stability” is given in the Materials and Methods section:

      “We use the immobile fraction of vinculin and its mutants as a measure of vinculin stability and, by extension of the molecular stability of adhesions, because the stability of other adhesion proteins is regulated by the stability of vinculin (Carisey et al. 2013, Liu et al. 2016, Yonemura et al. 2010).”

      The authors infer relationships between different quantities, but they remain qualitative, even though the authors use a language that suggests otherwise. For example, "The combination of Focal Adhesion stability and force transmission from the cytoskeleton predicts the migration speed of single cells" (p 2). I am not sure what is meant by prediction, but this heading suggests that knowledge of FA stability and force transmission yields the migration speed. Reading this line, I expect that if I give you values for FA stability and force transmission, you would give me a value for the migration speed. Such a quantitative mapping is not provided. In fact, it cannot be provided, because - as mentioned before - these quantities are not properly defined, so I would not know how to measure them. I do not even know their units.

      We thank the reviewer for suggesting a more quantitative analysis. Initially, we used Boolean logic to build our model. Based on the effects of mutants, vinculin can be either tensed or not, and either stable or not, which yields four combinations that associate with more or less fast migration. We represent the model as a Venn diagram, which we now specify in the results section and figure legends. To complement this simplified approach, we have now added quantitative analyses by fitting changes in single cell speed, in the difference between single and collective cell migration speed, and in the ratio between collective cell migration speed and wound healing rate to the changes in tension, stability, or the gradients of tensions in FAs and AJs based on the quantitative measurements of speed (migration assays), tension (FRET index of vinculin sensors) and stability (immobile fraction of FRAP experiments) re-scaled between their extreme values across vinculin constructs, as explained in the Materials and Methods. This allows us to quantify the contributions of changes in tension, stability, and the gradients of tension to changes in single cell migration speed, in the difference between single and collective cell migration speed, and in the ratio between collective cell migration speed and wound healing rate. As shown in the added Fig. S2I, the change in single cell speed is explained by a linear combination of changes in tension and stability with contributions of 2_/3 and 1/_3, respectively. In Fig. S4J, the difference between single and collective cell migration speed changes with the stability exclusively, and its increased sensitivity to low stability is well captured by a power law. In fig. S5C, the ratio between collective cell migration speed and wound healing rate is set by the difference in mechanosensitivity between FAs and AJs in which 1/3 of that of AJs counts. Overall, these results confirm our initial models.

      Furthermore, the authors do interpret some of their results without explaining or justifying the basis for their interpretation. For example, they use the FRET index of vinculin - another notion that is not properly introduced - to make statements about mechanical stress.

      We are sorry that we had overlooked this important explanation. We have now added explanations in the main text, and in the Materials and Methods. Briefly, the FRET sensor module inserted in vinculin and its mutants is made of two fluorescent proteins separated by an elastic polypeptidic linker of known elasticity, such that an increase in tension on the protein will stretch the sensor and will decrease the amount of FRET between the two flanking fluorescent proteins. As a result, the lower the FRET, the higher the tension. We cite the original paper that introduced this sensor to allow the reader to get more information (Grashoff et al. 2010). Figures now also include the direction along which the tension increases when FRET changes.

      It also seems that the figures could be improved. Some of the sketches are, in my opinion, not helpful. Examples are Figure 3A (how could a cell move while the hexagonal arrangement of the cells is maintained?) or Figures 2F, 4F, and 6F (what do the colored ellipses indicate?). In Figures 1B, 1D, 2A, 2E, 3B, 3D-F, 4A, 4F, 5B-D, it is not clear which lines merely connect data points and which lines are fits to the data.

      We thank the reviewer for suggesting these improvements. We have now changed figure 3A for a more realistic drawing of the epithelium. We have specified in figure legends what colored ellipses are (as explained above, they are the Venn diagram categories), and whenever a line was a fit or a curve connecting data points.

      Reviewer #2 (Public review):

      Summary:

      The manuscript by Canever et al was assessed by three Referees at another journal, who brought up a range of critical points. I will not repeat a summary of the work; this can be found in the first-round reviews.

      Strengths:

      In their revised manuscript, the authors include substantial changes and additional reasoning. Along with their rebuttal letter, I think they make a very convincing case. While the claims are well supported by the analysis, I do not see that the findings need to be universal to be relevant. It might be rather surprising to me if there existed such a universality, in fact. I think that the findings are solid and interesting in their own right and are worthy of publication, especially with the amended discussion in this revision.

      Weaknesses:

      However, while the more bio-oriented parts are not fully accessible to me, I do have a few points from the data analysis point of view that need amendment. (1) The used mathematical models need to be specified more precisely. First, the authors confuse Levy flights and walks. These are distinct processes in the sense that a Levy flight does not have a finite variance and thus no finite speed. The proper model here would be Levy walks. As in a big body of the literature, both notions are used interchangeably here, while they are distinct processes. Then the authors speak about a "superdiffusive model", for which I do not find a proper definition. There exists an entire range of superdiffusive models, each with a different physical background, so this needs more clarity. The authors may consult one of the standard reviews for more details, e.g., Soft Matter 8, 9043 (2012) or Phys Chem Chem Phys 16, 24128 (2014). Overall, a few equations (maybe in the Supplement) would help to be more specific.

      We thank the reviewer for these suggestions. We have changed the main text as follows to address these points:

      - "To distinguish between the various walk models that could produce such a super-diffusive behavior (Lévy walk, fractional Brownian motion, or their combinations."

      - "we found that the average Mean Square Displacement as function of lag time ∆t (MSD, see Materials and Methods) was better described by a persistent random walk (Fürth et al. 1920, Uhlenbeck et al. 1930) than anomalous diffusion: the MSD transitioned from ballistic (MSD ∼ ∆t<sup>2</sup>,∆t → 0) to pure diffusion (MSD ∼ ∆t,∆t → ∞) with a persistence time P of the order of 10min, rather than scaling as ∆t<sup>𝛼</sup> with α ̸\= 1" and the Materials and Methods as follows:

      - "MSD(∆t) curves were fit with the Fürth equation MSD = 4D(∆t−P(1−exp−∆t/P)) where D is the coefficient of diffusion and P the persistence time, as a model of persistent random walk, or with MSD ∼ ∆t<sup>𝛼</sup> (straight line of slope α in ln−ln scale), as a model of anomalous diffusion, with anomalous exponent α > 1 for super-diffusion."

      We thank the reviewer for the additional references, we cite the more recent Meroz et al., 2015 for reference on anomalous diffusion.

      (2) For fractional Brownian motion, the authors should check the displacement correlation function; it should show slowly decaying, positive correlations. More details on the practical analysis of FBM can be found, e.g., in Phys Chem Chem Phys 27, 14350 (2025). These correlations should decay as a function of the bin time, e.g., as discussed for the opposite case of subdiffusion in Phys Rev E 88, 010101(R) (2013) [cf Fig 3b]. In general, FBM was determined to be a highly relevant process for a number of systems, including amoeba cells at shorter times, see the detailed analysis in Phys Rev Res 4, 033055 (2022). In this paper, there are also different ways to characterise the motion in terms of scaling. Exponents are detailed.

      We thank the reviewer for these suggestions and references. We have added explanations in the main text and in the Materials and Methods about the metric we use to characterize fractional Brownian motion together with the suggested reference Phys Chem Chem Phys 27, 14350 (2025).

      In summary, we define the angular memory as a modified angular correlation in which we consider the angular deviation θ of each elementary step of duration 10min from its immediate previous step of duration τ equal to the lag time ∆t. Specifically, the angular memory <sub>i,t</sub>(∆t) of a cell i at time t is defined as the cosine of the angle θ<sub>i,t</sub> between consecutive step vectors between times t−∆t and t, and between times t and t+10min, such that the step duration τ of the first vector and the lag time ∆t before the next are equal. M<sub>i,t</sub>(∆t) = cosθ<sub>i,t</sub> (∆t) = cos . Figures display ⟨M<sub>i,t</sub>(∆t)⟩. This metric measures the duration of the past that the cell considers when deciding on its direction. It decays to 0 when ∆t → ∞ for persistent random walkers and remains constant for fractional Brownian motion, similarly to the auto-covariance function of fractional Brownian motion C(∆t/τ) = ((∆t/τ +1)<sup>α</sup> +|∆t/τ −1|<sup>α</sup> −2(∆t/τ) <sup>α</sup>)/2, which is a constant C = 2<sup>α-1</sup> −_1 for all ∆_t \= τ, as in our definition of angular memory (while it decays to 0 when ∆t/τ → ∞, as pointed out by the reviewer) (Metzler et al. 2025). Ballistic motion yields 1 whatever ∆t and uncorrelated random walks, whether anomalous or not, yield 0. For this reason, and also because M<sub>i,t</sub>(∆t) was found more robust to noise than C(∆t/τ), we considered this metric a more compelling discriminant between fractional Brownian motion and other uncorrelated super-diffusive walks.

      (Of Note, we have increased the analysed data set in the revised Fig. 1D, 3D,F for the sake of representativeness. The conclusions are unchanged).

      (3) Some relevant approaches discussed in literature that should be discussed in the context of this work: eLife 9, e52224 (2020); Rep Prog Phys 86, 126601 (2023); Chaos 35, 023145 (2025). In the context of non-Gaussianity for active particles: Phys Rev E 104, 064615 (2021); New J Phys 25, 013010 (2023).

      We thank the reviewer for these interesting references. We have added them in the discussion as follows: "More recently, efforts have focused on developing analysis tools and models to account for heterogeneous migration properties along individual trajectories and among populations (Lemaitre et al. 2023, Khadem et al. 2021, Woszczek et al. 2025, Waigh et al. 2025, Han et al. 2020)." We have also made changes in the main text to specify when and how our data could indicate the presence or the absence of such heterogeneity in the migration of single cells and at confluence.

      (4) In the abstract, I am having some issues with the formulation in the sentence: "This directional memory emerges from fractional Brownian motion". It sounds as if FBM were a fully clarified phenomenon. I would prefer some statement along the lines that the data are consistent with such a mathematical modelling approach.

      We thank the reviewer for this suggestion. We have changed the formulation to "This behavior is consistent with a fractional Brownian motion that emerges from velocity coordination between neighboring cells with intact intercellular adhesion." After fixing these points, I think the manuscript will clearly warrant being shared.

      Reviewer #3 (Public review):

      This manuscript focuses on the presence/origin of directional memory during epithelial cell migration. It starts by analyzing single cells and then moves to more complex systems (confluent layers and scratch assays). The paper first demonstrates that the migration in all of these systems is well-described by persistent random walks, which likely emerge from fractional Brownian motion. This is an important demonstration, as it implies orientation memory in the systems. Then the paper proceeds to attempt to discern the origin of this memory and claims to establish key roles for adherens junctions and vinculin dimerization. While for the most part the manuscript is well-written, there are some significant overinterpretations in experimental results. The largest issue is demonstrating the role of vinculin dimerization, which is not a well-studied phenomenon inside living cells, as all data is reliant on a single point mutation (Y1065E). Additionally, the authors seem to be over-interpreting several of the assays; the statistical analysis does not seem to encompass all comparisons made, and the molecular model proposed does not clearly explain the observed results. The discussion could also be strengthened by considering other aspects of vinculin behavior (e.g., vinculin catch bonding) as well as discussing some other recent similar papers.

      (1) Likely the most significant issue with the manuscript is the interpretation of the vinculin Y1065E variant and the assumption that the only defect the mutations cause is a lack of dimerization. Vinculin dimerization is mediated by a conformational change in the vinculin tail domain induced by F-actin binding (Thompson, FEBS Letters, 2013). Dimerization of the vinculin tail domain has been clearly demonstrated in in vitro systems involving purified proteins, as the authors point out in the manuscript. However, the dimerization of full-length vinculin has not been well characterised in living cells. There are several reasons to suspect dimerization is potentially not prevalent in cells. For instance, in the presence of other actin-binding proteins, there may not be sufficient binding sites available on neighboring actin filaments to facilitate dimerization. Additionally, pY1065 vinculin and vinculin Y1065E have been associated with increased vinculin activation (Huang, JBC, 2014), so other effects seem possible. While the Y1065E variant clearly has an effect on the tension sensor readout and vinculin dynamics, further experimental evidence is needed to show that these effects are due to a lack of dimerization in living cells. To justify the definitive claims made in the manuscript, the authors likely need to develop, or employ, an assay for detecting vinculin dimerization in living cells. The authors could choose between intermolecular FRET, proximity labeling assays (i.e., antibodies with DNA for signal amplification), bimolecular fluorescent complementation (i.e., split GFP) based approaches, or some other approach. It should be noted that working with full-length vinculin, not just Vt, and designing an assay that can incorporate vinculin Y1065 variants (Y1065E and potentially Y1065A/F) would strengthen results. Also, the authors should be aware that the observation of strong dimerization may invalidate the use of FRET-based tension sensors in this system or at least necessitate intermolecular FRET control experiments.

      We thank the reviewer for raising this important point. We agree that we lack direct evidence for the dimerization of vinculin in cells. Therefore, we have replaced “dimerization” with “the ability to dimerize” wherever it is relevant in the revised version of our manuscript, to emphasize that the ability to dimerize does not imply dimerization. The effects of the YE mutant may then be attributed to a lack of proper dimerization, or to any other, yet to be discovered defect dependent on the mutation but independent of the loss of the ability to dimerize. We have added a sentence in the discussion to account for this possibility:

      "Whether vinculin dimerization, or another unknown independent function disabled by the YE mutation or phosphorylation of Y1065, is specifically involved in the adhesion and migration phenotypes described above may be addressed in future studies."

      We thank the reviewer for suggesting experimental strategies to assess vinculin dimerization in cells. In another work, we have evidenced proximity by intermolecular FRET in FAs between proteins with no known interacting domains (doi: 10.64898/2026.04.22.720102). This raises the possibility that FRET, as well as split-GFP and PLA, the detection ranges of which are equal or larger than FRET, will not be able to discriminate between bona-fide direct interactions and very close proximity in environments such as adhesion complexes where protein densities are very high. As pointed out by the reviewer, this is the major reason why we preferred not to carry the experiments in the present paper in a null background, such that the endogenous vinculin can prevent intermolecular FRET between neighboring sensors, as we explain in the Materials and Methods.

      Despite this methodological challenge, indirect evidence is largely in favor of dimerization in cells rather than against it, as explained below.

      - While there are indeed many actin binding proteins in cells, the proposed scenario by which they would prevent vinculin dimerization by competing with vinculin for actin binding seems very unlikely to us. Indeed, according to this scenario, vinculin would also fail to be under tension, since it needs to bind to actin for that. We show here, as many others did before, that vinculin is under tension, implying that it is able to bind to actin. Therefore, vinculin-bound actin may subsequently facilitate vinculin dimerization.

      - Additionally, vinculin also dimerizes in the absence of actin in solution, albeit at higher concentrations than in the presence of actin, equivalent to at least 0.1 molecule per 100nm² in any 2D section of the volume (doi: 10.1074/jbc.M111.244293, 10.1021/bi801764a). The density of vinculin within adhesions is promoted by the multiple neighboring vinculin-binding sites on its partners (such as talin, in which the neighboring binding sites are occupied nearly all at once upon talin stretch, doi:10.1021/acs.nanolett.6b00650, 10.1039/c5ib00307e), and is likely to reach a molecule per 100nm² in order to accommodate the traction forces that cells exert on their substrates (doi: 10.1021/acs.nanolett.6b04364). This exceeds the threshold concentration for vinculin dimerization in the absence of actin by at least an order of magnitude, and is therefore likely to offer another route for vinculin dimerization in addition to actin binding.

      - Furthermore, Huang et al have shown that Y1065 phosphorylation is required for the activation of vinculin, and the YE mutant mimics this behavior, but they have also shown that the activation level is quite similar to that of WT vinculin (compared to the loss of activation of the YA mutant). Additionally, phosphorylation or the YE mutation does not abolish the head-tail interaction of vinculin, as shown by Küpper et al. (doi: 10.1016/j.bbrc.2010.07.110), who also show that YE is less stable in FAs, in agreement with our results. Altogether, these results support a model by which pY1065 is required for vinculin activation but facilitates its inactivation and release from FAs, which is easily explained if dimerization, which antagonizes head-tail interaction, is impaired.

      In conclusion, in the absence of identified mechanisms to oppose vinculin dimerization in cells, and to better explain the observed phenotypes at the cellular level, vinculin dimerization in cells remains the most parsimonious scenario. We have added the following sentence to account for this:

      "Nevertheless, vinculin dimerization, with its ability to antagonize its head-tail interaction and to promote actin bundling, remains the most parsimonious mechanism that can explain the stabilization of vinculin in FAs and the stiffening of cells described here and elsewhere (Tolbert et al. 2014, Küpper et al. 2010)."

      (2) The authors have seemed to assume that FRAP and adhesion stability are interchangeable. To this reviewer’s knowledge, this is not the standard in the field. FRAP informs about molecular dynamics. Stability assays, which probe the spatial position of an entire focal adhesion over time (Zaidel-Bar, JCS, 2007, although other approaches are equally suitable), are typically used for assessing adhesion stability. If the authors wish to make strong claims about the stability of the adhesions, non-FRAP-based assays should be employed. Alternatively, the authors could interpret the FRAP data simply in terms of vinculin dynamics.

      We agree with the reviewer. We did not wish to make claims about the positional stability of adhesions as a whole, therefore, we now specify “molecular stability” wherever needed in the revised version of the manuscript, to reflect that we refer to the stability of the molecular components of adhesions. We use the immobile fraction of vinculin and its mutants as a measure of vinculin stability and, by extension of the molecular stability of adhesions, because the stability of other adhesion proteins is dependent on the stability of vinculin, as supported by the various references we cite in the text (Carisey et al. 2013, Liu et al. 2016, Yonemura et al. 2010).

      (3) A major conclusion in the manuscript is that in response to overexpression of a specific vinculin construct, focal adhesions behave the same in single cells, confluent cells, and collectively migrating cells for all the mutants but Y1065E. However, outside of the FRET measurements, there is not much evidence to support this claim. The authors should perform a greater comparison of the focal adhesions between the systems used in the manuscript (single cell, confluent cells, collectively migrating cells). Key measurements would include focal adhesion number per cell, focal adhesion size, focal adhesion orientation, vinculin dynamics (e.g., FRAP), focal adhesion stability, and some indicators of focal adhesion composition. For the last aspect, focusing on focal adhesion components that also have roles in adherens junctions, such as VASP, seems appropriate. Without such characterization, it is an overinterpretation to assume that focal adhesions are the same in each system and, therefore, effects are due to vinculin behavior in the adherens junctions.

      We thank the reviewer for raising this point. We do not assume or need to assume that FAs are the same in single cells, at confluence or during directed migration. The simplest model that explains our results, however, does imply that the response of FAs to a given construct is the the same whether cells are single, at confluence or involved in directed migration. We explain below our approach:

      - First, we show that the migration speeds of WT, FL, TL, T12 but not YE cells at confluence are predictable from their migration speed as single cells (Fig. S4C). Roughly, v<sub>c</sub> ≈ v<sub>s</sub> _−_10(_µ_m/h) for all but YE.

      - From here, there are two possible scenarios:

      (A) Each construct has the same effect on cell speed in single cells and at confluence through FAs, and AJs provide an additional downregulation of ≈ 10µm/h for all the constructs except YE. This implies that the mutants (except YE) have no effect on cell speed through AJs, since confluence induces the same decrease of ≈ 10µm/h in mutant cells as in FL or WT cells, in which vinculin is not mutated.

      (B) One or several mutants have different effects through FAs on cell speed between single cells and at confluence, and there is an additional effect of AJs on migration that depends on the mutant and that compensates for the difference in the effect of the mutant through FAs between single and confluent cells, such as to preserve the observed v<sub>c</sub> ≈ v<sub>s</sub> −10(µm/h). For instance, compared to WT, T12 could increase the speed of 15µm/h in single cells and of 15−xµm/h at confluence through FAs, but decrease it of 10+xµm/h through AJs to compensate. It is already straightforward that this scenario, which adds one unknown parameter per mutant, is the least parsimonious. It would require as many additional pieces of evidence to be considered equally likely as the first scenario.

      - If we review the effects of the mutants (except YE), there is no additional evidence in support of the second scenario: overall, mutants have similar effects on tension in FAs of single and confluent cells, as well as in AJs (Fig. 2D, 4D,E, S4G). They also have similar effects on stability in FAs and in AJs (Fig. 2E, 4F).

      - As a matter of fact, we do not exclude the possibility that the mutants have different effects in single and confluent cells on other FA properties. In light of the above, however, the principle of parsimony requires that evidence for 1) such differences and 2) their impact on cell speed be brought first before we can consider the second scenario equally plausible.

      In summary, there is no need nor other reason for x to be substantially different from 0 for any mutant, and YE is the only mutant for which there is a need for a specific contribution through AJs distinct from the other mutants to explain its difference in speed between single cells and confluent cells. We have now added a quantitative analysis of how this difference in speed changes across mutants (Fig. S4F and Materials and Methods). Results show that a power law provides an excellent description: the speed difference only depends on the molecular stability and not on the tension in AJs, and it is very weakly sensitive to the changes in stability between FL, TL and T12 while very sensitive to the low stability reached by YE. We detail this analysis below in response to Question 6.

      (4) What is shown in Figure 3G is not clear. How are P/Po and alpha shown on different areas of the same plot?

      We are sorry that our plot was not clear enough. For any given pair of simulation coordinates P<sub>0</sub>/τ and n=πρd<sup>2</sup>, the simulation yields either a persistent random walk or a super-diffusion behavior, based on the Akaike Information Criterion. Simulations show that the vast majority of the points that yield a persistent random walk (in blue) are grouped on the low density side of the plot, and the vast majority of the points that yield a super-diffusion behavior (in orange) are grouped on the high density side of the plot, typical of a system with two distinct phases within the space defined by the simulation parameters. Within each phase, each migration behavior changes as a function of the simulation parameters, these changes are quantified through either P/Po or alpha according to the most likely migration behavior of the phase. Of note, there are 3 regions of slight overlap: very low persistence (bottom line), very high persistence (top line) and the boundary between the two sides of the plot, because the finite number of simulation repeats (5) for each coordinate and their intrinsic stochasticity do not allow us to discriminate the two behaviors when their difference becomes smaller in these regions. Nevertheless, it is possible to determine the most probable behavior for each point and its close neighbors at the cost of some resolution, which results in a boundary that is slightly scaled rather than smooth if one looks closely. We consider that this is sufficient resolution for the purpose of this study. Our procedure is explained in detail in the Materials and Methods section. We have added a reference to this section in the figure legend for clarity.

      (5) It seems that an insufficient statistical test was used in many experiments. There are comparisons being made between systems (cell migration speed, FRET index...) that are not directly compared in a statistical test. Statistical tests are limited to differences from control (over-expression of full-length vinculin), and consistent increases or decreases (not quantitative values) are taken as evidence of similarity across systems. It seems that a more rigorous and standard approach would be to use an ANOVA/MANOVA with a suitable post-hoc test to perform all of these.

      We thank the reviewer for these suggestions.

      - For comparisons within a system (between migration speeds only, or between FRET index only...), we selected a priori the most sensible comparisons for our analysis: between the control FL and mutants (Fig. 2B-E, 4B-F), or between front and back cells for each constructs (Fig. 6C,E). To account for multiple comparisons of FRET to FL, we have now re-analysed our data with non-parametric Kruskal-Wallis and unpaired, two-tailed Dunn’s tests, and applied corrections to the p-values with the Benjamini-Krieger-Yekutieli (BKY) two-stage step-up FDR procedure after a check for positive dependency between comparisons by bootstrapping. To account for multiple comparisons of immobile fractions in FRAP experiments, we applied the same BKY corrections to p-values obtained from fit comparisons. To account for multiple comparisons of FRET between front and back cells, we applied the same BKY corrections to p-values obtained from Mann-Whitney tests since none of the comparisons shared any condition. Overall, the corrections resulted in marginal changes in p-values that did not alter our conclusions.

      - For comparisons of effects between systems (migration speed vs FRET index...), MANOVA and related approaches are not suited for comparisons between system-level means with different statistical units between systems. To account for effect sizes, we instead performed Pearson correlations or linear regressions, assuming a linear relationship between effect sizes from different systems (Fig. 6A, S2D-G, S4C,H). This allowed us to identify whether mutants have quantitatively similar effects in different systems and which of the mutants do not. Specifically, this is how we identified the YE mutant as different.

      - Finally, to quantitatively support our Boolean models of speed dependence on tension, stability and tension gradients (Fig. 2F, 4G, 6F), which binarized the output of each system for the sake of simplicity (fast/slow, tensed/relaxed, stable/unstable, mechanosensitive/insensitive), we have now performed additional regression analyzes between re-scaled data (as detailed in the Materials and Methods). This allows us to quantify the contributions of changes in tension, stability, and the gradients of tension to changes in single cell migration speed, in the difference between single and collective cell migration speed, and in the ratio between collective cell migration speed and wound healing rate. As shown in the added Fig. S2I, the change in single cell speed is explained by a linear combination of changes in tension and stability with contributions of 2_/3 and 1/_3, respectively. In Fig. S4F, the difference between single and collective cell migration speed changes with the stability exclusively, and its increased sensitivity to low stability is well captured by a power law. In fig. S5C, the ratio between collective cell migration speed and wound healing rate is set by the difference in mechanosensitivity between FAs and AJs in which 1/3 of that of AJs counts. Overall, these results confirm our initial binary models.

      (6) It is unclear how a lack of vinculin dimerization at adherences junctions perturbs epithelial migration, but the complete lack of vinculin tail, which can also not dimerize, does not. In other words, how can TL "have no other role in cell migration at confluence than those at FAs as in single cells." Notably, the authors do not include the tailless variation in the schematic model figures. These results should be included and explained.

      We are sorry that we lacked clarity. Here was our reasoning:

      Both the YE and TL mutants are indeed impaired for dimerization but they differ in two ways:

      - YE binds actin and is under tension while TL does not.

      - YE is not impaired for head-tail interaction and not stable while TL is.

      To determine which of these properties affect cell migration, we first compared YE to the other constructs. Just like YE, FL and T12 also bind actin and are under tension, but the migration speeds of FL and T12 cells at confluence can be predicted from their migration speed as single cells, unlike YE. Therefore, tension is unlikely to explain why YE has an effect on migration speed at confluence not predictable from single cell speed. The irrelevance of tension for the scaling of single to collective cell migration speed is also consistent with the fact that TL lacks tension but still obeys the same relationship as FL and T12 between single and collective cell migration speed. Furthermore, FL and T12 also share with TL their stability in adhesions, unlike YE. The instability of YE is then likely to explain its peculiar effect on migration behavior, because this is the only feature that differentiates YE from all the other constructs, TL included. The Boolean models in Fig. 4G and elsewhere are meant to show within a Venn diagram the main molecular conformations and associated interactions of intact vinculin, and their individual and combined consequences at the adhesion and migration level. We have now specified this is the figure legends of the revised manuscript. There is no 1-to-1 mapping of each mutant to one particular conformation of the intact vinculin. Rather, the effects of the mutations on each conformation are specifically indicated in Fig. S2A.

      In support of this model, we have added in the revised manuscript a corresponding quantitative analysis, as mentioned in response to Question 3 and 5. Briefly, we first looked for the optimal linear combination of change in tension and stability that could explain the change in the difference between single and confluent migration speed across vinculin constructs. This step excluded tension as a significant contributor to the speed difference. We then looked for a relationship that was an as simple as a weighted combination of two terms (i.e. with only 1 adjustable parameter) that related the changes in speed difference to those in stability only, and found the power law dependence on stability. These results, which confirm our initial analysis, are shown in Fig. S4F. Notably, they show that 1) none of the constructs have an effect on the speed difference between single and confluent cells through tension, and 2) the changes in stability across TL, FL and T12 have a minimal impact on this difference, only that between YE and the others has an impact, as highlighted by the small exponent of the power law. Overall, this is consistent with a model whereby the migration speed of cells at confluence is largely predictable from their migration speed as individuals for WT, FL, TL and T12 (Fig. S4C), with an effect of the mutants TL and T12 similar to that of the unmutated FL. The most parsimonious explanation is that the effects of those constructs on cell speed at confluence are explained by the same mechanisms as their effects on cell speed in single cells, that is, through their FAs, and that the effects of TL and T12 through AJs are not much different from that of FL, meaning that the mutations have no other role in cell migration speed at confluence than those at FAs as in single cells. We have slightly modified this sentence as above in the text to specify that the lack of effect of these mutations on migration is on migration speed specifically, not that they have no effect whatsoever.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      In general, I would suggest that you properly define all notions that you use. Notably, you should explicitly introduce basic concepts like the Furth model, Lévy flight, fractional Brownian motion, the shape index, and others. It gives you the possibility to introduce your notation. For the readers, it would make your manuscript more accessible as they would not need to look up these notions elsewhere. The following points and questions are not exhaustive, but might serve as a guide to improve your write-up.

      We thank the reviewer for this suggestion, we have modified the text in the main manuscript to explain the notions in plain English and have added references to the Material and Methods for the more formal definitions, mathematical formulations and additional explanations whenever appropriate. All the modifications are highlighted in the revised manuscript. We hope this revised version will make our manuscript clearer.

      You should give the parameter values for all fits that you provide. Table S1 should give them, if I understand correctly, but in the version I have, this table only provides p-values.

      We have now added the fit parameters in Table S1 in the revised version. They are also displayed in Fig. S2D and discussed in the associated text.

      Why is vinculin or FA stability related to the immobile fraction in FRAP experiments? I would suggest speaking about vinculin or FA lifetimes as measured by the characteristic recovery time obtained from FRAP. How do you interpret the immobile fraction? Do you think that there is an FA ’core’ that persists until the FA is dissolved? In that case, the immobile fraction would report on the relative core size of the FA.

      We indeed consider that this is the amount of protein that remains the longer that is the most relevant to assess the molecular stability of adhesions and its impact on migration, because an adhesion must disassemble entirely to allow cell displacement away from that site.

      In Figure 1B, the fits of the exponents are not very convincing, and they extend over as they cover hardly one order of magnitude.

      We are sorry that figure was misleading. The extreme slopes of 2 and 1 were not meant to indicate the actual time windows where ballistic and pure diffusion would actually be observed but just the values toward which experimental data would tend at short and long lag times, respectively, for a persistent random walk. We hope the new version of the figure in the revised manuscript will clarify this. Additionally, while the range indeed appears short, it is largely sufficient to discriminate between persistent random walk and pure or anomalous diffusion based on the Akaike Information criterion, which is the quantitative and objective metric we exclusively use throughout this work to discriminate between migration behaviors. The scores range from 0 (pure or anomalous diffusion) to 1 (persistent random walk) and table S1 shows that Fig. 1B (among others) is unambiguously a persistent random walk, even within this limited fitting range.

      Figure 2B, D, what do the stars indicate?

      Stars indicate p-values. We now explain this in the figure legends in the revised version of the manuscript.

      Please explain how the FRET index is related to stress?

      We are sorry that we had overlooked this important explanation. We have now added explanations in the main text and in the Material and Methods. Figures now also include the direction along which the tension increases when FRET changes.

      "This shows that impaired head-tail interaction, regardless of tension, is sufficient for vinculin stability." Sorry, but I do not understand what you mean.

      We are sorry that we lacked clarity. We have modified this sentence as follows in the revised manuscript: “This shows that impaired head-tail interaction, whether associated with impaired actin-binding (TL) or increased tension (T12), is sufficient for vinculin stability with FAs.”

      I would avoid the term angular memory. You might use a correlation time, that is, fit the curve to an exponential and take the corresponding characteristic time as a measure for persistence.

      We thank the reviewer for this suggestion. The reason why we introduced this metric was not to extract a persistence time, which we already obtained from the MSD, but to provide compelling evidence that the super-diffusive behavior at confluence arises from a fractional Brownian motion, rather than from another type of super-diffusive walk. We now provide in the revised manuscript a more detailed explanation of this metric, why we prefer it to the more conventional velocity auto-correlation function for our purpose, along with its formal mathematical definition, as explained below. The angular memory is a modified angular correlation in which we consider the angular deviation θ of each elementary step of duration 10min from its immediate previous step of duration τ equal to the lag time ∆t. Specifically, the angular memory M<sub>i,t</sub>(∆t) of a cell i at time t is the cosine of the angle θ<sub>i,t</sub> between consecutive step vectors between times t−∆t and t and between times t and t+10min, such that the step duration τ of the first vector and lag time ∆t before the next are equal. M<sub>i,t</sub>(∆t) = cosθ<sub>i,t</sub>(∆t) = cos. This metric measures the duration of the past that the cell considers when deciding on its direction. It decays to 0 when ∆t → ∞ for persistent random walkers and remains constant for fractional Brownian motion, similarly to the auto-covariance function of fractional Brownian motion C(∆t/τ) = ((∆t/τ +1)<sup>𝛼</sup> +|∆t/τ −1|<sup>𝛼</sup> −2(∆t/τ)<sup>𝛼</sup>)/2, which is a constant C \= 2<sup>𝛼-1</sup>−1 for all ∆t \= τ, as in our definition of angular memory (while also decaying to 0 when ∆t/τ → ∞) (Metzler et al. 2025). Ballistic motion yields 1 whatever ∆t and uncorrelated random walks, whether anomalous or not, yield 0. For this reason, and because M<sub>i,t</sub>(∆t) was found more robust to noise than C(∆t/τ), we considered this metric a more compelling discriminant between fractional Brownian motion and other uncorrelated super-diffusive walks. Consistently, we found that the angular memory of single cells decayed to 0 while that of confluent cells did not and remained nearly constant within our experimental time frame.

      (Of Note, we have increased the analysed data set in the revised Fig. 1D, 3D,F for the sake of representativeness. The conclusions are unchanged).

      "While cells adopt a superdiffusive behavior at confluence, they do so in any possible direction." Sorry, but I do not understand what you mean.

      We are sorry we were not clear. We changed the sentence as follows : “While cells adopt a super-diffusive behavior at confluence, they do so in the absence of any external guidance cue, and as a consequence without any preferred direction.”

      Reviewer #3 (Recommendations for the authors):

      (1) The authors have chosen to use an overexpression system. That means that wild-type vinculin is competing with the mutant vinculin in many cases. Also, the authors have chosen not to study a phospho-deficient form of vinculin or manipulate vinculin dimerization in any other way. Given that these are not the most rigorous experiment set-ups and designs possible, the authors may wish to lessen the strength of some of their conclusions.

      This is correct. We have added in the discussion the following sentence to account for the possible contribution of consequences of the YE mutation other than dimerization impairment, and for the presence of the endogenous vinculin:

      “Whether vinculin dimerization, or another unknown independent function disabled by the YE mutation or phosphorylation of Y1065, is specifically involved in the adhesion and migration phenotypes described above may be addressed in future studies. Likewise, whether the effects are stronger in the absence of endogenous vinculin may be addressed in a null background.” Additionally, we have modified the text throughout to change "dimerization" into "the ability to dimerize".

      (2) Dominant effects have been shown for T12 and VinTL; however, to this reviewer’s knowledge, dominant effects have not been shown for vinculin Y1065E.

      This is correct, we now specify it in the revised version.

      (3) This statement: "Overall, this is consistent with the idea that vinculin acts primarily as a migration moderator, and this supports that insertion of the sensor module weakens to some extent the auto-inhibition of vinculin, thereby contributing to the dominance of all exogenous constructs over endogenous vinculin, in addition to the effects of their mutations" lacks experimental support. Multiple studies have shown that the effects of the insertion of the tension-sensitive module are small on vinculin, including demonstrations that FRAP recovery is unaltered. To make this statement, the authors should perform comparisons of vinculin and vinculin mutants with and without a tension sensor. If differences are observed, it seems that experiments in the manuscript should be repeated with vinculin mutants not harboring a tension sensor. If the presence of the sensor affects mutant behavior, then it seems unlikely that the claims of the paper are correct. For instance, it would suggest that vinculin dimerization is not the sole driver of the velocity coupling, instead it could be a combination of partial activation and lack of dimerization. Alternatively, the authors could remove or edit this sentence.

      We agree that the second part of our statement was incorrect and have removed it. We cannot say that the insertion of the sensor module weakens the auto-inhibition and we agree that there is no difference in turnover compared to a vinculin construct without the sensor.

      (4) Vinculin dimerization is drawn incorrectly in many of the schematic figures summarizing results. Vinculin dimerization is dependent on F-actin binding (see work of Sharon Campbell and others). Vinculin is unlikely to form a "dimer" in solution, as shown in these schematics. Also, vinculin dimers are thought to form along the length of two bundled actin filaments, not at the end, as drawn in the schematics.

      We thank the reviewer for these suggestions. Sharon Campbell and others have indeed shown that actin binding promotes the dimerization of vinculin tails in solution. They and others have shown, however, that vinculin tails also form dimers in the absence of actin, albeit at higher concentrations, which are equivalent to at least 0.1 molecule per 100nm<sup>2</sup> in any 2D section of the volume (DOI: 10.1074/jbc.M111.244293, 10.1021/bi801764a). The density of vinculin within adhesions is promoted by the multiple neighboring vinculin-binding sites on its partners (such as talin, in which the neighboring binding sites are occupied nearly all at once upon talin stretch, doi:10.1021/acs.nanolett.6b00650, 10.1039/c5ib00307e), and is likely to reach a molecule per 100nm<sup>2</sup> in order to accommodate the traction forces that cells exert on their substrates (doi: 10.1021/acs.nanolett.6b04364). This exceeds the threshold concentration for vinculin dimerization in the absence of actin by at least an order of magnitude, and is therefore likely to offer another route for vinculin dimerization in addition to actin binding. We conclude that vinculin density in adhesions is very likely to allow dimerization in the absence of actin, and the binding to actin additionally promotes dimerization. Due to the omnipresence of actin in adhesions, the dimer unbound to actin certainly accounts for a small fraction of possible vinculin conformations, but this is likely to be very context-dependent and current knowledge is too limited to be more quantitative. We have therefore decided to keep our model simple with all these possible conformations, without indications of their possible proportions.

      We agree that the drawing of the interaction with actin does not properly depict the side-binding of actin and we have modified it in the revised version. Nevertheless, vinculin and actin are known to bind by both their sides and ends (DOI: 10.1074/jbc.M110.102830).

      (5) Technically, the authors have not shown that conservation of angular momentum is "infinite". It just appears longer than the experimentally accessible terms. The use of term short-lived and long-lived, instead of finite and infinite, might be more appropriate.

      We agree, we have changed “virtually infinite” to “long-term” everywhere in the text to avoid confusion.

      (6) The conclusions of the manuscript seem to treat vinculin loading and vinculin stability as independently regulated. However, vinculin has been shown to act as a catch, both in vitro (see work of Alex Dunn) and in living cells (see work of Sharon Campbell), suggesting strong coupling of these quantities. A discussion of the points would benefit the manuscript.

      We agree that vinculin loading and stability in adhesions depend on each other and thank the reviewer for suggesting these additional references. We formulate our model as follows: “Mechanistically, our results support that the head-tail interaction of vinculin challenges both force transmission and stability of vinculin in FAs, as has been observed in other cell types (Carisey et al. 2013, Humphries et al. 2007, Cohen et al. 2006, Dumbauld et al. 2013, Liu et al. 2016, Omachi et al. 2017)...” This shared dependence and factors that independently affect force transmission or stability, but indirectly feed back to each other, are not mutually exclusive, as we state next: “... and is countered by the actin-vinculin tail interaction, which provides force transmission but is unnecessary for stability, and the ability of the tail to dimerize, which associates with higher stability and is dispensable for force transmission (Fig. 2D,E).”

      Such feedback implies that the interaction between actin and the tail of vinculin can promote stability, even though it is not necessary for this (as shown with TL), and that the ability of the tail of vinculin to dimerize can promote force transmission, even though it is not necessary for this (as shown with YE). We have added the following sentence in the revised version to clarify this point:

      “As a result of this feedback, stability and force transmission can be further promoted by the interaction of the vinculin tail with actin and its ability to dimerize, respectively, indirectly through their antagonism with the head-tail interaction of vinculin.” Consequently, this opens the possibility that a catch-bond between vinculin and actin also promotes vinculin stability in adhesions, which is indeed shown by the Campbell lab (doi:10.1038/s41467-023-43779-x), thanks to a prolonged antagonism with the head-tail interaction. Interestingly, their results show that the ability to form a catch bond does not appear to oppose the head-tail interaction more than actin binding does (their Fig. S10). This suggests that the actin-vinculin catch bond stabilizes vinculin in adhesions through a mechanism that has yet to be identified. In conclusion, vinculin loading and stability in adhesions are interdependent through the head-tail interaction and through another unknown mechanism that involves the catch bond between vinculin tail and actin. We now include a sentence that refers to this catch bond in the revised manuscript.

      (7) Recently, two papers have come out assessing the role of AJs and mechanical coupling during epithelial migration: Noordstra, Dev Cell, 2023, and Shoyer, PNAS, 2023. Comparing the results of this manuscript to those of these publications would strengthen the discussion.

      We thank the reviewer for suggesting these references.

      Noordstra et al provides a very interesting investigation of the mechanisms whereby the mechanosensitive alpha-catenin down-regulates lamellipodial activity in epithelial sheets that form intercellular contacts during wound closure. This could offer a potential mechanism that would explain why we observe that cells at confluence migrate at a lower speed than single cells. While a minimal lamellipodial activity is indeed required for cell migration, we have previously shown, however, that the down-regulation of lamellipodial activity by the formation of AJs does not decrease cell migration speed (doi:10.1073/pnas.1002662107), but the formation of desmosomes does (doi:10.1242/jcs.146316). We have included these considerations in the discussion of the revised manuscript.

      The main finding Shoyer et al is that the phosphomimetic mutant S1033D of vinculin relaxes vinculin tension and reverts it to a close conformation in both AJs and FAs. The mutant affects directed collective cell migration in a manner that preserves the relationship between lateral velocity deviation amplitude and coordination length but consequences on vinculin stability in adhesions, or on single and undirected collective migration are unknown. Thus, it would be worth assessing them to determine whether this mutant affects cell migration through FAs, AJs or both, and how it fits in our model. We have now included this reference in the discussion of our revised manuscript.


      [Editors' note: The authors included an author response to reviews from another journal]

      Reviewer #1 (Comments to the Authors):

      In this manuscript the authors describe that cells in collective movements adopt a superdiffusive behavior to out pace individual cells. This behavior is regulated by cell-cell junctional stability and force transmission. The authors state that speed is regulated by vinculin through mechanosensitivity.

      While is makes intuitive sense that cells may move more efficiently collectively as it reduces their exploratory space and therefore increases their efficiency of movement,

      We agree that this is an intuitive explanation. However, previous literature had shown that confluent cells may or may not migrate depending on conditions that do not solely depend on the space available per cell, but also involve the intrinsic activity of the cell, its cortical tension, and its adhesion with its neighbors, with sometimes counterintuitive effects (doi: 10.1016/J.CEB.2021.07.011). This was the reason that motivated us to investigate how these various ingredients affected space exploration efficiency on different time scales.

      Our results indeed refute the intuition that cells move more efficiently when their exploratory space is reduced by showing that the outcome depends on the time scale considered (Fig. S3B). Specifically, on short time scales (less than 3 hours), the area explored by individual MDCK cells is larger than that explored by MDCK cells at confluence. On a longer time scale (greater than 3 hours), however, the area explored by confluent MDCK cells is larger. This switch is a direct consequence of the change in migratory behavior from persistent random walk to superdiffusion, Moreover, its position in time depends on the cell line: extrapolation of our results on RPE-1 cells suggests that it should theoretically occur after approximately 300hrs, if this time scale was experimentally accessible (Fig. S3F).

      …the role of junctions specifically is less clear.

      We are sorry that we were not able to clearly convey the roles of junctions. We have substantially rewritten our text to address this and all the changes are highlighted in orange. As summarized in Fig. 6F, junctions have three roles. The first role is on persistence, through velocity coordination between neighbors, the second is on speed, through the stability of junctions, and the third role is on directionality, through the sensitivity of the monolayer to the wound edge.

      The first role is evidenced thanks to the comparison of the MSD between single cell and confluent migration assays and the use of the alpha-catenin KD cell line. Alpha-catenin depletion is known to be the most potent disruptor of adherens junctions (DOI:10.1091/mbc.e06-05-0471, , DOI:10.1126/science.aaf7119, (DOI:10.1073/pnas.1002662107, DOI:10.1073/pnas.1119313109), and we show that it significantly alters the superdiffusive behavior that emerges in the confluent migration assay (Fig. 3E,F, 5C). Therefore, junction integrity is critical for the control of cell persistence.

      Moreover, alpha-catenin depletion induces a loss of velocity coordination between neighbors (Fig. S3E), which we show through numerical simulations to induce superdiffusion (Fig. 3G). By contrast, E-cadherin KO and vinculin mutants have no effect on the superdiffusion of confluent cells (Fig. 3E, 4A). Therefore, the critical molecular ingredient is the link provided by alpha-catenin to the cytoskeleton that provides junction integrity.

      The second role of junctions is evidenced thanks to the comparison of cell speeds between single and confluent migration assays with the vinculin mutants (Fig. S4A). Results show that cell speed is reduced of about 10µm/h by confluence, regardless of the mutant except for YE, whose only difference with other mutants is its lower stability (Fig. 4F). This supports that junction stability, and not the other effects of mutants, controls cell speed (we provide a detailed demonstration in the response to the following question). As expected, junction integrity is required as well, as seen from the higher cell speed of the alpha-catenin KD cell line compared to WT (first MSD point in Fig. 3B, E).

      The third role of junctions is evidenced thanks to the comparison between confluent and directed migration assays (Fig. 6A). Results show that the wound healing rate is proportional to cell speed at confluence, regardless of the mutant except for YE, which displays no tension gradient in junctions from front to back cells (Fig. 6C). This supports that such gradient is required for cells to identify on which side is the wound edge. As expected, junction integrity is required as well, as seen from the loss of directional bias of the alpha-catenin KD cell line (Fig. 5F).

      The authors chose vinculin as the basis by which to manipulate tensions at cell-cell junctions, but this comes with considerable drawbacks. Namely, since vinculin appears at both cell-cell and cell-matrix junctions, its role and the role of its mutations is not clear here. The authors state that the collective migration speed is related to junctional stability, but because vinculin is also at FA, how can this be concluded?

      We apologize for the lack of clarity. We hope that the highlighted changes in the revised manuscript will improve this point. As exemplified above, comparing cell migration between isolated cells and confluent cells is essential to enable us to distinguish between the contributions of AJs and FAs. Indeed, since isolated cells lack AJs, the impact of vinculin mutants on single cell migration can only be explained by their effects on FAs. This is how we first determine the effects of vinculin mutants on migration that depend on FAs. Because confluent cells also have FAs, we expect that the effects of vinculin mutants on the migration of isolated cells will still be present in confluent cells, to which will be added the effects of these mutants on AJs and their consequences on migration, if any.

      Therefore, when compared to WT cells, if a given mutant decreases or increases migration speed in individual cells, and does so in confluent cells in the same proportion, then its effects at confluence can be entirely explained by its effects in individual cells, and there are no additional effects of that mutant from AJs. This is indeed what we observe for all mutants except the YE mutant (Fig. S4C), leading us to conclude that none of the vinculin mutants, except the YE mutant, have an effect on migration at confluence that results from AJs. In contrast, the YE mutant has effects on migration at confluence that cannot be explained by its effect on individual cell migration. Therefore, the effects of YE at confluence depend on AJs, whether they result from alterations in AJs, FAs, or both. To distinguish between these scenarios, we proceed by elimination, comparing the effects of YE to those of other mutants on force transmission and adhesion stability, and how these two factors associate with migration speed, as explained below. In FAs, YE alters force transmission differently in individual cells and at confluence, but we already know from Fig. 2 that force transmission in FAs cannot alone explain the speed of migration. This result rules out an indirect effect of AJs on cell migration at confluence through FAs. Furthermore, in AJs, YE affects stability and force transmission, but TL has the same effect on force transmission as YE and we already know that none of the effects of TL on migration depend on AJs (Fig. 3, S4C). This result rules out an effect of force transmission in AJs on migration speed at confluence. We conclude that stability at the AJ level, which is the remaining property specifically impaired by YE, is what regulates migration speed at confluence.

      The manuscript's logic and flow are not clear in some places, making the story hard to follow. As one example, the FRAP data, which the authors suggest is used to investigate vinculin's combined role does not help in this capacity as the interpretation and its connection to the bigger story are not clear.

      We are sorry again for the lack of clarity. We used FRAP data to evaluate the effects of vinculin mutants on adhesion stability. Indeed, mutants have different effects on adhesion stability (Fig. 2E, 4F). In addition, they also have different effects on force transmission (Fig. 2D, 4D,E). The partial overlap in functional alterations caused by the mutants allows us to test the involvement of the overlapping function (here stability) in the overall migration outcome. For example, if two mutants have a similar effect on adhesion stability but different effects on migration speed (such as TL and T12), we can then rule out that speed results from adhesion stability. Similarly, if two mutants have different effects on stability but a similar effect on speed (such as TL and YE), we can also rule out that speed results from stability. We applied the same reasoning to force transmission to conclude that neither adhesion stability nor force transmission alone is sufficient for cells to migrate rapidly. However, the combination of the two enables rapid migration.

      As another example, the information derived from the use of the mutants is not clear in the context of the message in the manuscript since they affect cell-cell and cell-matrix junctions and in some places show results that are counter intuitive and not well-explained, to which the authors admit they are surprising but then do not explain their meaning.

      As such, it is very hard to follow the logic with regard to the information resulting from the mutant experiments.

      We provide above a detailed break-down of our strategy to analyze the results. We regret that our manuscript did not adequately convey our conclusions and we hope that the new version of the manuscript improves this point.

      Proliferation has been shown to play a role in wound healing. Does proliferation change in the various conditions?

      This is an important point. The average speed of cells at confluence is approximately 20 µm/h (Fig. 4B), which means that each cell moves approximately its own size in one hour. During this time, assuming a 16-hour cell cycle, 6% of the cells would have divided, each of them likely pushing one of its neighbors a distance equivalent to the size of a cell. Therefore, cell proliferation accounts for at most a few percent of the total cell movement. For this reason, we can assume that growth does not account for a large part of the movement we observe. This is consistent with previous work showing that proliferation does not contribute significantly to wound healing (DOI: 10.1073/pnas.0705062104, DOI: 10.1083/jcb.201207148).

      Minor comments:

      The authors should provide a better description of the mutants: what does a tailless mutant not bind, or bind differently? More context is needed to help interpret the results. While the mutants have all been published on before, it would be helpful to have more information here so that the manuscript is easier to follow.

      We are sorry that the information we provided was insufficient. We have now detailed the mutations to help the reader understand how interactions are altered.

      Figure 1A is not necessary. Figure 1 overall is fairly predictable as there have been many papers using the persistent random walk as the best model to single cell migration (dating back to the early 1990's). The authors define a new term, angular memory, which they show decreases with increasing delta t as one would predict.

      We acknowledge that persistent random walks have already been observed for individual cells, as in references 3-4 cited in the introduction. Nevertheless, we believe that Figure 1 is important because not all cells migrate as persistent random walkers when isolated. Some migrate in a more exotic manner, resulting in superdiffusive behavior, as in references 5-8 cited in the introduction. Since we observe superdiffusive behavior at confluence (Figure 2), it was therefore necessary to show whether or not single cells were superdiffusive too. We also use this figure to introduce angular memory, a measure that, to our knowledge, has never been used before. According to intuition, it decreases to 0 for persistent random walkers, just as another resembling measure, velocity autocorrelation, would do. However, the angular memory of fractional Brownian walkers does not vanish with increasing delta t (Fig. 3D), while velocity correlation would, just as that of persistent random walkers. This difference makes angular memory much more appropriate for distinguishing between the two migration behaviors, and prompted us to introduce it in the first figure as a reference.

      In the wound healing assay, which cells were measured? Leading edge or interior, and does it matter?

      Figure 5A shows that cells behave differently depending on their distance from the wound. This is because the traces shown correspond to the first few hours of the movie, during which the cells at the front begin to move first. Figure S5A shows the speed of the cells over time after the wound and indicates that the cells reach a stable speed after approximately 3 to 4 hours. Figure S5B shows the speed of the cells as a function of distance from the wound at steady state. These results show that the speed of the cells no longer depends on the distance from the wound at this stage. As indicated in the “Materials and Methods” section, we only considered time points beyond this stage for subsequent analyses of population-averaged MSD and velocity presented in Figure 5, so the location of cells at the front or rear was irrelevant.

      Reviewer #2 (Comments to the Authors):

      To migrate cells must spatially explore their environments, a process that is guided by intrinsic signals (adhesive and mechanical properties, etc) and extrinsic (gradient cues) signals. This exploration can occur on the single or multicellular level. In this study, the authors examine the effect of cell-cell interactions, guidance cues, and cell mechanics in the exploratory capacity of MDCK cells. The authors show that cell-cell adhesion provides a "infinite directional memory for migration" and cell speed is dependent upon the focal adhesion stability, cell mechanics, and the mobility of adherens junctions-these processes are modulated by vinculin.

      My three major concerns with the manuscript are as follows:

      (1) While there is potential new information about the role cell-cell junctions and guidance cues play in cell migration, there is not enough NEW insight presented. Rather the role of vinculin in these processes is expected given what is already known about its ability to control focal adhesion stability, mechanics, and adherens junctions.

      We agree that our cell migration results make sense based on the effects of vinculin mutants on the stability and force transmission of adhesions. Nevertheless, we argue that this was not the only possible scenario. Indeed, we find that none of the effects of vinculin mutants on AJs (except YE) have an impact on cell migration (Fig. S4C). One might have expected that the increased stability provided by the TL and T12 mutants would reduce the speed of collective cell migration, just as the YE mutant increased cell speed due to its altered stability. This is not what we found, and this reveals a nonlinear relationship between AJ stability and migration speed that could be investigated more thoroughly in future studies. Another example is that the effects of the mutants on force transmission in AJs do not impact migration speed at confluence but do impact directed collective migration (Fig. 6). One might have expected that vinculin-mediated force transmission in AJs would impact collective migration, whether directed or not.

      More importantly, we show that the role of intercellular adhesion in cell migration is more complex than expected. Indeed, it depends on the timescale considered: intercellular adhesion is detrimental to short-term spatial exploration and beneficial in the long term (Fig. S3B). Such a timescale-dependent behavior is impossible to predict from previously known effects of the mutants or other molecular considerations. Furthermore, we show that this behavior can be fully explained by the coordination of velocities between neighbors, which depends on intact connections between AJs and the cytoskeleton via alpha-catenin, but is independent of vinculin mutants that connect AJs to the cytoskeleton in parallel with alpha-catenin. One might have expected these connections to also have an impact on velocity coordination, and thus on spatial exploration, but we show that this is not the case (Fig. 3). Finally, we show that directed collective migration has a negligible impact on cell exploration at our experimental timescale (Fig. 5), whereas we initially expected the wound to make migration more ballistic. This reveals that such a directional signal affects spatial exploration at much longer timescales than expected.

      Overall, our results quantify the outcome of competing effects and provide timescales at which one effect outweighs the other in influencing cell migration. We believe this is an original approach that provides substantial new insights into collective cell migration.

      (2) The phenotypes of the cells expressing the mutant vinculins varying greatly. These phenotypes are not addressed despite the fact that they could potentially complicate the analyses. For example, there are dramatic differences between focal adhesion numbers and sizes in the cells expressing the different vinculin mutants; cell spreading is also dramatically altered. Likewise, the T12 mutant vinculin has previously been reported to have increased adhesive strength, increased traction forces, and cell spreading. How does this knowledge change the interpretation?

      We agree that vinculin mutants may have effects on the size and number of FAs, cell spreading, and traction forces that we do not examine here. These consequences can be explained by the effects of these mutants on force transmission in FAs and on their stability, which we report in our work. They do not affect our interpretations. Here, we provide a predictive model of migration speed based on the combination of two consequences of vinculin function, namely stability and force transmission. An interesting avenue for future research would be to assess whether these combinations can be reduced to a single higherlevel effect of vinculin on the cellular phenotype that would be sufficient to predict migration speed. This work remains to be done, as neither FA size and number, cell spreading, adhesion force, nor traction forces alone are sufficient to predict migration speed.

      Along the same lines, it has previously been established that tagged version of vinculin do not efficiently integrate into adherens junctions. Published work from the Nelson laboratory suggests that GFP-vinculins do not localize to cell-cell junctions and work from other laboratories suggests localization occurs only when the endogenous vinculin is silenced.

      We are aware that some GFP-vinculin constructs may not localize as well as the endogenous protein at AJs. This is due to the localization of the GFP tag on the head of vinculin and depends on the length of the linker between GFP and the head of vinculin. The longer the linker, the easier the interaction with AJ partners. Unlike these constructs, the vinculinTSMod sensors we use in our work do not carry a GFP on the head and do not suffer from the same limitations.

      Furthermore, vinculin recruitment to AJs depends on force, with little or no recruitment when tension on the AJs is relaxed (DOI: 10.1038/ncb2055). Vinculin recruitment has in fact already been used as an indicator of AJ tension in Drosophila (DOI: 10.1038/s41467-01807448-8). Consequently, the amount of vinculin visible at the AJs varies depending on the tension exerted on the AJs, which our results confirm: vinculin is more difficult to detect at the AJs in cells located at the front of a wound than in those located at the back (Fig. 6B), which is consistent with the difference in vinculin tension between front and back cells (Fig. 6C) and to the E-cadherin tension gradient between front and back cells (DOI: 10.1083/jcb.201706013). Overall, these results show that vinculin is not always easy to detect at AJs, but this is due to the properties of vinculin, which the constructs we use reproduce better than previous constructs (see also below).

      The images in figure S2 and the prebleach images in figure S4 do not show convincing localization of the mutant vinculins to cell-cell adhesions. This is of special concern given that YE mutant protein hardly has any discernable localization to cell-cell junctions; additionally, none of the mutant proteins were tested for their ability to co-localize with adherens junction components. This raises the question if the parameters being examined and the conclusions drawn from them are affected by a difference in localization.

      We agree that the recruitment of vinculin at intercellular contacts may be difficult to see.

      Besides force-dependent effects mentioned above, other factors are involved. The images shown in Figures S2 and S4 are from live cells in which cytoplasmic vinculin is still present, and its level proportional to the mobility of vinculin. Indeed, the TL and T12 mutants show a more marked contrast between intercellular contacts and the cytoplasm, which is consistent with their greater stability at AJs (Fig. 4F). Conversely, YE shows lower contrast, which is consistent with the lower stability of this construct at AJs (Fig. 4F). The FL construct lies between the two. As a result, the cytoplasmic content can variably mask vinculin recruitment at the AJs depending on the mutant.

      We have now performed additional quantifications of mutant recruitment at intercellular contacts as a function of distance from the basal surface of the cells and relative to their recruitment in FAs, in live cells. Results are shown in the new Fig. S4F. We find that all the constructs are recruited to intercellular contacts with a density that is at most half of that in FAs and that varies along the height. FL shows the highest density, localized more apically, consistent with the localization of an AJ-bound actin belt. The mutants appear to be more homogenously distributed along the height of the lateral surface, which may be explained by their impaired autoinhibition (TL, T12), or mechanosensitivity (YE). This variability also contributes to the difficulty in seeing vinculin recruitment in all cells in a single z-slice.

      To confirm the proper recruitment of vinculin constructs to AJs we have performed immunofluorescence against alpha-catenin and phalloidin on each of the stable cell lines. Results are shown in the new Fig. S4D and E. In these experiments, cell permeabilization allows for the release of some of the cytoplasmic pool of vinculin, which highlights the recruitment of all vinculin constructs to intercellular contacts. There, all vinculin constructs colocalize with alpha-catenin and F-actin, as expected. Additionally, images displayed are maximum intensity projections to mitigate recruitment variability along the height.

      Overall, our results clearly support the localization of vinculin at intercellular contacts, and the differences between the constructs are consistent with the effects of their mutations.

      (3) There is a lack of new mechanistic insight. Conclusions are made about a role of vinculin dimerization. This conclusion appears to be based upon the usage of the mutant version of vinculin Y1065. Did the authors directly measure the ability of this mutant protein to dimerize? Is actin binding also affected.

      The binding properties of the Y1065E mutant, including its dimerization and binding to actin, have already been characterized by other researchers (ref. 40 in our manuscript, as well as DOI:10.1111/j.1432-1033. 1997.01136.x or DOI: 10.1016/j.febslet.2013.02.042). We assumed that these properties are now well established and can be used to explain higher-level phenotypes that we show for the first time, to our knowledge.

      Reviewer #3 (Comments to the Authors (Required)):

      Canever et al. tracked two epithelial cell lines on collagen coated glass and showed that isolated cells (non confluent) move as persistent random walkers, whereas confluent monolayers migrate super diffusive, with long range directional memory. By systematically perturbing adhesion machinery they found that focal adhesion mutations mainly tune the speed of single cell tracks, but cannot create long range memory, while force bearing adherens junctions are essential for the super diffusive regime-genetically perturbing them collapses collective memory. These interesting results identify junctional tension as important to switch epithelial cells/sheets between individual and collective search modes - an important quantitative insight that is of clear relevance to cell biologists.

      - The presented data is nicely quantitative and convincing, but I have subtle concerns about the generality of the findings. While the authors show that the differential behavior, they describe is not cell-line specific (MDCK, RPE), there are no experiments evaluating the generality of their conclusions across different matrix conditions. How are the measured migration parameters affected by matrix stiffness? Cell migration on collagen coated glass coverslips is a relatively narrow and artificial condition. How is the collective directional memory expected to behave on softer substrates? The generality of the conclusions could be strengthened by repeating measurements using hydrogels of varying stiff-ness. Further, it should be discussed to which tissues in the body the selected matrix conditions and migration modes plausibly apply.

      We agree that the generality of our results and the relevance of glass-rigid substrates is an important point. In vivo, epithelial cells rest on a basement membrane with a typical stiffness of approximately 10 MPa, as demonstrated by experimental evaluations on various tissue explants, including renal glomeruli and Bruch's membrane, which are relevant to MDCK and RPE-1 cells (DOI: 10.1111/j.1742-4658.2007.05823.x, DOI: 10.1172/JCI106898, DOI:10.1038/eye.1987.35), we have added these references in the manuscript to support our experimental strategy. In vitro, the most significant effects of substrate stiffness on FAs and cell migration generally occur at much lower stiffnesses, between 0.2 and 100 kPa, and cell phenotypes generally plateau at levels comparable to those observed on glass, even below 100 kPa (DOI: 10.1242/jcs.133645, DOI: 10.1038/ncb3268, DOI:10.1039/c5ib00307e, DOI: 10.1039/c9sm01893j). Furthermore, substrate stiffness has much more moderate effects on confluent cells than on isolated cells. For example, it has been previously demonstrated that confluent layers of MCF10A epithelium showed no change in velocity coordination in the range of 3 to 65 kPa (DOI: 10.1083/jcb.201207148). Therefore, collagen-coated glass appears to be a reasonable model for the basement membrane. Overall, we believe that we have conducted our experiments under physiological conditions, and that our results apply to a wide range of substrate stiffnesses.

      - It would be nice to see how long it takes confluent cell layers to close rectangular wounds of defined size when cells migrate as individual (adherens junctions perturbation) versus collective (wt) (on substrates of different stiffness). Presumably, there should be faster wound closure under the collective regime, at least for simple shaped wounds.

      This is an interesting question, which our results indirectly address. In our study, we measured the wound healing speed of the WT MDCK cell line as well as lines expressing mutant vinculin constructs (Fig. 6A). These results show that this speed ranges from 5 to 15 µm/h depending on the construct expressed (and for reasons that we explain in the manuscript). These values make it easy to estimate the time required to close a wound based on its width. For example, it would take 5 hours to close a 100 µm wide wound for the WT cell line, which has a rate of 10 µm/h (on both sides of the wound).

      Wound closure for cells with disrupted adhesive junctions has already been documented (DOI: 10.1083/jcb.200910041). The results show that wound closure is indeed slower than with WT cells. Although this previous study does not reveal the underlying causes, our work now shows that there are two factors: weaker directional memory due to impaired intercellular coordination and, in the longer term, an additional lack of sensitivity to the guidance signal provided by the wound.

      - Akin to substrate stiffness variation, I am missing experiments that test the effect of cytoskeletal tension on these migration modes. Experiments with Rho kinase or myosin inhibitors could meaningfully broaden the scope of this study.

      Rho kinase or myosin inhibitors applied to cells during the time required to assess migration patterns (a movie recorded overnight is necessary to obtain a statistically reliable calculation of MSD over 3 to 4 hours) are likely to affect many other cellular processes in addition to the cytoskeletal tension directly involved in migration. We believe that the accumulation of these effects will make interpretation of the results very difficult. For example, it has been shown that inhibition of ROCK by Y27 promotes healing of corneal endothelial lesions by affecting proliferation through cyclin D and p27 (DOI: 10.1167/iovs.13-12225), or by improving respiration, which would provide the energy necessary for migration (DOI: 10.1096/fj.202101442RR). Consistently, another study on HaCaT epidermal cells confirms that myosin phosphatase accelerates wound healing through proliferation (DOI: 10.1016/j.bbadis.2018.07.013). In contrast, in HUVEC cells, ROCK inhibition significantly impaired the proliferation and migration of vascular endothelial cells in vitro in a dose-dependent manner (DOI: 10.1097/ICO.0000000000000493).

      Furthermore, previous studies have highlighted that differential contractility at the subcellular level is important for collective migration (DOI: 10.1038/ncb2133, DOI: 10.1083/jcb.201706013), which is not possible to examine with global activation or inhibition of contractility. This prompts the development of more refined and specific measurement and disruption strategies to assess the respective impact of cytoskeletal tension on cell-cell and cell-matrix adhesion mechanisms. Our work, which uses biosensors to assess how this tension differentially affects cell-cell and cell-matrix adhesions, is a step in this direction. The localized spatio-temporal activation or inhibition of myosin subtypes or Rho GTPase regulators specific to these adhesion structures will likely answer these questions in the future, but we believe that the development and application of these approaches will require a substantial amount of work that goes beyond the scope of our study.

    1. Author response:

      The following is the authors’ response to the previous reviews

      Public Reviews:

      Reviewer #2 (Public review):

      Summary:

      The authors set out to investigate how well the onset of a self-initiated movement could be predicted at different times prior to action onset. To do so, they collected EEG and MEG data across 15 human participants who watched natural landscape images on a screen. These participants performed active self-initiated movements, or observed passive actions, to have a new image appear. By comparing the neural activity prior to active and time-matched passive actions, the authors found that even though a build-up of neural activity is visible close to 1s prior to action, action onset could only be reliably predicted around 100ms prior to action. These results confirm what was already suggested in previous literature: the commitment to action is only clear from the late stages in the visible neural ramp-up to action onset.

      Strengths:

      (1) The paper presents a well thought out methodology to assess the predictive value of neural activity prior to a self-initiated movement and passively observed action, while keeping all other experimental factors identical. This methodology can be applied outside the specific scope of this paper as well, in efforts to assess the correspondence of a neural signature with an observed behavior.

      (2) The results are a strong confirmation of what was suggested less clearly in previous research (Trevena & Miller, 2010, Consciousness & Cognition; Schmidt et al., 2016, Neuroscience & Biobehavioral Reviews; Travers et al., 2020, NeuroImage).

      Comments on revised version.

      I thank the authors for addressing my concerns in the Introduction and Discussion of their paper. I don't require any further edits at this point.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      (1) Please more concretely define the parameters of 'early' and 'late' time windows in the manuscript so that the reader can better understand the difference between these with respect to the time-course of effects relative to a motor response.

      Those changes were addressed in the previous round of revisions (please refer to previous round). Namely, we made the following addition:

      “The lower bound of meta-analytic estimates of awareness, at 250 ms before movement onset (Braun et al., 2021), can be used as a pragmatic threshold to classify neural signals as “early” (more than 250 ms before movement onset) or “late” (less than 250 ms before movement onset).”

      (2) Code and data do not appear to be uploaded to the linked OSF repository. We understand that this may typically occur after the reviewed preprint is available via eLife; however, please ensure that this is made publicly available. Because such materials were not available, we were unable to verify some of the method's details and went by what was reported in the preprint.

      We apologize for the oversight, the link to the code was in the description of the OSF data repository that was linked in the data availability statement. We have now updated the data availability statement to directly reflect links to both the data (OSF) and the code (GitHub):

      “Data used in this study are publicly available on the OSF repository: https://osf.io/wm95q/.

      Code used in this study is publicly available on GitHub: https://github.com/lucasjeaybizot/Slideshow2025.”

      (3) For the sentence: 'Proponents of the early-decision account have taken early brain activity, like the RP, to support the thesis that decisions happen early in the brain, taking these early signals to reflect a cascading process that brings about the forthcoming action.' it would be very informative to cite the papers that propose this account, as only the Schurger et al. (2021) paper is cited in this paragraph.

      We have modified the sentence to the following to include the original result (Libet et al., 1983), an influential review that describes this interpretation (Haggard, 2008), and an influential study that applied such interpretation (Fried et al., 2011):

      “Proponents of the early-decision account have taken early brain activity, like the RP, to support the thesis that decisions happen early in the brain, interpreting these early signals to reflect a cascading process that brings about the forthcoming action (Libet et al., 1983; Haggard, 2008; Fried et al., 2011).”

      (4) In Figure 2C, the units are not displayed in the colour bar. These should be included so that the colours can be better interpreted.

      The units have now been added to the figure.

      (5) It is unclear why the time-frequency power estimates (and multiple comparisons procedures) extend to an upper limit of 80 Hz (as displayed in Figure 2C), despite the key signal of interest only spanning 10-30 Hz (Mu/Beta range). Extending the frequency range this high results in a larger number of comparisons and a potentially stricter multiple comparisons correction. Please justify why this larger frequency range was used, given this potential drawback.

      The rationale for extending the time-frequency decomposition to 80 Hz was to characterize the spectral landscape over the same frequency range that was available to the Haar-AdaBoost classifier, whose features extended up to 80 Hz. The purpose of this analysis was therefore not limited to testing the canonical mu/beta ERD range, but also to visualize whether other frequency-specific activity was present in the broader feature space used by the classifier. We have clarified this rationale in the text:

      “We examined this broader frequency range, rather than restricting the analysis to the canonical Mu/Beta bands, to characterize the time-frequency landscape over approximately the same spectral range available to the Haar-AdaBoost classifier, whose frequency-sensitive features extended from 2 to 80 Hz.”

      (6) For the time-frequency analysis, it is stated that 'Here, we used complex Morlet wavelets to decompose our data at C3 into 78 logarithmically spaced frequency bands from 2 Hz to 80 Hz with logarithmically decreasing cycle counts'. Do the authors mean logarithmically increasing in this case? Usually, more cycles are used for higher frequencies to achieve a similar time/frequency precision balance across lower and higher frequency wavelets. Fewer cycles for higher frequencies is highly unusual. This should be corrected if it is an error.

      We thank the reviewer for catching this important error. We indeed used an increasing cycle count. We have modified the text accordingly by changing the description to “increasing”.

      (7) Regarding the sentence: 'We used standard procedures for identifying and interpolating bad channels in the EEG recordings.' Please specify what those procedures are, as they are not necessarily standard across different research groups, and multiple methods exist.

      We have modified the section to better describe the procedures:

      “We manually identified bad channels and interpolated them using a weighted average of the 5 nearest channels.”

      (8) For the ERP analyses of differences between the active and passive conditions, the parameters of the cluster-based permutation test should be specified (e.g., the alpha levels for cluster inclusion and cluster-level statistical significance).

      We have added the following to better characterize the cluster-correction parameters:

      “Samples exceeding a two-sided uncorrected threshold of were grouped into temporal clusters, and the cluster statistic was defined as the sumα of = 𝑡.-05 values within each cluster. Statistical significance was assessed using 1,000 permutations, with clusters considered α =. 05 significant at a cluster-level based on the two-sided permutation distribution.”

      Reviewer #2 (Recommendations for the authors):

      (1) I am curious how the current results would compare to an analysis in which pre-action neural activity is compared to baseline and post-action neural activity. In other words, activity at any point in time during which the person was at rest, rather than an explicit time-matched passive action condition. I would expect that neural activity predictive of an upcoming action or intention will look significantly different from the neural activity in time at any other moment at which the person is not intending to act.

      We agree that comparing pre-action activity with unconstrained resting activity could be informative and would likely reveal differences associated with preparation for action. However, this comparison would address a somewhat different question from the one targeted here. Our goal was to determine whether activity preceding self-initiated movement contains information specific to the forthcoming movement when compared with a temporally matched condition that controls for elapsed time and anticipation of the slide transition. An arbitrary resting baseline would not provide these controls and could therefore introduce differences unrelated to movement commitment. We agree that such an analysis could be useful in future work.

      (2) It would be good to discuss the current results in comparison with those of Trevena & Miller (2010, Consciousness & Cognition).

      We have addressed this comment in the previous round of revision:

      “Previous work showed that these early ramping signals were not specific to the outcome of a motor decision (Trevena & Miller, 2010). However, because their analyses remained time-locked to decision outcomes, they could not directly test whether the observed slow buildup specifically reflected a commitment-like process.”

      (3) The order of reporting throughout the paper is somewhat confusing, as many results are provided before the "Results" section. For example, there is repetition in the "A new approach to self-initiated movement analysis" section, compared to the "Results" section. The argument for why event-locked potentials are not necessarily predictive in value is also repeated multiple times throughout the paper. The paper could benefit from some restructuring to avoid repetition.

      We appreciate this point. Some repetition is intentional because the Introduction motivates the methodological problem and previews the logic of the analyses before the formal Results section. We deem this contextual overlap necessary for adequately understanding the rationale for the study at each stage of the manuscript, we have therefore retained the current overall structure.

      (4) Is there a particular reason why this paper includes and compares both EEG and MEG data?

      The earlier held-out dataset collected at PF included both EEG and MEG, whereas the independent main dataset collected at OC used EEG only. We used the PF EEG data for model selection and parameterization, while the independent OC EEG dataset served as our main test set. Showing that the same overall pattern was present across EEG and MEG also provided an opportunity to assess whether the result generalized across recording modalities.

      (5) Is there a particular reason why the AdaBoost results are compared to the outcome of an SVM and Random Forest?

      We compared AdaBoost with SVM and Random Forest as part of the model-selection procedure on the held-out PF dataset. Each algorithm was evaluated with a range of feature representations, and Haar-AdaBoost produced the highest AUC in the window immediately preceding slide transition. It was therefore selected for the primary analyses. We additionally compared Haar-AdaBoost post hoc with several standard EEG classifiers, including CSP-LDA and EEGNet, to assess whether the main temporal pattern depended on classifier choice. This supports our claim that lack of early classification is due to non-separability of the data rather than classifier selection.

    1. Author response:

      We thank the editors and reviewers for their careful and constructive evaluation of our manuscript. We are encouraged that the reviewers recognize the value of our biochemical, biophysical, structural-modeling, and cell-based analyses of kinesin-1 holoenzyme assembly, KHC–TRAK2 recognition, and the regulatory interplay between KLC1 and TRAK2. We also appreciate the concerns regarding the relationship of our findings to previous work, the strength of several mechanistic conclusions, validation and presentation of the structural models, and the need for additional controls and quantitative analyses.

      We plan to revise the manuscript substantially in response to these comments. Our provisional responses and planned revisions are summarized below.

      Reviewer #1

      We agree that the novelty of several findings should be more carefully defined in the context of the existing literature. In the revised manuscript, we will better integrate previous biochemical and structural studies of KHC–KLC assembly, TRAK-family adaptor binding to KHC, and kinesin-1 autoinhibition. In particular, we will explicitly compare our findings with the work of Diefenbach et al. [1]., Weijman et al. [2]., Tan et al. [3]., Ashaduzzaman et al. [4]., and Gladkova et al. [5]., and distinguish previously established structural features from the additional residue-level mutational validation and quantitative biophysical analyses provided in our study. We will accordingly revise statements of novelty throughout the manuscript.

      We also agree that our current data establish a direct CC1–CC4 interaction and its disruption by TRAK2 and KLC1, but do not directly demonstrate that this interaction is itself autoinhibitory or that its disruption activates full-length kinesin-1. We will therefore distinguish the experimentally observed CC1–CC4 interaction from the proposed regulatory model and temper terms such as “autoinhibitory latch,” “activation switch,” and related mechanistic conclusions where appropriate. We will also expand the Discussion to consider how this interaction may relate to the established roles of full-length KLC and MAP7 in kinesin-1 regulation.

      To strengthen the presentation of the AlphaFold3-based models, we will provide model-confidence information, including pLDDT, PAE, and ipTM metrics, specify the exact sequences and residue boundaries used for each prediction, and include additional prediction outputs where informative. We will also more clearly distinguish experimentally supported conclusions from structural hypotheses, particularly regarding the proposed steric and/or conformational effects of the extended KLC1 coiled-coil on the KIF5C CC4 region.

      Finally, we will strengthen the quantitative and methodological presentation of the study. We will provide clearer construct information, explicitly report experimental replication, quantify the mitochondrial enrichment and cellular distribution analyses in Figures 4 and 5, and revisit the interpretation of stoichiometries obtained with shorter coiled-coil fragments. Statements implying mitochondrial transport will be revised to reflect that the current cellular experiments directly demonstrate mitochondrial recruitment rather than organelle motility.

      Reviewer #2

      We agree that the relationship between our study and previous structural work should be made substantially clearer. Although several relevant studies were cited in the original manuscript, the extent to which our findings confirm, extend, or differ from these previous models was not sufficiently explained. We will revise the Introduction, Results, and Discussion accordingly, including explicit comparisons with the structural predictions of Weijman et al. [2]., the XL-MS-supported model of Tan et al. [3]., the recent cryo-EM/integrative model of Ashaduzzaman et al. [4]., and the TRAK–KHC work of Gladkova et al [5].

      We also appreciate the concern that mutations introduced into hydrophobic interfaces could affect the intrinsic stability or homodimerization of KHC or TRAK2, rather than selectively disrupting heterotypic interactions. To address this alternative explanation, we plan to evaluate the oligomeric states and stability of key interface mutants using appropriate biophysical approaches, including SEC-MALS and thermal-stability measurements. These results will be incorporated into the revised manuscript and used to reassess the interpretation of the corresponding binding and cellular recruitment experiments.

      As noted above, we will also provide substantially more information on the confidence and reproducibility of the AlphaFold3 predictions, including pLDDT, PAE, and ipTM metrics, and will clearly annotate the residue boundaries of all modeled fragments.

      Reviewer #3

      We agree that the cellular experiments require additional quantification and clearer presentation. We will quantify the mitochondrial enrichment of KIF5C and the effects of KLC1 co-expression on the intracellular distribution of KIF5C and TRAK2 across independent experiments. We will also include appropriate controls for endogenous/background fluorescence, improve image and scale-bar presentation, and revise the corresponding terminology so that the conclusions accurately reflect the experiments performed.

      We will strengthen the reproducibility and presentation of the biochemical and biophysical data. Key ITC measurements will be supported by independent repeats and reported with the corresponding binding parameters and variability. For the SEC experiments in Figure 3, we will include SDS-PAGE analysis of relevant fractions and more clearly describe the composition of each protein mixture. Appropriate positive controls will also be added to the Co-IP experiments where requested.

      We will further improve the presentation of the structural models by providing confidence metrics and residue annotations, and we will carefully revise the terminology used to describe SEC, SEC-MALS, ITC, and other biochemical approaches. The Abstract and main text will also be edited to more clearly describe the experimental approaches used and to ensure that all mechanistic conclusions are matched to the strength of the available evidence. More broadly, we will revise the manuscript to sharpen its central message while avoiding overstatement. In particular, we will distinguish direct experimental observations—such as KHC–KLC1 assembly, KHC–TRAK2 recognition, KLC1-dependent modulation of TRAK2 engagement, and the CC1–CC4 interaction—from mechanistic models that remain to be tested more directly.

      We expect to complete these revisions and associated experiments within approximately 10–12 weeks. We thank the editors and reviewers again for their constructive comments, which we believe will substantially improve the rigor, clarity, and positioning of the study.

      (1) Diefenbach RJ, Mackay JP, Armati PJ, Cunningham AL. The C-terminal region of the stalk domain of ubiquitous human kinesin heavy chain contains the binding site for kinesin light chain. Biochemistry. 1998 Nov 24;37(47):16663-70. doi: 10.1021/bi981163r.

      (2) Weijman JF, Yadav SKN, Surridge KJ, Cross JA, Borucu U, Mantell J, Woolfson DN, Schaffitzel C, Dodding MP. Molecular architecture of the autoinhibited kinesin-1 lambda particle. Sci Adv. 2022 Sep 16;8(37):eabp9660. doi: 10.1126/sciadv.abp9660.

      (3) Tan Z, Yue Y, Leprevost F, Haynes S, Basrur V, Nesvizhskii AI, Verhey KJ, Cianfrocco MA. Autoinhibited kinesin-1 adopts a hierarchical folding pattern. Elife. 2023 Nov 1;12:RP86776. doi: 10.7554/eLife.86776.

      (4) Ashaduzzaman M, Tang Y, Okada K, Fried SD, Mckenney RJ, Al-Bassam J. Structural basis of kinesin-1 autoinhibition and its control of microtubule-based motility. Sci Adv. 2026 Jul 17;12(29):eaeg1267. doi: 10.1126/sciadv.aeg1267.

      (5) Gladkova C, Paez-Segala MG, Grant WP, Kittisopikul M, Myers SA, Wang Y, Vale RD. A molecular switch for coordinating kinesin and dynein transport of mitochondrial cargo. Science. 2026 Aug 6;393(6811):601-606. doi: 10.1126/science.aeh1475.

    1. Author response:

      We thank the reviewers for the overall positive review that declares our results convincing. We will revise the paper to improve the presentation of the model and results as suggested by the reviewers. The revision will be accompanied by a more detailed response.

    1. Author response:

      Reviewer #1 (Public review):

      (1) The authors investigate the use of the knocked-in human immunoglobulin genes in heavy chains and light chains and provide the frequency of productive rearrangements using these genes. However, there is no information about the frequency of the right heavy-light chain pairs. This information would be important to calculate the real frequencies of potential bNAb precursors in these mouse models.

      We acknowledge that our bulk sequencing-based repertoire analysis does not assess the pairing of immunoglobulin (Ig) heavy and light chains. To add this information, we plan to sort IgM<sup>+</sup>IgD<sup>hi</sup> naive B cells from the mouse models and use single-cell RT-PCR to analyze paired heavy and light chains from individual B cells. Since the assay detects Ig transcripts, it will also address comment #2 about the lack of expression data for the human Ig segments.

      The main goal of the single-cell RT-PCR experiment is to verify that the human Ig segments in the mouse models can be expressed as B cell receptors (BCRs) in naive B cells. However, because of its low-throughput nature, the assay is unlikely to be sensitive enough for detecting bnAb precursors. As shown in Figure 5G, the frequencies of bnAb-like CDR H3s for DH270, BG18 and PCT64 are in the range of 10<sup>-4</sup>. The frequencies of paired bnAb-like heavy and light chains will be even lower. It will be difficult to robustly measure the frequencies of such rare BCRs even with 10x Genomic single-cell sequencing. For reference, 10x Genomic sequencing of B cells from 10E8 KI mice yielded 1026 heavy and light chain pairs (1). The sample size was adequate for analyzing light chains paired with the pre-rearranged 10E8 heavy chain, which is expressed in most B cells. The sequencing depth will be insufficient for detecting rare bnAb precursors in the rearranging mouse models of this study. Deep bulk sequencing data were used to calculate bnAb precursor frequencies in our previous VRC01 mouse models and in humans and nonhuman primates (2-8). It is possible to enrich bnAb precursors for single-cell analysis by sorting epitope-specific B cells (9-11). However, this method requires sorting probes that exhibit high affinity and selectivity for bnAb precursors. We believe immunization of the mouse models will be the most direct and definitive way to detect bnAb precursors and test their functions in these mouse models. As mentioned in the manuscript, we have already provided the mouse models to several investigators for immunization experiments.

      (2) The authors use HTGTS-rep-seq to investigate immunoglobulin gene rearrangements at the genomic DNA level. This method is very useful for analyzing gene recombination because it provides information about both productive and non-productive rearrangements. However, this method does not provide information about BCR expression, and it is not optimal for investigating repertoire composition. BCR expression would provide a more rigorous characterization of the mice and confirm functionality.

      It is true that HTGTS-rep-seq does not directly show the expression of productive rearrangements. As outlined in our response to comment #1, we plan to perform single-cell RT-PCR to confirm the expression of the integrated human Ig segments in IgM<sup>+</sup>IgD<sup>hi</sup> B cells.

      We have used HTGTS-rep-seq extensively to analyze V(D)J rearrangements. Overall, the outcomes of the repertoire analysis correlated well with functional assays of BCR expression. For example, we identified VRC01-class heavy and light chains in VRC01 mouse models with HTGTS-rep-seq; correspondingly, immunization of the mouse models elicited VRC01-class antibodies (7, 8, 10). As another example, we used HTGTS-rep-seq to characterize V(D)J rearrangements at different stages of B cell development (12). The ratio of productive/nonproductive V(D)J rearrangements increases as B cells mature. The correlation suggests that the productive rearrangements, as detected by HTGTS-rep-seq, are selected by virtue of their expression as BCRs, which are required for B cell maturation and survival.

      (3) The goal of this study was to produce models that could provide a diverse bNAb-like repertoire. Specific quantification of the diversity of the repertoire is not provided. The study does not provide information about the sequences that do not use the intended genes.

      In our previous analysis of the VRC01 mouse models, we calculated the proportion of unique CDR3s and CDR3 overlap among different animals and used these parameters to represent repertoire diversity (7, 8). We will perform the same analysis for the six mouse models in this study. The V(D)J rearrangements that do not use the human Ig segments are composed of mouse Ig segments, and we will show repertoire analysis of these rearrangements in the revised manuscript.

      Reviewer #2 (Public review):

      (1) Abstract Clarity:

      Concluding sentences should incorporate the discussion's explanation: finding natively low-frequency precursors in standard humanized locus mice is statistically prohibitive due to their smaller absolute B-cell compartment. These models bypass this restriction by maximizing relevant segment expression to expand the functional CDR3 search space.

      We will make the suggested change in Abstract.

      (2) Results (Line 183, BG18 expansion):

      The intriguing expanded B1 cell population warrants more conservative commentary regarding genuine autoreactivity versus other possibilities, such as hyperactive baseline signaling via autophosphorylation (as shown by Hassan Jumaa for certain HC/LC clonotypes). While beyond this manuscript's scope, these mechanisms are differentiable via calcium flux assays with general anti-BCR signaling reagents.

      We are currently examining the cause of B1 cell expansion in the BG18 model. Our preliminary data suggest that some of the B1 cells express autoreactive antibodies, but more work is needed to reach a conclusion. Until then, we are open to alternative possibilities, as suggested.

      (3) Results (p15/Line 324, PCT64/CH235 Vκ Allelic Architecture):

      The text states that lacking a recombination cassette caused hVκ3-20 to account for only a fraction of rearrangements. While Figure 1B's general engineering feature (tandem reverse hJκ-RSS 23 and 12 RSS hJκ) implies human Vκ should predominate everywhere, Figure 1C suggests hVκ3-20's low representation in CH235 and PCT64 models stems from being introduced differently-specifically via pre-rearranged minigenes rather than unaltered RSS orientations in an unrearranged cassette. The authors should clarify this point in the text and/or Figure 1.

      The recombination cassette, as diagrammed in Figure 1B, is not in the CH235 and PCT64 models. Instead, the hVk3-20 allele in these models was derived from one of the previous VRC01 mouse models (7). As described in the Luo et al paper (7), hVk3-20 replaces mouse Vk3-7 in the Igk locus, but all the other mouse Vk segments are intact and functional. In this configuration, hVk3-20 rearranges as one of the Vk segments in Igk allele and accounts for about 10% of total Igk rearrangements. We will clarify this point in the revision.

      (4) Results (p14, Clever Engineering of λLC rearranging mice):

      Replacing mCκ with hCλ3 is a clever genetic trick and an important proof of concept for stably accommodating a human lambda rearranging light chain cassette within the mouse kappa locus. This excellent methodological highlight deserves prominent recognition as a template for other model developers. I suggest giving this further play in the discussion.

      We will highlight this design in the discussion.

      (5) Discussion (Model Comparisons & Baseline Resolution):

      The authors aptly compare these humanized mice to macaques; in addition to their superior scalability, they point out that macaques don't recapitulate human-specific bnAb-relevant configurations in certain instances (like lacking the VH1-2 minigene for VRC01-class responses, or utilizing germline D segments that favor V2 apex responses, potentially overestimating human responses). To further enhance nuance, referencing other prior review KI model literature on this topic (some published by these authors) would be beneficial. For context, KI-derived adoptive transfer models offer more potential diversity (thus, 'higher bar' off-target response testing) and frequency control but are restricted to short priming studies. Conversely, the rearranging models in this study support full vaccine regimens and generate multiple variant bnAb precursors to compare potential in vivo response plasticity.

      As suggested, we will include additional references and comparisons of the Ig humanized mouse models with KI mice. The reviewer raised an important point about off-target responses. Adoptive transfer models have the full mouse antibody repertoire. By comparison, the antibody repertoires of the Ig-humanized mouse models are dominated by a select set of human Ig segments, with minimal contribution from mouse antibodies. From this perspective, the adoptive transfer model provides a more diverse range of potential off-target antibodies. On the other hand, the Ig-humanized mouse models may be superior to wild-type mice in producing antibodies against the immunogenic glycan holes in envelopes (13). Reaching these glycan holes may require sufficient CDR H3 length, and based on CDR H3 length distribution, Ig-humanized mouse models could be more capable of recapitulating this type of off-target response than wild-type mice.

      (6) Discussion (Baseline phenotypes):

      One limitation of the cellular flow data, albeit beyond the manuscript's current scope, is that the baseline phenotypes predominantly reflect variations of a fixed pair of V(D)J rearrangements, rather than bona fide patient-derived UCA bnAb precursors with correct charges/lengths. To help resolve pre-antigenic functional signaling boundaries and thus potentially aid immunogen design, the discussion could note how future work could aim to use techniques like single-cell transcriptomics to map expressed selection signatures of bnAb precursor paired V(D)J's to rule out anergy or survival/death gene signatures.

      The reviewer is correct that the surface phenotypes of rare bnAb precursor B cells, such as low BCR levels on anergic B cells, may not be apparent in the bulk flow cytometric analysis. Single-cell transcription signature analysis would be a high-resolution method to analyze bnAb precursor B cells. The technical challenge is low bnAb precursor frequencies, and enrichment of bnAb precursors by immunogen sorting may be the necessary for their detection. We will discuss this point in the revised manuscript.

      (7) Discussion (PG9 Model & HCDR3 Length Constraints):

      While the PG9 model's failure to produce bona fide precursors is unsurprising given its long HCDR3, the authors should provide a bit more detail as to whether a subset of PG9 variants with slightly shorter HCDR3s are permissive for bnAb production (analogous to DH511/10E8). Providing the specific HCDR3 sizes generated by this model in relation to recently discovered monkey antibodies-which are shorter/different but function like PG9 bnAbs (e.g., Guenega et al Nature 2026) - would offer excellent context. Such related lineage and/or lineage precursor variants could serve as structural alternatives, and highlighting how these length constraints impact selection provides vital boundary conditions for the immunogen design field when planning germline-targeting regimens.

      The suggested recent studies (14-17) showed that V2 apex targeting is achievable with relatively shorter CDR H3s (22-25aa), which are within reach in the PG9 mouse model. However, the rhesus antibodies utilize IGHD3-15 with optimal V2 apex targeting motif. It remains to be determined whether hD3-3-based antibodies with comparable CDR H3 length would function similarly. We will incorporate the new information from rhesus immunization studies into the discussion.

      References:

      (1) Ray R, Schiffner T, Wang X, Yan Y, Rantalainen K, Lee CD, et al. Affinity gaps among B cells in germinal centers drive the selection of MPER precursors. Nat Immunol. 2024;25(6):1083-96.

      (2) Habib R, Solieva SO, Lin ZJ, Ghosh S, Bayruns K, Singh M, et al. Deep mining of the human antibody repertoire identifies frequent and genetically diverse CDRH3 topologies targetable by vaccination. Proc Natl Acad Sci U S A. 2026;123(18):e2532810123.

      (3) Swanson O, Martin Beem JS, Rhodes B, Wang A, Barr M, Chen H, et al. Identification of CDRH3 loops in the B cell receptor repertoire that can be engaged by candidate immunogens. PLoS Pathog. 2023;19(5):e1011401.

      (4) Steichen JM, Phung I, Salcedo E, Ozorowski G, Willis JR, Baboo S, et al. Vaccine priming of rare HIV broadly neutralizing antibody precursors in nonhuman primates. Science. 2024;384(6697):eadj8321.

      (5) Steichen JM, Lin YC, Havenar-Daughton C, Pecetta S, Ozorowski G, Willis JR, et al. A generalized HIV vaccine design strategy for priming of broadly neutralizing antibody responses. Science. 2019;366(6470).

      (6) Willis JR, Berndsen ZT, Ma KM, Steichen JM, Schiffner T, Landais E, et al. Human immunoglobulin repertoire analysis guides design of vaccine priming immunogens targeting HIV V2-apex broadly neutralizing antibody precursors. Immunity. 2022;55(11):2149-67.e9.

      (7) Luo S, Jing C, Ye AY, Kratochvil S, Cottrell CA, Koo JH, et al. Humanized V(D)J-rearranging and TdT-expressing mouse vaccine models with physiological HIV-1 broadly neutralizing antibody precursors. Proc Natl Acad Sci U S A. 2023;120(1):e2217883120.

      (8) Tian M, Cheng C, Chen X, Duan H, Cheng HL, Dao M, et al. Induction of HIV Neutralizing Antibody Lineages in Mice with Diverse Precursor Repertoires. Cell. 2016;166(6):1471-84.e18.

      (9) Havenar-Daughton C, Sarkar A, Kulp DW, Toy L, Hu X, Deresa I, et al. The human naive B cell repertoire contains distinct subclasses for a germline-targeting HIV-1 vaccine immunogen. Sci Transl Med. 2018;10(448).

      (10) Cottrell CA, Hu X, Lee JH, Skog P, Luo S, Flynn CT, et al. Heterologous prime-boost vaccination drives early maturation of HIV broadly neutralizing antibody precursors in humanized mice. Sci Transl Med. 2024;16(748):eadn0223.

      (11) Schiffner T, Phung I, Ray R, Irimia A, Tian M, Swanson O, et al. Vaccination induces broadly neutralizing antibody precursors to HIV gp41. Nat Immunol. 2024;25(6):1073-82.

      (12) Lin SG, Ba Z, Du Z, Zhang Y, Hu J, Alt FW. Highly sensitive and unbiased approach for elucidating antibody repertoires. Proc Natl Acad Sci U S A. 2016;113(28):7846-51.

      (13) McCoy LE, van Gils MJ, Ozorowski G, Messmer T, Briney B, Voss JE, et al. Holes in the Glycan Shield of the Native HIV Envelope Are a Target of Trimer-Elicited Neutralizing Antibodies. Cell Rep. 2016;16(9):2327-38.

      (14) Marchitto L, Wagh K, Roark RS, Coleon S, Li H, Skelly AN, et al. Enhanced B cell priming induces broadly neutralizing HIV-1 apex antibodies. Nature. 2026;656(8128):712-22.

      (15) Guenaga J, Ádori M, Bale S, Phulera S, Zygouras I, Schleich FA, et al. Vaccination generates broadly cross-neutralizing antibodies to the HIV Env apex. Nature. 2026;654(8119):777-85.

      (16) Mishra N, Liang B, Roark RS, Ghosh AR, Callaghan S, Lee WH, et al. Germline-targeting HIV immunogen induces cross-neutralizing antibodies in outbred macaques. Immunity. 2026;59(4):1140-60.e11.

      (17) Ma KM, Sutton HJ, Pratap PP, Steichen JM, Carnathan D, Quinn J, et al. HIV broadly neutralizing antibody precursors to the Apex epitope induced in nonhuman primates. Sci Immunol. 2025;10(110):eadt6660.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      This study by Damphousse, Calvin, and Redish investigates how the hippocampus represents competing future outcomes during approach-avoidance conflict. Using an ethologically relevant robotic predator foraging paradigm, the authors aimed to dissociate hippocampal activity associated with reactive defensive responses (escape) from that linked to anticipatory withdrawal decisions. The central finding is that dorsal hippocampal representations differentiate these two modes of defensive behavior within a single naturalistic assay. Specifically, the authors show that attack-triggered retreats and mid-track aborts differ in movement dynamics and hippocampal spatial decoding despite sharing a common behavioral endpoint, that hippocampal representations during pauses predict subsequent behavioral outcomes, and that these representational biases emerge before overt behavioral divergence. The main importance of the study lies in moving beyond viewing the hippocampus as merely encoding spatial location or threat salience, instead suggesting that hippocampal ensemble activity dynamically tracks and differentially weights threat-related, reward-related, and safety-oriented future states to bias behavior before overt action occurs.

      Strengths:

      The study has several notable strengths. First, the behavioral decomposition into retreats, mid-track aborts, and mid-track continues is rigorous and provides a highly interpretable analytical framework. Second, replication across two independent cohorts - despite differences in arena configuration, robot design, and extinction procedures - meaningfully strengthens confidence in the robustness of the findings. Third, the unified reanalysis pipeline across cohorts reflects strong analytical discipline, and the Bayesian decoding framework is well-suited to addressing the central representational questions. Fourth, the ethological relevance of the robotic predator paradigm is a major advantage, allowing the authors to examine a richer repertoire of defensive and decision-related behaviors than is possible in conventional fear-conditioning assays. Overall, the experiments are well designed, the data are clearly presented, and the findings make a valuable contribution to understanding how the hippocampus supports decision-making under threat.

      Weaknesses:

      The study is technically strong, but a few modest revisions would further enhance it.

      (1) First, the abstract mentions extinction and reinstatement effects, but neural analyses focus primarily on the attack phase. It would be helpful to clarify or adjust the abstract accordingly.

      (2) Second, some interpretive language ("guide," "bias") leans toward causal phrasing. Given the correlational data, using "predict" or "correlate with" would be more precise.

      (3) Third, given the relationship between running speed and hippocampal theta, considering speed-related contributions to decoding differences would be useful.

      (4) Fourth, reporting turnaround positions for mid-track abort and continue trials (Figure 7) would provide helpful context.

      (5) Fifth, a figure comparing stimulated vs. non-stimulated sessions in cohort 2 would support the claim that closed-loop stimulation had no measurable effect.

      (6) Finally, reporting effect sizes for key decoding comparisons would add clarity.

      Reviewer #2 (Public review):

      Summary:

      This manuscript extends previous work from Calvin et al. and examines hippocampal representations during approach-avoidance conflict in a robotic predator foraging task. The paradigm itself is very interesting and addresses an important but relatively understudied question in the navigation and foraging literature: how the brain balances risk versus reward during goal-directed behavior. While hippocampal representations of positively valenced goals and future intentions have been extensively studied, much less is known about how these representations evolve during risk-reward tradeoffs involving threat.

      The authors use a relatively simple and interpretable decoding approach together with thoughtful behavioral comparisons to ask whether future behavioral outcomes can be read out from hippocampal activity before behavior diverges. The most compelling comparison is between mid-track aborts (MTAs) and mid-track continues (MTCs), where the animals initially exhibit very similar pause behavior but ultimately either abort or continue the trajectory. The authors show that decoded location during these pauses differs prior to the overt manifestation of the behavioral decision, suggesting that hippocampal representations may reflect evolving internal evaluation processes during approach-avoidance conflict.

      Strengths:

      A major strength of the work is the behavioral paradigm itself. This type of risk-reward conflict task is relatively uncommon in the hippocampal navigation literature and provides a rich framework for examining defensive decision-making during naturalistic foraging behavior.

      The decoding analyses are also relatively simple and easy to interpret. Rather than relying on highly complex modeling approaches, the authors use straightforward comparisons of decoded spatial representations across behavioral conditions, making the results accessible and conceptually clear.

      Another strength is the use of behavioral controls to isolate comparisons between related behaviors. In particular, the comparison between MTAs and MTCs is compelling because the animals exhibit similar pause states before the behavioral outcomes diverge. This provides a useful framework for asking whether hippocampal activity reflects future behavioral outcome before the decision is overtly expressed.

      Overall, the study asks an interesting question using a novel paradigm and provides evidence that hippocampal representations during approach-avoidance conflict may reflect future behavioral trajectory.

      Weaknesses:

      The main weakness is that many of the reported effects are relatively subtle and are not sufficiently controlled for differences in speed, trajectory structure, and other behavioral variables across conditions. While the subtraction plots (green versus purple decoding differences) appear visually striking, the actual effect sizes are fairly small, making it difficult to assess how robust or behaviorally meaningful these differences are.

      Relatedly, many of the most interesting questions in this task concern how behavior unfolds dynamically within a trial, yet much of the analysis averages across events and trajectories. As a result, potentially important aspects of the behavior may be obscured.

      In particular, the manuscript would benefit from richer characterization of the animals' actual movement trajectories and spatial strategies. Because the analyses rely heavily on linearized position, it is difficult to determine whether animals behave differently in two-dimensional space across conditions. For example, during continued approaches, do animals preferentially hug the wall opposite the robot? Do different behavioral conditions show distinct lateral occupancy or trajectory structure? These types of analyses would make the behavioral interpretation substantially more compelling.

      More generally, while the results are suggestive and interesting, the relatively small decoding differences and substantial behavioral confounds make it difficult to conclude that the observed effects reflect distinct internal evaluative or threat-related states.

      Reviewer #3 (Public review):

      Summary:

      The study reanalyzes data from a previously published cohort together with an additional cohort to investigate hippocampal activity during approach-avoidance conflict. Unlike many prior studies that isolate reward- or threat-based learning, this task requires animals to evaluate reward and threat concurrently. The central finding is that hippocampal representations differ between hesitant behaviors that lead to approach versus avoidance outcomes, with representations of the attack zone more likely during pauses preceding abort decisions. This is an important extension of prior work on hippocampal activity and deliberation, suggesting that the hippocampal content may help shape the eventual outcome.

      Strengths:

      All behavioral findings are replicated independently across cohorts, making the behavioral results highly convincing. The design is robust, and the task is especially valuable for studying approach-avoidance conflict. The behavioral paradigm is complex and rare, and neuronal recordings in such a paradigm are of great value.

      The major strength of the study is the comparison of neural activity during hesitant behavior leading to different outcomes, namely, pauses followed by the animal aborting the approach (mid-track aborts), and pauses followed by the animal committing to the approach (mid-track continues). Hippocampal activity differed between the two pauses: the attack zone was more likely to be represented during mid-track aborts. The same effect was observed on the journey before the pause: even before the animal hesitates, hippocampal activity before a pause that led to a mid-track abort was more likely to represent the attack zone than hippocampal activity before pauses that led to continued approach. This analysis suggests that hippocampal content before and during deliberative behavior is predictive of the animal's decision.

      Weaknesses:

      The interpretation of the retreat-related decoding results is less clear. The study compares two sets of retreating behavior: on the one hand, retreat after being attacked, and on the other hand, retreat after hesitation in the absence of an attack (a mid-track abort). Hippocampal activity represents the attack zone more after the animal is attacked. However, these two retreating behaviors originate from different spatial locations: retreats always start past the "attack threshold", while mid-track aborts always start before this threshold. Given that hippocampal decoding is strongly location-dependent, this difference in position makes the neural decoding results difficult to interpret. The increased representation may be due to differences in physical location, rather than the distinct processing of immediate threat and an anticipatory return state.

      We thank the reviewers for their careful, constructive, and fair assessment of our manuscript, “Hippocampal representations differentiate reactive and anticipatory responses during foraging under threat.” We were pleased that the assessment characterized our study as important and the evidence supporting its main finding as solid. We also appreciate the reviewers’ recognition of the strengths of the behavioral paradigm and the conceptual contribution of distinguishing hippocampal representations associated with reactive and anticipatory responses to threat.

      We carefully considered the reviewers’ comments and do not feel that the manuscript requires extensive revision. The reviewers suggested several thoughtful additional analyses, including further behavioral controls and explicit predictive analyses. We agree that these would be informative and intend to carry several of these directions forward with future datasets. However, for the present manuscript, the suggested analyses would extend the scope of the work but are unlikely to substantially alter the central observations, and we have therefore chosen not to undertake them for the present manuscript.

      We have only made very minor changes to the text and figures, corresponding to what we might do in a manuscript that had been “accepted” under the old-style journal process. We have

      - Revised the abstract to more accurately reflect the neural analyses presented.

      - Softened the interpretive language throughout to avoid implying causality where the data establish associations, and explicitly acknowledged this limitation in the discussion.

      - Clarified the explanation of the timing and location of robot attacks relative to the attack threshold.

      - Clarified the definitions and explanations of the temporal segmentation of MTA and MTC pauses.

      - Clarified the explanations of the outbound epoch used in the MTA-MTC comparison.

      - Expanded the methods describing temporal and spatial normalization of behavioral epochs.

      - Moved the headers on figures 5-7 as suggested by the reviewers to make them more clear.

      With these revisions, we believe the manuscript now accurately reflects what can be concluded from the current data and appropriately acknowledges the limitations raised during review.

      We sincerely thank the editor and reviewers for their thoughtful engagement. Their comments have improved the clarity and precision of the manuscript and provided valuable directions for future work.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      There are no major concerns, but some material could be added for clarity and to make the work more accessible to a more general scientific audience.

      We will add text for clarity and to make the work more accessible to a general audience per this comment and similar suggestions of the other reviewers.

      (1.1) A figure clearly showing the habituation protocol and the use of the dishabituators would be a good addition, even if the procedure has been done before and is cited. There can always be readers who are seeing this for the first time.

      We do think this is a good idea as the time scales of the experiment will be clearly marked as well and we plan to generate one in the revised manuscript.

      (1.2) It would also be nice to comment on other ways dishabituation can happen (for example, when the stimulus is removed for a short time and returns) and what their time scales are.

      If the stimulus is withheld, spontaneous recovery occurs, a process distinct from dishabituation and worth exploring on its own. In a previous publication (Semelidou et al. eLife 2018;7:e39569), we have shown that in this habituation paradigm with 4 min exposure either to the aversive Octanol, or the attractive Ethyl Acetate, spontaneous recovery occurs on or after 6 minutes after the habituated stimulus is withheld. This contrasts the immediate effect of the single dishabituating stimulus, delivered for a few seconds at the end of exposure to the habituator. Granted that per Thomson (Neurobiol Learn Mem. 2009), spontaneous recovery is a characteristic of habituation, we will work this point in the text.

      (1.3) And more generally, the paper could perhaps improve by making a stronger case for why the results are important not just for flies but for neuroscience in general.

      Thank you for the encouragement. We will try to rationally generalize our findings.

      Reviewer #2 (Public review):

      (2.1) However, the claim that this represents a fundamental difference between homosensory and heterosensory pathways for dishabituation is overstated.

      We had no intention of stating more than the fact that footshock and yeast odor dishabituators relay these stimuli to the mushroom bodies via distinct dopaminergic neurons, hence differentiating distinct dishabituating stimuli via the mechanosensory (footshock) and olfactory (yeast odor) modalities as they engage the mushroom bodies. As the reviewer suggests we will use more measured and specific language to state the above.

      (2.2) The introductory section does not adequately present current broad models for habituation and dishabituation.

      This was not done intentionally, but rather because we aimed at a less extended introductory section and ostensibly this resulted in brief and possibly inadequate presentation of current habituation models. We will present a much more detailed introduction and detail of habituation and dishabituation models in the revised manuscript (Also see reply to point 3.5 below).

      (2.3) There are many different time scales, even for Drosophila olfactory habituation. These, as well as potential underlying mechanistic differences, need to be acknowledged; any claim should be specifically qualified for the time scales being studied here.

      We understand and appreciate the point of the reviewer, as well as its significance and we will address this both in the revised text, but also by the paradigm figure we will add as stated above (point 1.1), where the time scales will be explicitly included and emphasized.

      (2.4) Additionally, there are several unclear, vague, and inaccurate sections and statements. A more careful, precise, and considered presentation of current views, as well as more measured claims of the impact of the findings, would substantially enhance my enthusiasm.

      We will address these concerns of course, though pointing out the specific offending parts would ascertain addressing them thoroughly. As stated above, we will incorporate current views in the introduction and when discussing our results and their impact.

      Reviewer #3 (Public review):

      (3.1) The key issue is that the main concepts of this manuscript appear to be based on a misunderstanding/misinterpretation of the literature. As the authors set out to settle the debate "whether the novel dishabituating stimulus elicits sensitization of the habituated circuits, or it engages distinct neuronal routes to bypass habituation reinstating the naïve response", it seems that the authors based their investigation on the premise that "sensitization" is mediated by a facilitatory process within the S-R pathway, and "dishabituation" by a facilitatory process outside the S-R pathway. This is not the status quo in the field, particularly with the prevailing theory like the Dual-Process Theory.

      We appreciate the reviewer’s comment and the opportunity to clarify the conceptual framework of our work. Our intention was in fact to test the Groves and Thomson hypothesis (Neurobiol Learn Mem. 2009), in our olfactory habituation system. As such, dishabituation could have been the result of a facilitatory process within the S-R pathway, or from mechanisms outside of it. Our experimental design allowed to distinguish these possibilities and our results clearly show that dishabituation involves circuitry outside the S-R pathway. We do thank the reviewer for pointing out that we have not articulated clearly this intention and we will take care to communicate this effectively in the revised manuscript.

      (3.2) The original version of Dual-Process Theory (Groves and Thompson 1970, but also see Thompson 2008, Neurobiol Learn Mem) already hypothesized that habituation happens within the specific S-R pathway, and sensitization occurs separately in an "organism-wide" state system that modulates the output of all S-R pathways.

      As mentioned above, we are aware of the Dual-Process hypothesis. In fact, our data demonstrate that activity outside the olfactory S-R pathway, engaging novel neuronal circuits, mediates dishabituation. Unlike habituation, these circuits mediating dishabituation include at minimum, the mushroom bodies, the dopaminergic system and the APL neurons. In our view this does not support the “organism-wide state” system, but rather particular circuits that in agreement with the Groves and Thomson hypothesis, are outside the S-R pathway and modulate its behavioral output. We will work these concepts in the discussion section of the revised manuscript.

      (3.3) Dishabituation is recognized by the Dual-Process Theory as sensitization (organism-wide facilitation) manifested on top of existing habituation (depressed S-R pathway). This notion has been supported by a wide range of studies, including cat spinal cord reflex (e.g. Spencer et al. 1966) and work in Aplysia on heterosynaptic facilitation for both sensitization and dishabituation. Therefore, simply showing that the newly identified facilitatory pathways are outside the S-R habituation pathway is insufficient to demonstrate dishabituation.

      We respectfully disagree with the concluding sentence here. In all of our experiments, we observe a clear recovery of olfactory avoidance after exposure to the footchock, or yeast odor dishabituators. Moreover, the dishabituators are emulated by (photo)activation of particular neuronal circuits and the recovery of olfactory avoidance is blocked when these circuits are silenced. Regardless of whether this recovery is classified as dishabituation via sensitization or another facilitatory process, the key point is that the habituated response is reliably reinstated contingent upon the dishabituating stimulus. We believe this meets the established criteria for dishabituation.

      (3.4) As behavioral facilitation of a habituated response can be achieved by dishabituating (specific recovery of the S-R pathway) and/or superimposed sensitizing (organism-wide) processes, dishabituation and sensitization of this olfactory response must be first dissociated; however, the study provided no evidence for the dissociation. Without this piece of evidence, the claim of this paper that the newly identified pathways mediate dishabituation is not fully supported.

      We agree with the reviewer that we have not provided specific evidence dissociating dishabituation and sensitization of the particular olfactory response beyond the evidence implicating particular circuitry in the outcome of facilitation of the olfactory response.

      It should be noted that in photoactivation of the implicated circuitries in naïve flies, we do not observe enhanced octanol avoidance, suggesting that activation of these circuits alone does not induce sensitization. Moreover, our results show that neither footshock nor yeast odor drive an organism-wide sensitization, as silencing specific circuits was sufficient to block dishabituation—something that would not be expected if a global sensitization process was responsible of reinstating the olfactory response.

      Nonetheless, we will also attempt to dissociate sensitization from dishabituation using mutants previously reported deficient in sensitization (Duerr and Quinn, PNAS 1982), assuming these mutants retain normal olfactory habituation.We will also try sensitization protocols in the case of within-modal dishabituation to further clarify the underlying mechanisms. In principle, this includes using diluted Octanol as the habituating stimulus and attempt dishabituation with concentrated octanol.

      (3.5) The literature review of this manuscript has some discrepancies. In the introduction, the authors wrote "initial studies in Aplysia were consistent with the "dual-process theory" (Groves and Thompson 1979), where response recovery due to dishabituation appeared to result from sensitization superimposed on habituation, thus driving reversal of the attenuated response (Carew, Castellucci et al. 1971, Hochner, Klein et al. 1986, Marcus, Nolen et al. 1988, Ghirardi, Braha et al. 1992, Cohen, Kaplan et al. 1997, Antonov, Kandel et al. 1999, Hawkins, Cohen et al. 2006)." Hochner 1986 and Marcus 1988 in fact indicated otherwise. Hochner 1986 suggests that dishabituation and sensitization involve different molecular processes, while Marcus 1988 showed that dishabituation and sensitization have different behavioral characteristics. Therefore, the authors' statement is not supported by the cited literature.

      We are grateful to the reviewer for pointing out these significant discrepancies, consequent of multiple rounds of edits followed by our own oversight. These important publications for this manuscript will be referenced properly in the revised manuscript.

    1. Author response:

      eLife Assessment

      The authors study global neuropeptide changes in C. elegans mutants lacking functional BMP, using this as a viable and fertile animal model that exhibits consistent dyspepsia and chronic dietary restriction. The findings of this study are valuable as they provide a global picture of neuropeptide responses to starvation and detail a circuit from a sensory neuron to lipid metabolism in the gut. This work provides evidence that nutrient stress resulting from impaired food processing engages NLP-10-, NPR-35-, FLP-18-, and NPR-4-dependent signalling to promote fat utilization. However, the evidence is incomplete, as the order of action of the neuropeptides is weak.

      We thank Reviewing Editor, Senior Editor and the three reviewers for their constructive comments. We are encouraged that the reviewers regard the central finding that impaired pharyngeal function engages neuropeptide signaling to modify intestinal lipid metabolism as physiologically meaningful and supported by multiple lines of evidence. At the same time, we recognize that the reviews converge on a central concern: the evidence for the order of neuropeptides’ action is weak. The reviewers also suggest us to distinguish more clearly between what our experiments demonstrate and what we infer, to present the pathway as less strictly linear, and to be more explicit about the limits of cell-specific rescue for secreted peptides. We take these points seriously, and we are exploring possible revisions in light of them.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      This manuscript describes how defective food grinding due to loss of TGF-beta signalling leads to fat loss via specific neuropeptides and their cognate receptors in C. elegans. They define transcriptional mechanisms from the ADL sensory neuron to neuropeptide relays from neurons to the gut, wherein enzymatic effectors mediate fat metabolism. The genetic evidence presented to support this neuropeptide circuitry is based largely on transcriptional changes detected in bulk mRNA, cell-type-specific rescue, and lipid measurements using Nile Red staining in permeabilized/fixed animals and with lipidomics. The findings are of interest to researchers in neuropeptide regulation of physiology.

      Strengths:

      (1) The multifaceted analysis of dbl-1 and sma-6 provides good evidence that the primary defect leading to metabolic phenotypes is due to pharyngeal function.

      (2) The transcriptional survey of neuropeptide expression under fasting and in TGF-beta pathway mutants will be a useful resource for many labs studying neuropeptides in food sensing.

      (3) Outlining the process from dietary restriction to fat metabolism in the gut provides a big-picture view that establishes physiological relevance.

      (4) Identifying new functions for specific neuropeptides and their receptors in fat metabolism.

      We thank R1 for an accurate summary and for recognizing the value of this work. We also note R1’s characterization of our evidence as transcriptional and genetic. We agree with this description and will explicitly state the scope of our claims in future versions, clarifying that this work defines a functional hierarchy among genes and cells but does not provide biochemical, electrophysiological, or secretion-based evidence for direct molecular interactions.

      Weaknesses:

      Evidence that links NLP-10-NPR-35 signalling to FLP-18-NPR-4 is weak, and primarily rests on overlaps in npr-35 and flp-18 expression, as well as rescue of flp-18 under the npr-35 promoter. It remains possible that FLP-18 acts from those neurons, but is not activated by NPR-35 signalling, since the mechanisms downstream of NPR-35 are unclear in this context. Strengthening this link would require showing a change in FLP-18 activity; for example, showing npr-35-dependent changes in flp-18 transcription in npr-35-expressing neurons.

      We agree that this is the weakest link in our model. At present, this rests mainly on two observations: the overlap between npr-35 and flp-18 expression reported in public databases, and the ability of npr-35p::FLP-18 (or ttx-3p::FLP-18) to restore fat levels. These observations cannot exclude the possibility that FLP-18 acts from these neurons, or even from additional neurons, without being activated by NPR-35 signaling, and that the FLP-18 induction reflects the nutritional state rather than receptor activity.

      To test this directly, we will begin by measuring flp-18 transcript levels in two comparisons: (1) well-fed npr-35(lf) versus well-fed sma-6(lf); npr-35(lf), and (2) well-fed npr-35(lf) versus fasted npr-35(lf). In addition, transcriptional levels of nlp-10, flp-1, and flp-4 can be compared in these worms. If NPR-35 activity is required for flp-18 induction when nutrients are limiting, removing npr-35 should blunt or reduce this induction in the sma-6-mutated or nutrient-deprived backgrounds; If NPR-35 activity is not required, flp-18 induction should not be affected. A third possibility is that NPR-35 amplifies FLP-18 signaling, which would not conflict with the nutrient-sensing role of FLP-18 per se. Regardless of the outcome, we will rewrite this section to clarify the step from NLP-10 to FLP-18.

      The expression patterns of the neuropeptides and receptors that guide the sites of cell-specific rescue experiments are from well-fed animals. However, it remains a possibility that starvation alters neuropeptides and their receptors are expressed, which would produce a different circuit.

      This is a fair point, and we accept it as a limitation of the present study. The expression patterns that guided our rescue experiments were defined in well-fed animals, using published datasets (Beets et al., 2023; Ripoll-Sánchez et al., 2023; Ghaddar et al., 2023) and our own transcriptional reporters under well-fed conditions. We cannot exclude that nutrient status alters the expression of these peptides and receptors.

      We plan to examine intestinal npr-4p::GFP in well-fed and starved animals in the near future. We could also attempt to image neuronal npr-35p::GFP, but this would be technically challenging given mosaic expression and issues with worm orientation. In the Discussion of future versions, we will state this caveat and will be careful to describe our rescue experiments as identifying the cells in which a gene is sufficient to support the phenotype under the conditions tested, rather than as confirming the circuit in the starved animals.

      Different food levels produce different physiological and transcriptional responses. The manuscript largely assumes that starvation is equivalent to food reduction when they are physiologically distinct states.

      We agree, and we regret that our wording implied equivalence. Our intention was not to treat all nutrient-limited states as identical but to ask whether a common pathway is engaged. The observation that the same components are required under each of these energy-deficient conditions supports the physiological relevance of the pathway. We will rewrite the relevant sentences to convey this intent and to avoid implying that different nutritional states are equivalent. We acknowledge the limitation that our design cannot determine the degree of energy deficit required to engage the neuropeptides, or whether the response is graded across milder and more severe restriction.

      Reviewer #2 (Public review):

      Summary:

      This manuscript investigates how animals adapt their metabolism to conditions of reduced nutrient availability. Using C. elegans, the authors identify a neuropeptide signaling network that promotes intestinal lipid mobilization when nutrient acquisition is compromised. The study proposes that nutrient stress activates signaling involving NLP-10, NPR-35, FLP-18, and NPR-4, ultimately leading to increased utilization of stored triglycerides.

      A major strength of the work is the combination of multiple experimental approaches, including genetic analyses, neuron-specific rescue experiments, starvation paradigms, and lipid measurements. Together, these experiments support the conclusion that the identified neuropeptide pathway contributes to the regulation of energy stores during nutrient stress. The observation that similar signaling components function in both the mutant and starvation contexts strengthens the physiological relevance of the findings.

      Strengths:

      The revised manuscript is substantially improved and presents a coherent model linking sensory and interneuronal signaling to peripheral metabolic responses. The data convincingly establish functional roles for the identified neuropeptide components in controlling fat storage and mobilization.

      Readers should keep in mind that the exact relationships among pathway components are not completely resolved. While the genetic evidence supports placement of NLP-10, NPR-35, FLP-18, and NPR-4 within a common regulatory framework, the data are somewhat less definitive regarding the precise order of signaling events and whether all interactions are direct. The authors appropriately acknowledge some of this complexity, and a clearer distinction between experimentally demonstrated versus inferred connections would further strengthen the presentation.

      Overall, this is a carefully executed and biologically interesting study that advances our understanding of neuroendocrine control of metabolism during nutrient limitation.

      Weaknesses:

      No weaknesses were noted by this reviewer in the revision. My main comment is that whilst I appreciate the authors’ efforts to refine the signaling model in response to earlier comments, the pathway architecture remains somewhat complex, particularly regarding the relationships among NLP-10, NPR-35, FLP-18, and NPR-4. I encourage the authors to make one final pass through the text and model figure to clearly distinguish interactions that are directly supported by experimental evidence from those that remain inferred based on genetic relationships. This would help readers accurately interpret the strength of evidence supporting each step of the proposed pathway.

      We are grateful to R2 for the positive assessment and for the constructive suggestions. We understand that the remaining concerns related to clarity and presentation. We agree that the pathway architecture remains complex and that readers should be able to distinguish experimentally connections from inferred ones. We will revise the text and the model figure accordingly. For example, future versions could use solid connectors for data-supported steps and dashed connectors for inferred steps.

      We agree with R2 that readers should keep in mind that the exact relationships among pathway components are not completely resolved, and we agree and appreciate R2’s comment that “…the data are somewhat less definitive regarding the precise order of signaling events and whether all interactions are direct”, which echoes the suggestions from R1. We will address these points as outlined in our response to R1.

      Reviewer #3 (Public review):

      Summary:

      In this manuscript, Liu et al. used C. elegans animals lacking functional BMP as a model to dissect the neuropeptide signaling pathways that lead to BMP-associated fat loss. First, they established the BMP mutants as a model of dyspepsia that results in chronic dietary restriction. They then used this model to identify neuropeptide genes that are upregulated and required for BMP-associated fat loss. Next, they sought to identify the receptors for these neuropeptides and to place the genes in a genetic and cellular pathway. They also showed that the same neuropeptides and receptors contribute to fat loss in diet-restricted C. elegans. They conclude that they have identified a neuropeptide signaling cascade in which impaired pharyngeal function activates sensory neurons, which then signal through interneurons to enhance triglyceride hydrolysis in the intestine.

      Strengths:

      In this manuscript, Liu et al. characterized the pharyngeal muscles and the intestinal bacterial context of animals lacking functional BMP. They showed a correlation between BMP-associated fat loss and pharyngeal impairments that could lead to insufficient food grinding. This finding suggests that C. elegans lacking functional BMP could serve as a model for dyspepsia and chronic dietary restriction. Moreover, the authors analyzed previously published gene expression data to identify neuropeptides that are overexpressed in animals lacking BMP. They then used mutants for these neuropeptides and their receptors to determine which of these genes contribute to BMP-associated fat loss. Finally, they showed that the same neuropeptides and receptors also contribute to fat loss in diet-restricted C. elegans.

      We thank Reviewer 3 for a detailed assessment on this manuscript.

      Weaknesses:

      (1) The authors use double mutants between BMP pathway mutants and neuropeptide or neuropeptide receptor mutants to argue that the reduced fat levels of BMP mutants are suppressed. However, with the exception of unc-31, the fat content of the corresponding single neuropeptide or neuropeptide receptor mutant is not shown. Without these, the double-mutant phenotype cannot be interpreted as suppression, since it could reflect an independent effect on fat storage. To show that the effects are related to BMP signaling, the authors should compare wild-type animals to neuropeptide mutants in a sma-6(+) background. Similarly, the fat content of ADL-ablated animals is not shown in an otherwise wild-type background.

      We accept this criticism. We are going to add experiments on wild-type and related single-mutant strains in the near future. Specifically, we will report the fat content of nlp-10(tm6232), npr-35(ok3258), flp-18(tm2179), flp-1(sy1599), flp-4(sy1606), and npr-4(tm1782), and of ADL-ablated animals, in the sma-6-functioning background. We will also survey published datasets for independent measurements of fat content in these strains, if any exist.

      (2) In several places, the authors use cell-specific expression of neuropeptides to conclude that a given neuropeptide acts in a particular cell type (e.g., Figure 4B, C; Figure 5C, D). However, because neuropeptides are secreted and can act at a distance, expression in a non-native cell type may rescue the phenotype. These experiments therefore show sufficiency but do not establish the endogenous site of action. Cell-specific knockout or knockdown, or expression from control promoters in unrelated cell types, would help address this.

      We agree with the underlying point of this criticism. Expression of a secreted peptide from a heterologous promoter demonstrates that the peptide can act when produced in that cell; however, it does not establish where the peptide acts under physiological conditions. We are grateful to the reviewer for these suggestions and have carefully considered both approaches. While we fully appreciate their potential value, we believe it is more appropriate to regard them as complementary rather than decisive, and we would like to explain our reasoning in detail.

      The first approach, cell-specific knockdown, may or may not affect peripheral lipid catabolism in this system, because (1) the number of peptides capable of influencing fat storage is large, as shown in Figure 2 – figure supplement 1D, E, and (2) the expression pattern of a receptor or peptide gene may be altered under nutrient-deprived conditions (as in comments of R1). The axis we describe could be buffered by ligand redundancy, as our data on FLP-1 and FLP-4 show. Under such redundancy, a negative result from knocking down a single peptide in a group of cells would not exclude a physiological role for that peptide in that cell. The second approach, expression from a control promoter in an unrelated cell, might also be complicated by the point that R1 raises: if nutrient status alters the expression of peptides and their receptors, it becomes difficult to specify a cell type that is reliably “unrelated” to lipid regulation in the relevant physiological state. Therefore, we will modify our manuscript to describe the rescue experiments consistently as demonstrating sufficiency and discuss this limitation frankly.

      (3) The authors report that expressing npr-35 from two promoters with non-overlapping expression each fully restores the low-fat phenotype of sma-6; npr-35 mutants. This is surprising for a receptor and is difficult to interpret.

      We thank the reviewer for raising this point, and we realize that our description was not sufficiently precise. The two promoters drive expression in different subsets of npr-35-expressing neurons; however, in both cases npr-35 is overexpressed, as is typical of C. elegans transgenic lines. A non-exclusive explanation also seems plausible to us: the two cell populations (nmr-1-positive & ttx-3-positive) may converge on a shared downstream output, which is the release of FLP-18 from these interneurons, so that restoring receptor function in either population restores the ultimate output. We will revise the text to present both possibilities and to describe the result in terms of sufficiency.

      (4) The authors identify neuropeptide genes co-expressed with npr-35 and follow up on flp-18. The rationale for restricting the search to co-expressed neuropeptides may bias hypothesis generation. Similarly, the authors show that flp-1 and flp-4, in addition to flp-18, contribute to BMP-associated fat loss, but only flp-18 is examined further because of its overlapping co-expression with npr-35, again creating a bias in the investigation of the role of neuropeptide signaling in BMP-associated fat loss.

      We accept that restricting our attention to peptides co-expressed with npr-35 introduced a bias, and we will state this openly. We would like to note two considerations that may help contextualize this bias. First, flp-18 showed the strongest transcriptional induction among the peptides we examined (Figure 2 - figure supplement 1D), and this was an important reason for prioritizing it. Second, our subsequent analysis was not confined to co-expressed peptides: flp-1 and flp-4 are also required for BMP-associated fat loss, while flp-1 shows little overlap with npr-35 and does not appear to be released from npr-35-expressing neurons (Figure 5 - figure supplement 1D). The co-expression therefore served as an entry point rather than as a filter. We will clearly describe this rationale in the text, present the broader set of candidate peptides identified in our screen, and note that additional peptides are likely to contribute to fat regulation. We hope that the dataset will support work in this direction, both in our laboratory and in other laboratories.

      (5) It is difficult to interpret the experiment in Figure 5E, where the authors conclude that npr-4 is required in flp-18-overexpressing animals. Without a demonstrated fat-loss phenotype from overexpressing flp-18, a requirement for npr-4 in those animals cannot be meaningfully assessed.

      We assume that the reviewer is referring to Figure 5G, and we apologize for the confusion in this panel. This confusion may have arisen from the way we arranged the columns. The experiment was designed to ask whether npr-4 is required for overdosed FLP-18 to function (with overexpression ensured by sma-6(lf)-induced upregulation and the ttx-3p::FLP-18 transgene). Therefore, a clearer way to organize these columns would be to swap the third and fourth columns, which we will do in the revised version.

      We nonetheless agree with the reviewer’s underlying point. Because ttx-3p::FLP-18 alone does not reduce fat in the already fat-deficient sma-6(lf), the assay has limited dynamic range. So, a requirement for npr-4 cannot be established from this comparison alone. We will reorder the columns, correct the legend, and present the panel as consistent with npr-4 acting downstream of flp-18. We would also place greater emphasis on the comparisons in Figure 5B, in which sma-6(lf); npr-4(lf) retained more fat than sma-6(lf); flp-18(lf), an outcome expected if the receptor acts downstream of the ligand and if additional ligands converge on NPR-4.

      Overall, the authors convincingly identify neuropeptides and receptors that are overexpressed and that contribute to fat loss. However, several points make it difficult to fully support the proposed model and the linear pathway from the pharynx to the intestine through ADL sensory neurons and interneurons. These include the absence of phenotypic analysis of the single mutants, the challenges of interpreting cell-specific rescue experiments when studying neuropeptide function, the fact that additional neuropeptides causing BMP-associated fat loss are identified but not studied further, and results that do not necessarily point to a linear pathway (e.g., the triple mutant sma-6; nlp-10; npr-35 has a stronger phenotype than the double mutants with sma-6, the fat loss caused by overexpression of nlp-10 in a sma-6 background is not suppressed by npr-35, and the flp-18 overexpression experiment is difficult to interpret). The reviewer therefore suggests that the linearity of this pathway, and the sites of action of the neuropeptides and receptors, should be presented more cautiously or supported by additional data.

      We are grateful for this synthesis, which we take as the central conceptual comment of the review. We agree that our data do not support a strictly linear pathway, and we will revise both the text and the model figure accordingly.

      The two observations the reviewer cites, that the triple mutant sma-6; nlp-10; npr-35 retains more fat than either double mutant, and that removing npr-35 does not offset the fat loss caused by NLP-10 overexpression, point in the same direction: NLP-10 likely acts through receptor(s) in addition to NPR-35. We consider this plausible on independent grounds. Because nlp-10 is induced when nutrients are limiting, an additional receptor might be engaged only when NLP-10 rises above its basal level, or only when the nlp-10 expression domain expands under dietary restriction. Either scenario would explain why such a receptor has not emerged from interaction screens carried out under standard feeding conditions.

      In the revision, we will describe the axis as a genetic framework in which the NLP-10/NPR-35 and FLP-18/NPR-4 modules are related, with branch points at both the ligand and receptor levels, and we will mark the connections that remain inferential. We will also note that the conservation of NPR-35 across nematodes (Beets et al., 2023; Golinelli et al., 2024) may provide an entry point for identifying additional NLP-10 receptors, and we would welcome works in that direction.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      The manuscript could provide more nuanced and accurate context in several areas:

      (1) Work from the Ashrafi Lab (Greer et al., 2008, Cunningham et al., 2014) has described roles for daf-7 (another TGF-beta) in fat metabolism and should be cited to provide a more comprehensive introduction.

      Thanks! We will cite the work from the Ashrafi laboratory on the DAF-7 branch of TGF-β signaling and on fat metabolism in the Introduction of the revised manuscript.

      (2) The interpretation of the unc-31 phenotype is not as straightforward as the text indicates. unc-31 does not only affect DCVs, unc-31 mutants also have SV defects. Moreover, DCVs also release TGF-beta and monoamines. Thus, an unc-31 phenotypes does not necessarily implicate neuropeptides.

      We thank the reviewer for this comment and apologize for the confusion. In fact, in addition to analyzing unc-31(lf); sma-2(lf), we analyzed the fat levels of egl-3(lf); sma-2(lf) and egl-21(lf); sma-2(lf), and the phenotypes caused by the loss of egl-3 or egl-21 were similar to those caused by unc-31(lf) in these BMP mutants. We omitted these data from the previous version for simplicity, and we acknowledge that we wrongly overlooked the non-DSV roles of UNC-31/CAPS. We will revise this section by adding additional data on egl-3 and egl-21.

      (3) In lines 132-134, the logic of the argument is not clear, since it does not indicate how sma-3 rescue in the pharynx is linked to sma-6 in the ADL neurons.

      We agree with the reviewer’s comment and will remove the wording related to sma-3 rescue from this sentence in the revised manuscript.

      (4) Lines 271-273 indicate that BMP mutants are mildly long-lived. This point is only partially correct. Depending on the food level, daf-7 mutants can be long-lived, have no phenotype, or be short-lived.

      Thank you. We will rewrite the section on lifespan so that it reflects the lifespan of daf-7 mutants and BMP mutants properly.

      This manuscript could also be improved by clarifying or acknowledging several technical gaps/weaknesses:

      (1) For Supplemental Figure 2d, it is not clear if there is any correction for multiple hypothesis testing when assaying multiple neuropeptides. This point should be clarified.

      We acknowledge that we did not perform any multiple hypothesis testing on the data shown in this figure panel in the previous version. Due to technical limitations, we were unable to compare all qRT-PCR groups within a single 96-well plate. The qRT-PCR assays were performed separately for each gene, with double mutant and single mutant worms collected in the same-day manner. Accordingly, these qRT-PCR results are not suitable for comparisons between different genes, but they do allow valid comparisons between the double mutant and the corresponding single mutant within the same target gene. We will clarify this point in the revised manuscript.

      (2) Strains used in this work have only been outcrossed twice, which leaves 25% of mutations. The parent strains with tm and ok alleles were isolated after mutagenesis and are expected to contain thousands of mutations. Two outcrosses imply that several hundred unlinked mutations remain, which weakens the genetic evidence.

      Because most of the data were obtained from double mutants (e.g., sma-6(lf); nlp-10(lf), sma-6(lf); npr-35(lf)), we performed at least one additional round of outcrossing by introducing the single mutants into the BMP mutants. We therefore expect that the background mutation load in these double mutants is lower than 25%. As we plan to do more experiments on the single mutants, we will first increase the number of outcrosses before measuring fat levels.

      (3) More details are needed on the methods related to fluorescence microscopy, especially since most of the manuscript's conclusions rest on quantitative fluorescence. It is important to describe the light source and whether there was any calibration to control for variable fluorescence due to the equipment.

      Thank you. We will do so. All Nile Red imaging was performed on the same microscopic system, which is not a confocal microscope but an upright widefield microscope, which captures the full depth of field along the z-axis (rather than a single optical section). In the revised manuscript, we will expand the fluorescence microscopy methods to describe the illumination source, the acquisition settings, and the measures taken, etc.

      Reviewer #2 (Recommendations for the authors):

      Minor Comments

      (1) The finding that NLP-10 overexpression alone does not produce a strong phenotype in wild-type animals is intriguing. A brief discussion of how this observation fits into the proposed model would be useful for readers.

      We agree with the reviewer that NLP-10 overexpression alone does not produce a strong phenotype in wild-type animals, which is intriguing. We have not yet performed a detailed mechanistic analysis of this phenomenon. We speculate that animals likely possess metabolic homeostatic mechanisms that buffer against perturbations in NLP-10 levels. As R1 suggested, it is also possible that dietary restriction or starvation conditions may broaden the expression range of nlp-10 or its receptor(s). We will discuss this possibility and its relationship to our proposed model in greater depth in the revised manuscript.

      (2) Some figure legends describing complex genetic comparisons could benefit from additional explanatory language highlighting the key conclusion from each experiment. This would improve accessibility of the paper.

      Figure legends will be improved in the revised version.

      Overall Recommendation:

      The manuscript has been substantially strengthened through revision, and the remaining issues are largely matters of clarity and presentation. I am supportive of the paper following minor revision.

      Thank you again for your feedback. Revisions will include updated data and improved wording in future versions.

      Reviewer #3 (Recommendations for the authors):

      (1) dbl-1 mutants are mentioned in the Introduction without explanation. The authors should briefly describe what dbl-1 encodes and how it relates to the BMP pathway studied here.

      We apologize for this confusion and will introduce DBL-1 properly in the Introduction by identifying it as the C. elegans BMP ligand that signals through the SMA-6/SMA-2/SMA-3/SMA-4 pathway.

      (2) Lines 19, 60, and 238: It is unclear what exactly the authors mean by "mutant-specific effects," "mutant-specific phenomenon," and "mutant-specific mechanism."

      We will replace the term “mutant-specific” with alternative wording. By this term, we meant “specific to BMP mutants”, as opposed to a general response to nutrient insufficiency.

      (3) Lines: 56-57 The authors state that "the ADL sensory neurons release neuropeptide NLP-10... to promote the secretion of... FLP18". To make this statement, the authors need to use a neuropeptide secretion assay (e.g., the coelomocyte release assay) to show their claim or tone down the language.

      We will tone down the language since we do not measure peptide secretion directly.

      (4) ADL ablation in the sma-6; nlp-10 double mutant could help support the authors' hypothesis.

      We agree that ADL ablation in sma-6(lf); nlp-10(lf) could in principle provide additional information. However, we do not consider this experiment essential for the revised manuscript. Our main concern is that metabolic regulation is mediated by many peptides with partially redundant and compensatory functions. Therefore, the outcome of ADL ablation in sma-6(lf); nlp-10(lf) would be difficult to interpret unambiguously. We will acknowledge this limitation in the Discussion of the revised manuscript.

      (5) Figure 3D: The authors perform an ADL-specific rescue experiment to show that expression of sma-6 in ADL does not rescue the fat content defect of sma-6 mutants. Because this is a negative result, it is hard to interpret unless the authors first show that the construct is indeed expressed in ADL (e.g., by co-expressing a fluorescent reporter from the same transcript, such as in an operon with sma-6) and, second, that they can rescue the sma-6 phenotype by expression in the pharynx, especially if they want to support the model shown in Figure 3E.

      We will either image ADL neurons expressing srh-220p::sma-6::sl2::gfp, using DiI filling as an ADL landmark, or test whether pharyngeal expression of SMA-6 rescues the phenotype.

      (6) Figure 5G: the figure legend describes a different experiment than the one shown in the figure.

      We will correct the legend for Figure 5G.

      Minor points:

      (1) Line 106: change "verify" to "verified".

      (2) Line 134: change "might have worked" to "might work".

      (3) Line 148: replace the ";" at the end of the phrase with a full stop.

      (4) Figure 5- figure supplement 1E: the title reads "npr-4 is required in flp-10 overexpressed animals". The authors presumably mean "nlp-10-overexpressing animals".

      We thank the reviewer for pointing out these flaws and will make corrections in subsequent versions.

    1. Author response:

      Thanks to the reviewers, reviewing editor and senior editor for their assessment of our manuscript. We summarize and address reviewer comments and suggestions below:

      (1) The granularity of action selection is ambiguous (Reviewers 1 & 3)

      (2) Consider neurons not modulated by movement (Reviewer 1)

      (3) How to interpret ramp-like vs. abrupt changes in pre-movement firing rates (Reviewer 1)

      (4) Population encoding could be considered a form of action selection (Reviewer 3)

      (5) Improve the sample-size and screening of optotagging results (Reviewers 2 & 3)

      (1) The granularity of action selection is ambiguous (Reviewers 1 & 3)

      The reviewers astutely pointed out a critical ambiguity of the original action selection model: on what level are actions differentiated in the basal ganglia? Is it activation of specific muscles, or concerted movements of multiple body parts, or even complex sequences of behavior? Anatomically, the organization of striatonigral input as well as nigrocollicular pathways appear to be highly somatotopic (Foster et al., 2021; Lee et al., 2020), in the sense that there are parallel circuits that separately project to orofacial or skeletomotor regions of the superior colliculus (Benavidez et al., 2021). This might suggest an upper bound for the granularity of action selection in SNr, manifest at the level of tongue/jaw vs. limbs, different directions of reaching, or reaching vs. retraction. We tested these permutations and found little evidence for sign reversals in SNr responses. Nonetheless, one could always parse “action” into even finer components, or combine them into more complex ensembles or sequences of movements. It was exactly this logic that led us to test more and more movements, starting with different directions of reaching and culminating in the unbiased examination of spontaneous movement (Fig. 5, 6, 7). Nonetheless, we of course could not exhaustively exclude all movement possibilities/permutations, and our arguments are limited to the sets of actions that we tested. But we also point out that the granularity argument could be extended ad infinitum, to the point of being practically unfalsifiable! In the end, we will lay this logic out more clearly in the revised Discussion. (On the other hand, it is exactly this “granularity” conundrum that led us away from trying yet another movement paradigm, and toward the idea of examining functional connectivity between the SNr and SC, as outlined below.)

      (2) Consider neurons not modulated by movement (Reviewer 1)

      Reviewer 1 pointed out that unmodulated SNr neurons could be grouped with increase neurons, since they could maintain or increase inhibitory output in order to inhibit unwanted movements. Upon further inspection, we found 56/427 (13%) SNr units decreased firing for reaching but not for licking; conversely, 12/427 (3%) units decrease firing for licking but not for reaching; while 334/427 (78%) units increased firing or were unmodulated for both reaching and licking. In our original analysis excluding unmodulated SNr units, the proportions of units with congruent (86%) vs. incongruent (14%) signs of modulation for reaching and licking did not differ drastically when we included unmodulated units (78% vs. 16%). Nonetheless, this is a valid point, and we will include this in the revised Results and Discussion.

      (3) How to interpret ramp-like vs. abrupt changes in pre-movement firing rates (Reviewer 1)

      Reviewer 1 questioned how the slow ramp-like modulation of SNr firing relates to the disinhibitory gating model. We adopted the self-timed/spontaneous movement task not only to separate sensory vs. motor activity, but also due to clinical observations in Parkinson’s disease that patients are more debilitated for self-initiated rather than cued movements. We observed early pre-movement neural modulation in SNr during self-initiated movements, whereas Mink and Thach (1991) argued that pallidal activation was too late for movement initiation – albeit only in the context of cued movements. Slow ramp-like changes SNr firing does not contradict action selection per se, since modulation of SNr firing might need to reach some threshold level for a desired movement to occur, even in the context of action selection. On the other hand, these ramp-like changes might also represent a generic movement initiation signal without specifying which action to take. We pointed out the existence of ramp-like modulation during self-initiated movements, but the ramp-like nature of SNr modulation is not fundamentally incompatible with the gating model. We will clarify this point in the revised Discussion.

      (4) Population encoding could be considered a form of action selection (Reviewer 3)

      The reviewers also pointed out that while action selection is largely absent in single SNr neurons, licking vs. reaching could be efficiently decoded from population activity. Reviewer 3 reasonably asked: could population encoding be a form of action selection?

      The answer, of course, is yes – but by the same token, any motor area that displays selectivity (motor cortex, thalamus, cerebellum, brainstem, etc.) could be argued to play a role in action selection. So what’s special about the basal ganglia? In this regard, it’s important to re-examine the basis for the action-selection hypothesis. The original model was put forward by Mink & Thach in 1991 to explain the paradoxical observation that most inhibitory pallidal output neurons increase rather than decrease firing during movement. The authors speculated that this increase population could inhibit unwanted movements, while the smaller decrease population could disinhibit the desired movement. The model has been tweaked here and there through the years, but the fundamental core of the idea has persisted, with little supporting evidence, presumably because it provides an explanation for the paradoxical increase neurons – an interesting explanation to be sure. However, if neurons that increase firing do so to inhibit an unwanted movement, then the simplest “other side of the coin” explanation is that they should decrease firing when that same movement is desired. Yet this sign-reversal motif was exceedingly rare among the SNr neurons in our study. Thus the critical question remains: why do so many pallidal output neurons increase firing with movement? We hope that one useful outcome of our study will be to stimulate others to think about pallidal responses outside of the action-selection framework.

      Nonetheless, one could certainly argue that action selectivity is a prerequisite for action selection, and it may be worth asking how the SNr selectivity could contribute to this role. The SNr projects broadly to multiple brainstem and thalamic motor nuclei, which in turn affect specific movements. One could certainly devise wiring schemes whereby SNr outputs is parsed out among those downstream targets to mediate action selection. But these schemes are not exclusive to the SNr; they could pertain to any motor area with selectivity, nor do they provide an explanation for the paradoxical increase neurons. Nonetheless, R3’s thoughts likely reflect those of other readers, and we will try to lay out our logic more clearly in the revised Introduction and Discussion.

      (5) Improve the sample-size and screening of optotagging results (Reviewers 2 & 3)

      We used an optotagging technique to identify SNr neurons projecting to arm vs. orofacial SC and demonstrated that – during both reaching and licking – SNr neurons predominantly increased their inhibitory output regardless of their putative projection target. We think these results have important implications for the role of SNr output. However, the reviewers pointed out some critical limitations of our optotagging approach. Typically, to rule out polysynaptic confounds, light-evoked spikes are expected to have very low latency (typically a few milliseconds, but highly dependent on light power and opsin efficacy). However, it is unclear where the threshold for spiking latency should be drawn. Instead, to rule out polysynaptic confounds in our study, we relied on the fact we observed extremely few (<5%) silenced SNr neurons during optogenetic stimulation of a predominantly GABAergic region. Because SNr neurons send collateral GABAergic projections to other SNr neurons, optogenetic activation of a neighboring neuron should synaptically inhibit (rather than excite) a neuron of interest. Another possible source of contamination would have come from light leaking to into SC, which could have polysynaptically excited SNr neurons through the collicular-thalamic-striatal pathway. In this case, direct pathway striatal projection neurons should also suppress SNr firing. However, we did not observe any light-evoked inhibition among hundreds of putative SNr neurons, perhaps because viral labeling of neurons was sparse enough that polysynaptic inhibition was rare and largely unable to overcome optogenetic excitation. Therefore we did not suspect polysynaptic contamination among our results. Nonetheless, even after we had restricted our analysis to SNr units with low (<median) optogenetic responses latencies, the fraction of SNr units negatively modulated for reaching or licking was still extremely low (4% for reach among putative arm-SC projecting neurons; 8% for lick among putative orofacial-SC projecting neurons). We plan to collect additional data to address concerns regarding the smaller sample size.

      References:

      Benavidez, N. L., Bienkowski, M. S., Zhu, M., Garcia, L. H., Fayzullina, M., Gao, L., Bowman, I., Gou, L., Khanjani, N., Cotter, K. R., Korobkova, L., Becerra, M., Cao, C., Song, M. Y., Zhang, B., Yamashita, S., Tugangui, A. J., Zingg, B., Rose, K., . . . Dong, H.-W. (2021). Organization of the inputs and outputs of the mouse superior colliculus. Nature Communications, 12(1), 4004. https://doi.org/10.1038/s41467-021-24241-2 

      Foster, N. N., Barry, J., Korobkova, L., Garcia, L., Gao, L., Becerra, M., Sherafat, Y., Peng, B., Li, X., Choi, J.H., Gou, L., Zingg, B., Azam, S., Lo, D., Khanjani, N., Zhang, B., Stanis, J., Bowman, I., Cotter, K., . . . Dong, H.-W. (2021). The mouse cortico–basal ganglia–thalamic network. Nature, 598(7879), 188194. https://doi.org/10.1038/s41586-021-03993-3 

      Lee, J., Wang, W., & Sabatini, B. L. (2020). Anatomically segregated basal ganglia pathways allow parallel behavioral modulation. Nature Neuroscience, 23(11), 1388-1398. https://doi.org/10.1038/s41593-020-00712-5

    1. Author response:

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      This study describes targeting Poltheta Helicase with a new drug RP-3467. The properties of the drug and a clinical response in a gBRCA1 Ovarian Cancer Patient with a mutation in TP53BP1 are described.

      Strengths:

      This is an important and interesting set of observations.

      We thank the reviewer for their positive assessment and appreciate their recognition of the significance and novelty of our findings.

      Weaknesses:

      (1) The response of the patient with a TP53BP1 mutant tumor is of interest but requires more clarification before solid conclusions can be drawn. The presence of the TP53BP1 mutation after but not before olaparib treatment is suggestive of selection, but in the absence of demonstration of a biallelic loss, this is conjecture. It could be a co-selected passenger mutation. The authors should report the TP53BP1 variant allele fraction, LOH, and orthogonal validation should be performed by targeted deep sequencing or ddPCR. This would establish the prevalence before and after selection and enhance the interpretation of the functional effects of the mutation observed.

      We thank the reviewer for this important comment. We agree that identifying a TP53BP1 mutation after olaparib treatment does not, by itself, establish whether the mutation was directly selected under therapeutic pressure or represents a co-selected event, and we do not intend to make that distinction. Instead, we report that whole-genome sequencing (WGS) identified the TP53BP1 mutation in the tumor collected at the second debulking surgery. Importantly, an additional biopsy obtained at disease progression during the POLAR trial revealed a TP53BP1 variant allele frequency of 77%, with FACETS analysis identifying copy-neutral loss of heterozygosity (CN-LOH). These findings (new data in the paper) provide additional evidence consistent with biallelic inactivation of TP53BP1 and support the biological relevance of this alteration. Nevertheless, we acknowledge that these observations do not establish whether TP53BP1 loss directly drove acquired olaparib resistance, and we clarified this distinction in the revised manuscript.

      (2) To further strengthen the proposed mechanism, the authors should consider knocking in the mutation (or a similar LOF mutation) into an appropriate cell line and establish resistance to olaparib and sensitivity to the combination, as well as each drug individually. This will address the latter question of whether it is the poltheta inhibitor or the combo that is responsible for the clinical response.

      We thank the reviewer for this thoughtful suggestion and agree that establishing the contribution of TP53BP1 loss to treatment sensitivity is important for interpreting the clinical response. We would like to highlight, however, that this genetic relationship has been investigated in several published studies. Genetic depletion of POLQ has been shown to be synthetic lethal with 53BP1 or Ku70 deficiency (Wyatt et al., Molecular Cell, 2016; Feng et al., Nature Communications, 2019). More directly, Zatreanu et al. (Nature Communications, 2021) demonstrated that loss of 53BP1 or Shieldin components (SHLD1/SHLD3) in BRCA1-deficient cells confers resistance to olaparib while retaining sensitivity to the POLθ inhibitor ART558 as a single agent. These findings are further supported by Krais et al. and Ronson et al. (Nature Communications, 2023), who demonstrated POLθ dependency in BRCA1/53BP1-deficient backgrounds. Collectively, these studies provide strong genetic and pharmacological support for our proposed mechanism and suggest that POLθ inhibition itself may have contributed substantially to the observed clinical response. While we acknowledge that the relative contributions of RP-3467 and olaparib cannot be definitively distinguished in this patient, we believe that the existing literature provides a strong mechanistic foundation for interpreting this clinical observation, without necessitating additional genetic modeling in the context of the present study.

      (3) In the animal experiments, "synergy" is overstating the situation. Without an interaction analysis, this is an enhanced combination activity. Also, several of the animal experiments have a small N. It would be better to show the growth of tumors in individual mice.

      Although we believe that minimally in BRCA2-deficient CDX models (e.g. Fig. 2a,b) the term synergy is appropriate (no/minimal single-agent activity of RP-3467 and tumor regressions in combination), we replaced the term ‘synergy’ with ‘enhanced combination activity’ due to lack of a formal interaction analysis. Data from individual animals are included as Source Data.

      (4) The authors propose that Poltheta inhibition could prevent the emergence of reversion mutations. This is not addressed in the paper, and if they want to suggest this, they should provide some evidence

      We thank the reviewer and agree that the manuscript presents no data bearing on reversion mutations. The discussion should not have implied otherwise. We have rewritten relevant paragraph so that the idea is presented explicitly as an untested hypothesis arising from the microhomology signatures reported at reversion breakpoints by others.

      Reviewer #2 (Public review):

      Summary:

      The authors set out to assess the in vitro potency of a new POLQ helicase inhibitor, assess its in vitro BRCA1/2 synthetic lethal properties, and confirm how it performs in vivo in PDX and cell line xenografts. The authors also show an anecdotal patient response with a PARP inhibitor + POLQ inhibitor combination.

      Strengths:

      This is a novel POLQi of the helicase activity. The anecdotal clinical response in a heavily pre-treated patient is interesting.

      We thank the reviewer for their positive assessment and are pleased that they recognize the novelty of targeting the POLθ helicase activity and the potential clinical significance of the response observed in a heavily pretreated patient.

      Weaknesses:

      Most of these issues could be addressed by changes to the main text, i.e. by the authors describing limitations/caveats to interpretation, etc.

      (1) The clinical anecdote is interesting but underanalyzed. It's difficult, though, to know one way or the other whether the PARPi+ POLQi treatment effect (only partial response) has anything to do with the 53bp1 mutation. There is a causative sign that the 53bp1 mutation could be the cause of PARPi resistance (the increase in 53bp1 mutation allele frequency in PARPi-naïve vs PARPi-resistant tumors), but no similar sign to show that the 53bp1 mutant tumor clone is targeted by POLQi treatment. For example, does 53bp1 mutation allele frequency fall in ascites or ctDNA during the course of treatment, or is the 53bp1 mutation lost in a tumor taken at the end of treatment?  

      We thank the reviewer for this suggestion. While longitudinal monitoring of the TP53BP1-mutant clone would be informative, such data are unavailable. A biopsy obtained at progression on the POLAR trial revealed a TP53BP1 variant allele frequency of 77%, with copy-neutral LOH by FACETS analysis. Importantly, extensive preclinical evidence establishes synthetic lethality between 53BP1 deficiency and POLQ inhibition (Wyatt et al., 2016; Feng et al., 2019; Zatreanu et al., 2021; Krais et al., 2023), supporting a contribution of POLθ inhibition to the clinical response. Nevertheless, determining whether the response was driven by POLθ inhibition alone or its combination with olaparib will require evaluation in a larger clinical cohort.

      (2) Although the relevant work is cited, the authors should be more explicit in the introduction and state that there is already evidence from 2 papers that Combined loss of BRCA1 and 53bp1 causes enhanced sensitivity to small-molecule POLQ helicase or polymerase inhibitors.

      Agreed, and adopted. We changed the introduction to state this prior evidence explicitly on first mention, naming both studies and specifying that the effect has been demonstrated for inhibitors of Polymerase theta.

      (3) Figure 4. Not exacerbating existing PARPi myelosuppression is great, but the authors have to acknowledge that the myelosuppression is still present when POLQ+ PARPI is used. Single-agent POLQi doesn't give myelotoxicity, but it also does not give strong anti-tumor efficacy. i.e. it would be fair for the authors to acknowledge this.

      We agree with the reviewer and have revised the text to more accurately reflect these findings. While POLθ inhibition does not exacerbate PARPi-associated myelosuppression, it does not eliminate the hematologic toxicity of PARPi treatment. We also acknowledge that POLθ inhibitor monotherapy has limited antitumor efficacy in the models tested, highlighting the importance of combination treatment and the need to balance efficacy with tolerability.

      (4) The increase in reticulocytes when mice are treated with POLQi could be a sign that there is an effect on myeloid lineages, but the animals are responding by increased production of this young myeloid lineage. Alternatively, this reticulocyte increase could drive or be a sign of pathology (polycythaemia vera, etc.). It would be good to see a commentary on this in the Discussion.

      We agree, and updated the language in Results, page 9, to reflect this possibility.

      (5) Re Figure 4. A therapeutic advance would be to see that, compared to other PARPi combinations such as platinum + PARPi or temozolomide + PARPi, a POLQ + PARPi combination doesn't give the same myelosuppression that these combinations do (by analogy, combined platinum + PARPi gives curative responses in mice but also wipes out the adaptive immune system). The authors need to add data showing the platinum+ PARPi positive control, or at the very least add a limitations of the study section to the manuscript to explain this fairly.

      We thank the reviewer for this suggestion. The substantial myelosuppression associated with combining PARP inhibitors with platinum-based chemotherapy or temozolomide has been well documented in preclinical and clinical studies, including the references cited by the reviewer (Rajan et al., 2012; PMID: 24827126). We agree that a direct comparison would be informative. However, given that these toxicities are already established in the literature, we believe that repeating these experiments is not essential to the present study. We have instead clarified that our findings demonstrate that RP-3467 does not exacerbate olaparib-associated myelosuppression under the conditions tested, without implying that the combination is free of hematologic toxicity or has been directly demonstrated to be safer than other PARPi combinations.

      (6) Figure 2 might give the impression that the new POLQi gives a similar, if not greater, BRCA2 synthetic lethal effect than a PARPi (e.g. 2d-f). It would help readers to see the full saruparib and olaparib dose-response curves, not (as per 2 A, B, C) just the single point estimates.

      The ZIP synergy matrices in Extended Data Figure 2 were acquired across a full concentration grid for both agents, and therefore already contain the complete single-agent dose–response for olaparib and for saruparib in each line.

      (7) Why was DOTC42510 not profiled for PARPi?

      We apologize for the poor signposting that made this data hard to find. DOTC24510 cells were profiled with olaparib: the combination growth data appear in Extended Data Figure 2c and the corresponding ZIP synergy plot in Extended Data Figure 2d. The main-text sentence reporting the olaparib combination does name DOTC24510 alongside the two colorectal lines, but cites only the main-figure panels, which do not include this line.

      (8) Figure 2f shows error bars on an n=2 dataset - one cannot estimate variance from only an n=2 dataset range.

      We thank the reviewer for pointing this out. We agree that an n=2 dataset is insufficient for a reliable estimate of variability. We revised Figure 2f to show the data points without error bars and clarify the sample size in the figure legend.

      (9) Is there a statistical analysis on Figure 2G?

      The data originate from two independent experiments, so we did not consider it appropriate to perform a formal statistical analysis. We note, though, that the data were consistent between the two replicates and that a robust difference was observed between the combination and single-agent arms.

      (10) Figure 3. Olaparib 25 mg/kg QD is well below the MTD in mice. This makes the olaparib response in HCT116 BRCA2 k/o xenografts look modest when compared to the combinations.

      We used 25 mg/kg to highlight the strong combination potential between RP-3467 and olaparib. That said, Fig. 3b shows that even when a PARP inhibitor (saruparib in this case) is used at its maximally efficacious dose (PMID: 35929986), the RP-3467 combination has the potential to outperform PARPi monotherapy.

      Reviewer #3 (Public review):

      Summary:

      The authors seek to validate the effectiveness of an inhibitor of the Pol theta helicase-like domain ATPase activity in its ability to ablate MMEJ activity in cell line models. They then confirm the inhibitor is synthetic lethal in a variety of BRCA1/2 deficient cancer models (and one PALB2 model). Finally, they report apparent effectiveness in treatment of a single patient that failed therapy with PARPi due to 53BP1 deficiency, a hypothesized special use-case for targeting pol theta.

      Strengths:

      It is a clear bench-to-bedside translation of mechanistic-oriented basic science to a clinical therapy. The experiments are largely rigorously performed. The approaches employed are impressively diverse, from in vitro to cell-line model, to preclinical model, to clinical application. The interpretations made are well supported by the available data.

      We sincerely thank the reviewer for their thoughtful and encouraging assessment of our work. We are particularly pleased that the reviewer recognizes the translational significance of the study, the breadth and rigor of the experimental approaches, and the strength of the conclusions. We appreciate these positive comments and the constructive suggestions, which have helped us further strengthen the manuscript.

      Weaknesses:

      The addition of a few missing details would improve the usefulness to the reader. Additionally, the rationale behind some approaches could be clarified.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      In this study, the authors identified transcription factor combinations capable of inducing retinal neuronal programs in cultured fetal human retinal pigment epithelial (RPE) cells. Using a pooled screening strategy, single-cell RNA sequencing, lineage barcoding, and immunohistochemical analyses, they identified ASCL1 and NEUROD1 as an effective combination for inducing retinal neuron-associated transcriptional states. This work aims to advance the development of therapeutic approaches for retinal regeneration by exploring the plasticity of RPE cells.

      Strengths:

      A major strength of the study is the comprehensive experimental design. The combination of transcription factor screening, lineage tracing, single-cell transcriptomics, and molecular validation provides a detailed characterization of the cellular responses to reprogramming factor expression.

      Weaknesses:

      All experiments were performed using fetal human RPE cells. Because fetal RPE remains relatively immature and retains proliferative capacity, it remains unclear to what extent the observed responses reflect true reprogramming of differentiated RPE cells versus activation of developmental plasticity already present in fetal tissue. The absence of adult human RPE controls limits assessment of the generality and translational relevance of the findings.

      We agree with the assessment that the reprogramming of fetal RPE due to its potential fate plasticity poses a different challenge than the adult. In fact, embryonic chick RPE will only undergo neural trans differentiation when treated with FGF before embryonic day 4. Therefore, we specifically focused on RPE at early developmental stages for our experiments. It is interesting in that light that the ages of fetal human retina are far more advanced in their development than the E4 chick, yet still have the capacity for neural reprogramming; while it will be interesting to explore in the future how long during fetal development this plasticity exists, we were limited by the fetal ages that were available to us. Moreover, the facility that supplied our tissues (Birth Defects Research Lab) are no longer able to use NIH funds to distribute fetal tissues as they have for the last >40 years, making any future studies with primary fetal tissues much more difficult.

      Reviewer #2 (Public review):

      Summary:

      This is an interesting study that explores how human RPE could be used as a source for new retinal neurons. This is a welcome addition to the field of retinal regeneration, which is currently focused almost exclusively on the regenerative capacity of Müller glia cells. The line of inquiry is firmly rooted in findings from amphibian and embryonic chick model systems and advances a fetal human retina RPE-based screening system as a rich resource for insights into human RPE biology, including as a potential stem cell source.

      The authors investigate the potential of fetal human RPE cells to be reprogrammed into retinal neurons using overexpression of pro-neural factors. While this is a critical knowledge gap in the field of retinal regeneration with significant promise for developing regenerative therapies, several methodological concerns impact the interpretation of results. Firstly, while the authors sought to evaluate factors that enhance RPE reprogramming when co-expressed with ASCL1, nearly all co-expression constructs tested failed to achieve appreciable expression of ASCL1, leaving a central hypothesis of this study largely untested (Major concern 1). Second, although the authors were able to detect a cluster of photoreceptor-like cells in their screen, they were unable to identify which reprogramming construct generated this cluster (Major concern 2). Finally, an essential control that definitively demonstrates the value of combinatorial transcription factor reprogramming is missing (Major concern 3).

      In summary, the authors establish a valuable new paradigm for culturing and reprogramming fetal human RPE, and even more importantly, demonstrate successful reprogramming to neural fates. However, the discussion and interpretation of results needs to be modified significantly to make it clear that (i) the outcome of many co-expression paradigms remains effectively unknown/untested due to failed over-expression of ASCL1, and that (ii) the reprogramming construct giving rise to photoreceptor-like cells could not be conclusively identified from their initial screen.

      Strengths:

      (1) Powerful new screening system advanced for exploring the regenerative potential of human fetal RPE cells.

      (2) Co-expression vector system for testing additive effects of proneural transcription factors.

      Weaknesses:

      Major concerns:

      (1) The authors executed a screen for combinations of factors that can enhance ASCL1-mediated reprogramming of RPE into retinal neurons. However, the expression level of ASCL1 was remarkably low in virtually all co-expression paradigms (see Figure 3C). Notably, the reprogramming combination with the highest potency (ASCL1 + NEUROD1) was also the one exhibiting the highest level of ASCL1 expression. The "failed" reprogramming of most of the co-expression constructs (ASCL1+LMO1, ASCL1+EZH2, and ASCL1+RAX2) is potentially a false negative resulting from low transgenic expression of ASCL1.

      We agree with the reviewer that insufficient ASCL1 expression in the combinations might have led to lack of reprogramming, representing a false-negative result. We do not rule out that individual, rather than pooled, expression vectors of the “failed” varieties might prove effective. A future version of such a screen might need a control to test proper vector functionality of each member in the pool. However, the expression of ASCL1 alone from a vector in the same pool worked well. Additionally, the expression of ASCL1 from the ASCL1-NEUROD1 vector was not nearly as high as from ASCL1 alone and still led not only to reprogramming but also to a shift in the gene expression landscape as seen in 4D. This shift is consistent across experiments and vector constructs.

      (2) The authors' interpretation is that the overexpression of NeuroD1 and Ascl1 generated a new cluster that expressed markers of photoreceptors such as RXRG and RCVRN (see Figure 3D). However, there does not actually appear to be any overlap between the ASCL1+NEUROD1 cluster (orange dots, left panel) and the cells expressing markers of photoreceptors (yellow/green/purple? /black? dots, right panel; yellow being ASCL1-EZH2, green being ASCL1, purple being ASCL1-and black being control - though color coding here is admittedly somewhat confusing). Thus, the photoreceptor-like cluster of interest actually seems to correspond to gray cells that were unmapped/exposed to an unknown programming cocktail. So, it remains completely unknown which reprogramming construct generated this cluster.

      We apologize for the confusion in Figure 3D, which stemmed from lack of proper labeling.

      The right panel shows the expression of photoreceptor genes in a feature plot, not the vector assignment. The color code is different between the left most panel (which shows vector assignment) and the other two panels (which show gene expression). To make this more clear, we have now separated this into a panel D and a panel D’, and added a caption as well as a scale bar for the D’ panel.

      The reviewer is correct that the farthest subcluster with highest RCVRN/RXRG expression was not assigned ASCL1-NEUROD1 identity. The inherent sparsity of scRNAseq experiments and the small size of that particular cluster made definite identification challenging. Furthermore, vector assignment is tied to vector and thus barcode expression. It is conceivable that as cells matured towards a photoreceptor-like cells, they silenced the vector insertion locus but initiated marker expression. Additionally, these photoreceptor-like cells were assigned to the same cluster (neur, Fig. 3B) as the positively identified ASCL1-NEUROD1 cells by unsupervised clustering, express NEUROD1 (Suppl. Fig. 2D) and seem to follow the same trajectory. This suggests that they stem from ASCL1-NEUROD1 overexpression. Moreover, the follow-up experiments showing the expression of the relevant genes in the reprog4 cluster (Fig. 4) and the corresponding stainings (Fig. 5) provide evidence that ASCL1-NEUROD1 overexpression causes expression of RCVRN.

      (3) To conclusively establish the additive role of NEUROD1 in reprogramming, it would be prudent to compare ASCL1 + FA directly to ASCL1+NeuroD1+FA. This control was not included but is needed for a more complete interpretation of results.

      We thank the reviewer for this suggestion. Such a control would indeed clarify the role of FA treatment on reprogramming with ASCL1 alone. However, to address the additive role of NEUROD1, we presented in this study the comparison of ASCL1-NEUROD1 with ASCL1 alone. Even without the addition of FA, we noted a shift in expression pattern (Fig. 4D) and the formation of neurogenic clusters (Suppl.Fig. 4B) with the addition of NEUROD1. Moreover, as noted above, it is no longer possible for us to obtain tissue from the BDRL to carry out additional experiments at this time.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      (1) The antibody section should mention the dilution used and how primary antibodies were validated (in the current study, or cited from previous literature).

      We have added the dilutions of the used primary antibodies. They are targeted against well-known markers in the field and have been validated by our lab and others.

      (2) A supplementary table summarizing and comparing pro-photoreceptor genes detected vs functional photoreceptor genes would be helpful to readers.

      We think that the heatmap in 4C provides a good overview of detected genes of interest.

      (3) The manuscript would benefit if figures have scale bars and marker labels above or below the images, but not superimposed (so as not to block the gene signal in some cells). (Figure 1C).

      We changed the labels in 1C and added a scale bar to be more consistent with the other figures in the manuscript.

      (4) Figure 2B and 5B (neurogenic dome) are missing scale bars.

      We added scale bars in 2B and 5B as well as the supplemental figures.

      (5) Plasmid design: dual promoters without insulators should be addressed (MCV and Ef1a). If possible, an RPE65-specific promoter to drive ASCL1-NEUROD1, to show that short temporal expression is not capable of inducing the desired reprogramming.

      We agree that an RPE-specific promoter would not only gauge the strength and duration that is necessary for reprogramming, but would also support translational efforts. While we have addressed that question somewhat with the HES1-ASCL1 construct in our initial experiments, more in-depth investigation to choose an optimal promoter will be necessary in the future.

      Reviewer #2 (Recommendations for the authors):

      (1) The first sentence of the abstract is identical to the third sentence of the introduction. Rephrase to avoid redundancy. There are currently a few promising approaches for treatment: for example, gene therapy to augment or replace mutated genes has proven successful in preclinical studies, and some of these therapies are moving towards the clinic [2], [3].

      We rephrased the sentence to:

      Current developments in gene therapy, which aims to deliver healthy copies of mutated genes, show promising results and are increasingly becoming available in the clinic.

      (2) Panel 1C would be more informative if images were enlarged/zoomed in ~4x or higher.

      We have enlarged the panels as requested by the reviewer.

      (3) Panel 1D reports size/area differences for cultures at a variety of time points. Data should thus be represented as a line chart to reflect whether cell size is changing over time, rather than pooling data points from disparate time points into a single group.

      We agree that such a chart would provide a measure of RPE maturation over time; however, our focus is the relationship between cultured and native RPE. As there seems to be little spread in the measurements between ages, and the range of ages between cultured and native RPE is comparable, we believe that the current chart represents a valid visualization.

      (4) Panel 2D would be clearer if cluster labels were moved to the top of the figure (such that they sit above the columns corresponding to those clusters). It could be further clarified by adding category labels to the marker genes (i.e., RPE markers, ascl1 targets, Neural markers, etc.).

      We thank the reviewer for this suggestion. We shifted the cluster labels and created new labels for the gene groups.

      (5) No comma necessary here: Using transcription factor binding site analysis on these peaks, revealed an enrichment of members of the ETS family like ELK1/4 and ETV1/4.

      Thank you for your attention to detail. We have removed that comma.

      (6) Add dashed box to Panel 3D to indicate region of detail displayed in panels to the right (as was done in Panel 3C).

      We have added a dashed box in panel 3D.

      (7) Distracting typos in the legend of Figure 3.

      We have corrected the typos.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      The authors used FBDD screening to identify numerous compounds interacting with the ORF9b dimer. They expanded the original fragment hit, soaked the derivatives into the crystals and confirmed their binding poses, and showed that the derivatives bind the target with higher affinity. The authors further targeted the ORF9b binding site on TOM70, and used a fluorescence polarization-based (FP) assay to screen a compound library and obtained several hits. Structure-activity relationship (SAR) optimization yielded hit analogs that have higher binding affinity to TOM70.

      Strengths:

      (1) The study adopted novel drug design strategies, including stabilizing ORF9b homodimer to prevent it from binding TOM70, and blocking ORF9b from binding TOM70 by screening compounds that compete with ORF9b for binding TOM70.

      (2) The work established a feasible high-throughput screening assay. This FP-based assay screened ~50,000 compounds, from which two hit compounds were further optimized to yield analogs with higher binding affinity.

      We thank reviewer #1 for their thoughtful assessment of our work and their constructive feedback.

      Weaknesses:

      (1) The study lacks functional assays to evaluate whether the ORF9b-stabilized compounds or TOM70 binding compounds could affect IFN inhibition caused by ORF9b or virus infection.

      We thank reviewer #1 for their feedback on this subject. We agree that cell-based assays measuring the impact of these compounds on IFN stimulation/suppression would be a valid next step. We have expanded the discussion section to include potential future experiments that could be conducted to probe this:

      “Although we have not assessed the permeability of these compounds and their ability to restore IFN in the context of cell-based assays, one way this could be accomplished is by adapting a previously used reporter cell line. Specifically, this assay uses a reporter cell line that has a Lucia reporter under the control of the IFN-β/ISG56 promoter that is expressed upon mock infection with synthetic dsRNA. When WT Orf9b is co-transfected with the reporter, IFN is suppressed, and, we have shown that phosphomimetic mutants of Orf9b that block its interaction with Tom70 restores IFN signaling. If these compounds are sufficiently permeable, then, for the lipidated-compounds targeting the Orf9b homodimer, we would expect the Orf9b monomer: homodimer equilibrium to shift towards the homodimer due to the stabilizing effect these lipidated-compounds have on the homodimer conformation leading to an increase in IFN signaling. Similarly, for compounds targeting Tom70, we would expect that these compounds block the Orf9b monomer from binding to Tom70 to produce a similar effect.”

      (2) There is a lack of experimental evidence to reveal the binding mode of lipidated-compounds with ORF9b homodimer.

      - We thank reviewer #1 for their feedback. We agree that we were unable to provide direct evidence that our lipidated-compounds are bound to the homodimer through the central lipid-binding channel. Experimental structures of our compounds bound to the Orf9b homodimer would have strengthened our functional studies, however, as we described in the manuscript pertaining to our initial crystallographic fragment screen:

      “Although we have shown that it is possible to refold the Orf9b homodimer to eliminate the lipid from the central channel, we found that apo-Orf9b homodimer crystals were far less tolerant to DMSO and on average diffracted to resolutions worse than 2.5Å. Importantly, we found that microseeding helped increase crystal reproducibility and yielded larger crystals on average. Therefore, for our crystallographic fragment screening campaign we elected to use the lipid-bound protein to identify additional potential binding sites that could be exploited to stabilize the Orf9b homodimer.”

      - We did undertake efforts to co-crystallize our lipidated-compounds with refolded apo-Orf9b homodimers but were unable to generate crystals of sufficient quality to collect X-ray data. Therefore, we relied on both our fluorescence polarization assay and prediction models like Chai1 to investigate if the expected behavior could be recapitulated. We felt this was reasonable for three reasons.

      - First, as we explain in the discussion, none of these compounds or structures were publicly available for models like Chai1 to train on which prevents data leakage:

      “None of these structures were publicly available on the PDB prior to these structural predictions, therefore, they were not available for Chai1 to train on. The placement of the lipidated-analogs in the central channel was in line with the anticipated binding mode, albeit, with discrepancies between the predicted and structurally observed portions of the analog compounds.”

      - Second, as we outlined in the fluorescence polarization assay, we tested these compounds in two control experiments that investigated whether the changes in FP signal over time could also be explained by the compounds binding to Tom70 directly, or, by acting on the obligate Orf9b monomer which was generated by truncating the N and C-termini:

      “We first considered whether the lipidated-analogs had any binding activity for Tom70 on its own and whether changes in FP signal were due to binding to the Orf9b homodimer. We tested the compounds on their own in the presence of the pre-equilibrated Tom70:Orf9b-FITC complex and observed no significant decrease in FP signal indicating that the lipidated-analogs do not directly bind to Tom70 to drive a decrease in FP signal (Figure 2—figure supplement 2A). We next tested whether these compounds acted on the Orf9b homodimer specifically or if they could inhibit the Orf9b monomer from binding to Tom70 by incubating compounds with an Orf9b peptide that acts as an obligate monomer. When chasing with the pre-equilibrated Tom70:Orf9b-FITC complex, we observed no significant differences in kinetics of Orf9b peptide binding compared to the peptide on its own which showed a fast single-exponential kinetic decay in signal suggesting that these compounds do not act on the Orf9b monomer to inhibit binding to Tom70 (Figure 2—figure supplement 2B)”

      (3) There is a lack of experimental evidence to reveal the binding mode of HTS hits or analogs for TOM70.

      We thank reviewer #1 for their feedback. We agree that experimental structures of our HTS compounds bound to Tom70 would provide more insights into how these compounds bind to Tom70 (and their precise location) in ways that the predicted complexes from models like Chai1 were unable to do. At the time of drafting this manuscript, we had not yet identified suitable conditions for structurally resolving Tom70 with our HTS compounds. Therefore, we elected to rely on two orthogonal methods of predicting where our HTS compounds are bound to probe whether the predicted binding sites could plausibly block Orf9b from binding. In the time since releasing this manuscript, one group had been able to crystallize apo-Tom70 which may serve as a suitable platform for future structural studies investigating these compounds and their exact binding mode to Tom70 to enable structure-guided optimisations of these initial hits.

      (4) Overall, none of the compounds shown in the paper have promising potency warranting further development; their binding affinity is limited to the micromolar range.

      We thank reviewer #1 for their feedback. We agree that these compounds should be viewed as starting points for potential future optimization on targets where there were no previous existing ligands. The molecules serve to validate that it is possible to develop small molecules that target Tom70’s C-terminal domain which may be relevant to future studies investigating Tom70’s biology.

      Reviewer #2 (Public review):

      Summary:

      The authors investigate chemical strategies to disrupt the interaction between the SARS-CoV-2 accessory protein Orf9b and the host mitochondrial receptor Tom70, an interaction implicated in suppression of type-I interferon responses. They employ two discovery approaches: a crystallographic fragment screen against the Orf9b homodimer and a high-throughput fluorescence polarization screen for compounds that compete with Orf9b binding to Tom70. The study identifies fragment-binding hotspots on Orf9b, develops lipidated analogs that stabilize the Orf9b homodimer, and discovers Tom70-binding compounds with low micromolar activity that inhibit Orf9b binding in vitro.

      Strengths:

      An impressive amount of work using a variety of complementary approaches and methods to validate binding (FP, SPR, and computational modelling and SAR). The combination of crystallographic fragment screening on Orfb9 and HTS on Tom70 provides two independent routes for perturbing the Orf9b-Tom70 interaction. The structural work seems to be of very high-quality. The fragment campaign is extensive, yielding a substantial number of fragment-bound structures and identifying biologically meaningful binding hotspots on Orf9b.

      Finally, the screen results in reporting useful chemical starting points. Although potency remains modest, the study provides tractable scaffolds and a clear framework for future optimization.

      We thank reviewer #2 for their thoughtful assessment of our work and their constructive feedback.

      Weaknesses:

      General comment:

      (1) Although there is already an incredible amount of data presented, one limitation of this study is the lack of cellular validation - do these drugs enter cells, restore interferon signalling, reduce viral loads, or alter Orfb9 localization?

      We thank reviewer #2 for their feedback. See also the feedback from Reviewer 1. We have not assessed the permeability of these compounds in the context of cell-based assays and IFN signaling and agree that cell-based assays measuring the impact of these compounds on IFN stimulation/suppression would be a valid next step. We have expanded the discussion section to include potential future experiments that could be conducted to probe this:

      “Although we have not assessed the permeability of these compounds and their ability to restore IFN in the context of cell-based assays, one way this could be accomplished is by adapting a previously used reporter cell line. Specifically, this assay uses a reporter cell line that has a Lucia reporter under the control of the IFN-β/ISG56 promoter that is expressed upon mock infection with synthetic dsRNA. When WT Orf9b is co-transfected with the reporter, IFN is suppressed, and, we have shown that phosphomimetic mutants of Orf9b that block its interaction with Tom70 restores IFN signaling. If these compounds are sufficiently permeable, then, for the lipidated-compounds targeting the Orf9b homodimer, we would expect the Orf9b monomer: homodimer equilibrium to shift towards the homodimer due to the stabilizing effect these lipidated-compounds have on the homodimer conformation leading to an increase in IFN signaling. Similarly, for compounds targeting Tom70, we would expect that these compounds block the Orf9b monomer from binding to Tom70 to produce a similar effect.”

      (2) The logic of locking Orfb9 as a dimer is that the monomer binds Tom70 - thus, a more stable dimer means less monomer. In Figure 2, the Orfb9 homerdimer stabilization by compounds should reduce binding affinity to Tom70. A direct binding experiment measuring reduced Tom70 binding with compound treatment would better strengthen this claim.

      We thank reviewer #2 for their observation and agree that compounds targeting the Orf9b homodimer conformation should block binding to Tom70 by preventing Orf9b homodimer dissociation into Orf9b monomers. As schematized in Figure 2D, we described how our fluorescence polarization assay measures the binding of Orf9b to Tom70. It provides insight into how compounds that bind to the Orf9b homodimer may slow the rate of homodimer dissociation. In addition, we have previously demonstrated in a separate publication that there are clear differences in the Orf9b homodimer dissociation kinetics when using either lipid-bound or lipid-free Orf9b homodimers as the competitor due to the stabilizing effect the lipid has on the homodimer conformation.

      Reviewer #3 (Public review):

      Summary:

      This paper attempts to and succeeds in demonstrating that Orf9b is able to bind small molecules using X-ray fragment screening, SPR and FP assays. Exploration of sites from the fragment screening is performed along with fragment linking with inter-dimer lipid moieties.

      Strengths:

      The experimental work looks strong and well performed. The interpretation of the data is appropriate and was often validated through orthogonal methods and follow-up compounds. The use of Tom70 to find binders that might disrupt interactions between Orf9b and Tom70 is elegant.

      Weaknesses:

      The use of Chai-1 to predict co-folded structures with binding molecules was not properly described - no mention of this in the methods. It was not commented on whether the compounds which were found were attempted to be co-crystallised. If they were but negative data was collected (didn't crystallise, didn't diffract or no additional density was found), then this needs to be stated.

      We thank reviewer #3 for their feedback. We have revised the manuscript to clearly point out that beyond our initial attempts to crystallize apo-Orf9b homodimer to enable fragment soaking, we also attempted to both soak our lipidated-compounds into apo-Orf9b homodimer crystals as well as co-crystallize the compounds which did not yield crystals.

      “We attempted two strategies of crystallizing our lipidated-compounds with the apo-Orf9b homodimer to structurally resolve the complex. First, we attempted to soak our compounds into apo-Orf9b homodimer crystals but observed poor tolerance to DMSO which quickly disintegrated the crystals after minutes. Second, we attempted to co-crystallise the lipidated-compounds after refolding the Orf9b homodimer to generate apo-Orf9b homodimers but could not identify conditions that yielded crystals upon re-screening.”

      We have also revised the methods and materials section to better explain the use of Chai1 to co-fold both Orf9b and Tom70 with their respective compounds.

      “Chai1’s web server was used for co-folding either Orf9b or Tom70 with their respective hits. For the Orf9b homodimer, the sequence for a single chain was supplied to represent chains A and B in the homodimer and the ligands were supplied as SMILES strings. In the case where two copies of the ligand were investigated, the number of copies of the ligand was increased to two. Co-folding was performed using MMSeqs2 for the MSA and template searching to ensure the correct folding of the homodimer conformation. Tom70 co-folding was performed by supplying the sequence for hTom70 as a single chain and the compounds as SMILES strings. Co-folding was performed using MMSeqs2 for the MSA with template searching.”

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      (1) It is disappointing that the authors screened binders for ORF9b homodimer, identified hits and derivatives binding at sites 1 & 2, measured the binding affinity to the target, but found no effects on stabilizing ORF9b homodimer. The FP competition assay was used to assess the efficacy of the compounds; maybe the authors could use alternative methods like Thermal Shift Assay (TSA) assays to detect some subtle changes in stability.

      We thank the reviewer for their comments and agree that the lack of stabilizing activity observed for the site 1 and 2 analogs was disappointing. However, we do feel that the lipid-binding central channel may be a viable alternative site target that may also yield insights into the role of lipid binding in Orf9b biology. We agree that orthogonal methods such as TSA could be insightful for probing the stabilizing effects of the compounds on the Orf9b homodimer.

      (2) To better illustrate the results of the FP kinetic assay to investigate whether lipidated-compounds binding to the Orf9b homodimer had effects on the stability of the Orf9b homodimer and Orf9b-Tom70 equilibrium, I recommend moving the results shown in Supplemental Figure 4 to a main figure and merging these results with Figure 2CD.

      We think that the eLife publication platform provides appropriate visibility for the supplementary figures and that Figure 2D does the best job of illustrating the effects on kinetics for the initial reader.

      (3) Have the authors tried to co-crystallise their top-rated lipidated-compounds with ORF9b homodimer to see where the lipid part of the compound could extend into the central channel of ORF9b homodimer?

      We have revised the manuscript to clearly point out that beyond our initial attempts to crystallize apo-Orf9b homodimer to enable fragment soaking, we also attempted to both soak our lipidated-compounds into apo-Orf9b homodimer crystals as well as co-crystallize the compounds which did not yield crystals.

      “We attempted two strategies of crystallizing our lipidated-compounds with the apo-Orf9b homodimer to structurally resolve the complex. First, we attempted to soak our compounds into apo-Orf9b homodimer crystals but observed poor tolerance to DMSO which quickly disintegrated the crystals after minutes. Second, we attempted to cocrystallize the lipidated-compounds after refolding the Orf9b homodimer to generate apo-Orf9b homodimers but could not identify conditions that yielded crystals upon re-screening.”

      (4) Have the authors tried to co-crystalize hit compounds or hit analogs resulting from SAR with the TOM70 protein, to really observe the binding mode of these compounds? Only using in silico methods is not satisfactory.

      We initially attempted to develop a crystallization system for Tom70 that would enable us to structurally resolve our bound compounds, but, at the time of writing the manuscript, had not identified a system that yielded crystals. However, another group has published a structure of apo-human Tom70 (https://pmc.ncbi.nlm.nih.gov/articles/PMC13075491/) - we sent them compounds and were unable to identify convincing density by soaking. We agree that a future study in a different crystal system or by pursuing co-crystallization could be fruitful.

      (5) Although the authors improved the binding affinity of HTS hits for TOM70 using SAR, there is a lack of functional assays to evaluate whether the HTS hits or analogs could affect IFN inhibition caused by ORF9b or virus infection (cell-based or animal-based assays).

      We have expanded the discussion section to include potential future experiments that could be conducted to probe this:

      “Although we have not assessed the permeability of these compounds and their ability to restore IFN in the context of cell-based assays, one way this could be accomplished is by adapting a previously used reporter cell line. Specifically, this assay uses a reporter cell line that has a Lucia reporter under the control of the IFN-β/ISG56 promoter that is expressed upon mock infection with synthetic dsRNA. When WT Orf9b is co-transfected with the reporter, IFN is suppressed, and, we have shown that phosphomimetic mutants of Orf9b that block its interaction with Tom70 restores IFN signaling. If these compounds are sufficiently permeable, then, for the lipidated-compounds targeting the Orf9b homodimer, we would expect the Orf9b monomer:homodimer equilibrium to shift towards the homodimer due to the stabilizing effect these lipidated-compounds have on the homodimer conformation leading to an increase in IFN signaling. Similarly, for compounds targeting Tom70, we would expect that these compounds block the Orf9b monomer from binding to Tom70 to produce a similar effect.”

      (6) Figure 4 doesn't have A, B, or C indicated in the figures.

      We have revised Figure 4 to include A, B, and C.

      Reviewer #2 (Recommendations for the authors):

      (1) Page 5 line 23: The authors could comment on the biological relevance of the lipid-bound version of Orfb9 and how it could associate with membranes.

      We thank the reviewer for their comments. Currently, it is unknown what role lipid-binding plays on Orf9b’s function beyond the stabilizing effect it has on the homodimer conformation. While it has been shown that Orf9b co-localizes at the outer mitochondrial membrane through Tom70 association, it has not been shown that Orf9b itself binds to membranes. While this does not exclude the possibility that the Orf9b homodimer could directly bind to membranes, we suspect a more plausible explanation is that Orf9b homodimers can bind to lipid-like metabolites within cells such as palmitate which we had previously shown.

      (2) Figure 3F: These SPR sensorgrams are not all to the same y-axis scale.

      We thank the reviewer for their comment. The sensorgram axis scale is reflective of three separate SPR experiments on three capture points for the ligand. Therefore, differences in ligand capture on each surface will produce slight differences in the total measured response. The axes are scaled to make interpretation easier. We are not quantitatively comparing between treatments, but noting the qualitative behavior of each individually as the concentrations change.

      (3) Discussion: The authors could comment on the next steps, ligands ADME, solubility, permeability as the compounds are at low uM binding affinity, with increased concentrations, comment on selectivity/specificity.

      Given that these are still “hits”, we think a discussion of these properties (which we study intently in the lab!) is premature and beyond the scope of this manuscript.

      Reviewer #3 (Recommendations for the authors):

      (1) The authors should carefully read the manuscript as there are numerous typos and duplicated words across the whole document and supplementary data.

      We have gone through the manuscript and the supplementary material and corrected the typographical errors and duplicated words that we found, including a repeated sentence in the crystallization methods and a repeated word in the purification methods. We have also renamed the supplementary figures to the eLife figure supplement style. We expect copy editing at the VOR stage to catch anything that remains.

      (2) Details of how Chai-1 was run, including constraints, should be given in the Materials and Methods section.

      We have revised the methods section to describe how Chai-1 was used for both Orf9b and Tom70 co-folding predictions. See above.

      (3) There was no comment on whether the compounds which were found were attempted to be co-crystallised. If they were, but negative data were collected (didn't crystallise, didn't diffract, or no additional density found), then this needs to be stated.

      We have revised the manuscript to clearly point out that beyond our initial attempts to crystallize apo-Orf9b homodimer to enable fragment soaking, we also attempted to both soak our lipidated-compounds into apo-Orf9b homodimer crystals as well as co-crystallize the compounds which did not yield crystals.

      “We attempted two strategies of crystallizing our lipidated-compounds with the apo-Orf9b homodimer to structurally resolve the complex. First, we attempted to soak our compounds into apo-Orf9b homodimer crystals but observed poor tolerance to DMSO which quickly disintegrated the crystals after minutes. Second, we attempted to co-crystallize the lipidated-compounds after refolding the Orf9b homodimer to generate apo-Orf9b homodimers but could not identify conditions that yielded crystals upon re-screening.”

    1. Author response:

      The following is the authors’ response to the original reviews.

      We thank the editors and reviewers for their careful and constructive assessment of our manuscript. Based on their comments and suggestions, we have revised the manuscript extensively to improve accessibility, clarify model novelty and the physical intuition behind the wave directionality, and correct and expand figures, units, equations, parameter definitions, and references.

      The main changes in the revised manuscript are that:

      - The abstract and main text now explicitly describe the work as coupling established reaction–diffusion models of Cyclin B–Cdk1 signaling and the excitable Rho–actin cortex, rather than presenting the individual modules as newly developed models.

      - The governing equations, model assumptions, coupling, and key parameters are presented in the main text, with clarified units and a complete parameter table.

      - Figures 1 and 2 were redesigned to make the geometry, kymographs, wave-front/wave-back definitions, and coexistence of travelling-wave-like and diffusive dynamics more intuitive.

      - The diffusion-coefficient units and the conversion used to calculate total active nuclear Cyclin B–Cdk1 were corrected; the affected plots were regenerated and total active nuclear content is now defined explicitly in Eq. 7.

      - The Introduction and Discussion now better distinguish established Cdk1–cortex coupling from the contribution of this study, incorporate work in Drosophila and zebrafish, and distinguish experimentally supported observations from model predictions.

      - The cortical dynamical regimes and the role of Ect2 were clarified, supplementary figures were revised, and the suggested classic references were added.

      eLife Assessment

      This valuable study combines previously established mathematical models to investigate why cortical waves in starfish and Xenopus embryos propagate in opposite directions. The modeling results are solid and plausible, but remain experimentally untested. Improving the presentation and discussion of the results could make the study more accessible to a wider audience.

      We appreciate this assessment and have focused the revision on exactly these points. The manuscript now makes the established origin of both model modules explicit, provides the core equations and parameters in the main text, gives a more intuitive explanation of the front–back mechanism, redesigns the key figures, and expands the discussion of experimental support, limitations, and testable predictions. The work remains theoretical, and we now state that limitation more clearly rather than implying experimental validation. See Abstract, Introduction, Model, and Discussion in the revised manuscript.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      The main goal of this manuscript is to develop a mathematical model of the regulation of cortical dynamics by Cdk1 activity to explain why, in some embryos (e.g., Xenopus), surface contraction waves are believed to move in the same direction as Cdk1, while in other embryos (e.g., starfish) they are believed to move in the opposite direction.

      Strengths:

      (1) The paper addresses a very important question.

      (2) The mathematical model is sensible and suggests that the different relationship between Cdk1 and surface contraction waves might arise from the different behavior of the mitotic entry wave and the mitotic exit wave.

      (3) The authors propose a mechanism by which the wave observed at mitotic exit might not passively follow the trigger wave observed at mitotic entry'

      (4) The proposed mechanism is a potential explanation of the observed differences.

      (5) The proposed mechanism is centered on different dynamics between the nucleus and the cytoplasm, highlighting the potential importance of the nucleus (and nuclear size) in organizing cortical dynamics.

      We thank the reviewer for this positive assessment. The revision now makes the central question and the scope of the contribution more explicit: the individual Cdk1 and cortical modules were already previously established, while the present study asks how their coupling, together with cell geometry and nuclear Cdk1 content, can generate distinct wave-back dynamics and cortical responses. The revised manuscript now also foregrounds the mechanistic distinction between activation fronts and wave backs and uses this distinction to organize the Results and Discussion sections. See Abstract, Introduction, Results and Discussion in the revised manuscript.

      Weaknesses:

      (1) The proposed mechanism works if the activity in the nucleus is much higher than the high activity (high state of the bistable system) of the cytoplasm. So, as the wave propagates across the cytoplasm, the activity around the nucleus remains higher, which potentially causes a delay in the onset of Cyclin B-Cdk1 degradation in the region around the nucleus compared to the surrounding cytoplasm. This effect happens over a typical length scale, and if such a length scale is comparable to embryo size, this becomes the predominant mechanism. However, such a mechanism should exist near the nucleus independently of embryo size. So, it seems that for embryos where the wave back and wave front should travel together, nuclear activity must be adjusted not to be much higher than cytoplasmic activity. A better discussion of the discovered process and its implications would strengthen the paper. It requires careful reading to understand what, in hindsight, is a rather simple explanation. Is there any experimental evidence that the overall activity of Cdk1 is higher in the nucleus than in the cytoplasm?

      We agree that the mechanism needed a more intuitive explanation. The revised Results now separate two simultaneous processes. The activation front propagates outward with an approximately constant trigger-wave-like velocity, whereas excess active Cyclin B–Cdk1 associated with the enriched nuclear pool also spreads diffusively. This diffusive component exists locally around the nucleus irrespective of cell size. What depends on effective system size is whether that diffusive length scale is large enough, relative to the cell, to shape the wave back over a substantial fraction of the domain and ultimately at the cortex. This is why nuclear content and effective system size act together. The revised Fig. 2B and the accompanying text now explain this competition explicitly. We also revised the Discussion to distinguish experimental plausibility from quantitative validation: active Cyclin B–Cdk1 has been observed to accumulate in nuclei before surrounding cytoplasmic activation in frog egg extracts, nuclei can specify where mitotic waves begin, and Cyclin B enrichment near the nuclear region has been reported in starfish oocytes. However, whether nuclear active Cyclin B–Cdk1 reaches the level required for complete wave-back reversal remains a model prediction, which we now state explicitly. See Results, Fig. 2B and caption (p. 6), Methods and Eq. 7 in the revised manuscript.

      (2) While the fact that Cdk1 can enslave cortical dynamics is clearly shown in the model, this is expected from the literature. There are systems where the enslavement of cortical and bulk actomyosin contractility to Cdk1 activity has been more clearly demonstrated (Drosophila and zebrafish embryos), as well as shown to have clear functions (nuclear positioning and ooplasmic segregation).

      We agree. The revised manuscript no longer presents Cdk1 control of cortical dynamics as a novel result. We expanded the introduction to discuss Drosophila and zebrafish and to note the established functions of Cdk1– actomyosin coupling in nuclear positioning and ooplasmic segregation. We now frame the contribution of the present work as explaining how established Cdk1-to-cortex coupling can transmit geometry-dependent cytoplasmic waveforms into different cortical directionality and reactivation regimes. See Introduction and Discussion in the revised manuscript.

      (3) The writing could be improved. The authors make some claims of originality that seem a stretch, e.g., in the abstract, they say: "we develop a reaction-diffusion model of Cyclin B-Cdk1 signaling in spherical cells with localized nuclear activation", but they essentially use a previous model with a few numerical tweaks. The figures are sometimes mislabelled or not explained, and some of the units seem wrong.

      We agree and revised the framing throughout. The Abstract now states that we “couple established reaction–diffusion models of Cyclin B–Cdk1 signaling and the excitable Rho–actin cortex.” The Introduction similarly states that we are not developing a new model, and a dedicated Model section now gives the equations, assumptions, coupling, and original sources of the two modules. We also revised figure labels and captions, added schematic panels, corrected the diffusion units to μm<sup>2</sup>/s, corrected the conversion used for total active nuclear Cyclin B–Cdk1, and regenerated the affected plots. The control variable is now defined explicitly as total active nuclear content in Eq. 7 and reported in pmol. See Abstract, Introduction, Model, Fig. 1 and caption (p. 3); Fig. 2 and caption (p. 6); Methods, especially Eq. 7 and Table 1 (p. 16) in the revised manuscript.

      (4) The authors give the existence of trigger waves as a fact. While the predominant view is that such waves exist in the first cycle of the Xenopus embryos (however, this is from measurement of the cortical contractions, so a bit circular for this paper), it is unclear if waves exist in the starfish embryo, so the potential explanation that the starfish embryo simply has different Cdk1 dynamics cannot be ruled out.

      We agree that the evidence is not equivalent across systems. The revised manuscript avoids treating a starfish intracellular Cdk1 trigger wave as an experimentally established fact and instead presents the cross-species comparison as an interpretation within the model framework. We distinguish the model prediction from the available experimental observations and explicitly state that the nuclear active Cyclin B–Cdk1 level required for complete waveback reversal remains to be tested. Thus, different underlying Cdk1 dynamics in starfish are not excluded by our study. See Introduction, Results and Discussion in the revised manuscript.

      Reviewer #2 (Public review):

      Summary:

      Large oocytes show prominent waves of cortical contractions. Previous works combining experiments and computational modeling have shown that the waves are driven by gradients of CDK1 kinase activity that trigger excitable Rho activity patterns on the cortex. This present work combines two previously published mathematical models for CDK1 activation and Rho activation, respectively. They show that the models combined can explain diverse shapes of cortical contractions observed in different species and at various stages of development. This shows how the same molecular machinery can generate diverse patterns dependent on the size of the system and the size and position of the cell nucleus.

      Strengths:

      (1) Carefully done modeling work providing a simple and elegant explanation for a complex cellular behavior.

      (2) Very nicely illustrated, simulations can be directly compared to previous experimental observations.

      (3) Explains observations made in different model systems, providing a unifying model.

      We thank the reviewer for this assessment. We have revised the manuscript so that this scope is explicit from the outset: the model modules are established, while the contribution is the analysis of their coupling and the identification of geometry, total nuclear Cdk1 content, and cortical recovery kinetics as controls that generate qualitatively different behavior within one framework. See Abstract, Introduction, Results and Discussion in the revised manuscript.

      Weaknesses:

      (1) Purely theoretical work, no experimental validation.

      We agree that direct experimental validation would strengthen the work. We have not added a new experimental dataset in this revision. Instead, we have made the experimentally testable status of the conclusions explicit. The revised discussion identifies total nuclear active Cyclin B–Cdk1 content and effective system size as controls of wave-back directionality, states that the nuclear enrichment required for complete reversal remains to be tested, and identifies perturbation of actomyosin contractility while monitoring Cdk1/Rho dynamics as one way to probe the role of omitted mechanics. We therefore present the work as a theoretical framework that generates concrete predictions, not as experimentally validated proof of the mechanism. See Discussion section in the revised manuscript.

      (2) Adopts previously published models more or less 'as is', without detailed re-evaluation and re-assessment, or without developing them further.

      We agree that the individual modules are adopted without substantial re-derivation or extension, and the revised manuscript now mentions this directly. We now discuss the models in the main text, mentioning the Yang and Ferrell / Puls Cdk1 model and the Michaud et al. cortical model, giving the equations and coupling, and then the Methods sections states that parameter values are retained from the original publications. Our aim is not to claim a new formulation of either module, but to analyze what emerges when they are coupled in a common geometry. That analysis yields the front–back asymmetry, geometry-dependent reversal of the Cdk1 wave back, and distinct cortical reactivation regimes. See Introduction, Model, Methods, and Results in the revised manuscript.

      Overall, I find this work important, as it shows that combining models of the CDK1 gradient and Rho activation modules can explain the surface contraction waves observed in oocytes. Strikingly, it elegantly explains the differences seen between different experimental systems. While previously these were considered a 'controversy', modeling shows that the differences are simply a consequence of the difference in the size of the oocytes. In addition, the model makes several intriguing predictions that can be tested in future experiments.

      We thank the reviewer. In revising the manuscript, we were careful not to reduce the mechanism to cell size alone: the model shows that directionality depends jointly on effective cell size and total nuclear Cdk1 content, which is set by nuclear size and nuclear concentration. We now mention this combination consistently and make the associated predictions explicit in the Discussion. See Results and Discussion in the revised manuscript.

      Reviewer #3 (Public review):

      Summary:

      Using realistic mathematical models, Cebrián-Lacasa et al. address the relationship between waves of activation of Cyclin B-Cdk1 that propagate through the cytoplasm of large (~1 mm) oocytes and fertilized eggs and surface contraction waves (SCWs) driven by Rho GTPase activity in the cell cortex. They present numerical simulations of the underlying reaction-diffusion equations that account in broad strokes for both the expected behavior of 'fronts' of Cdk1 activation (that propagate at constant velocity from the nucleus-the source of Cdk1 activity-to the cell cortex) and the unusual behavior of 'backs' of Cdk1 inactivation (that may propagate either away from or towards the nucleus, or exhibit simultaneous inactivation throughout the cytoplasm). They also model Rho GTPase activity in the cortex as an excitable system that propagates SCWs (target patterns, spiral waves, and more complicated patterns). When Cdk1 is activated in the cortex, it phosphorylates and inhibits the RhoGEF, Ect1, which suppresses SCWs by reducing Rho GTPase activity. As the wave-back of Cdk1 inactivation moves across the cortex, Rho GTPase activity recovers abruptly, and SCWs reappear as 'phase waves' whose speed and directionality are determined by the underlying cytoplasmic Cdk1 signal.

      Strengths:

      As a theoretical examination of an interesting and puzzling aspect of early embryonic development, this study shares the same strengths and weaknesses as all mathematical and computational approaches to molecular cell biology. The mathematical models are precise formulations of the underlying assumptions of the authors (which are quite reasonable in this reviewer's opinion), and the analysis and computational results are dependable consequences of the molecular mechanisms the authors have in mind. The model is expertly analyzed, and the results are both reliable and intriguing. The results are discussed in light of experimental evidence. Because the authors' methods and results suggest novel-and sometimes counterintuitive-avenues for experimental research, this paper is likely to have a significant impact on the field of Rho GTPase signaling in oocytes and early embryos, and perhaps in other cells as well.

      We thank the reviewer for this thoughtful assessment. We have preserved the mathematical formulations and made the assumptions, mechanisms, and experimentally testable consequences easier to identify. In particular, the revised Results section emphasizes the distinct mechanisms governing the activation front and wave back, the revised figures provide a more intuitive visual explanation, and the Discussion separates experimentally supported observations from model predictions. See Model, Results, and Discussion in the revised manuscript.

      Weaknesses:

      Like all mathematical models, the underlying assumptions can be critiqued as neglecting this -or-that 'crucial' effect (e.g., mechanical coupling via cortical tension or cytoplasmic flow, as the authors acknowledge), and the highly technical methods of analysis and simulation can be unfamiliar and off-putting to experimental cell biologists. The paper is a difficult read, even for an experienced theoretician. For those who take the time to understand this paper, it may change the way they think about the coupling of cell cycle control (Cdk1 activation and inactivation) and cell surface contraction waves.

      We agree on both accessibility and model scope. To improve accessibility, we added the core equations and parameters to the main text, introduced more qualitative descriptions of the dynamical regimes, and redesigned Fig. 2B to show the physical mechanism schematically. We also expanded the discussion of the limitations. We did not add mechanical coupling to the model in this revision; instead, the manuscript now states explicitly that showing biochemical signaling to be sufficient within the model does not demonstrate that cortical tension, cytoplasmic flow, or surface deformation are unnecessary in living cells. These effects are identified as additional important factors that can affect the dynamics and as targets for future perturbation experiments. See Model, Results, Fig. 2B and caption (p. 6), Discussion in the revised manuscript.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      (1) Carefully proofread the manuscript, Figures, and Figure Legends to make sure that statements are accurate. Please describe in more detail what is shown in every Figure panel. The units of diffusion in Figure 2C appear wrong, total activity is not really explained in the text, and it is a strange use, as the activity changes over time; the units of total activity are millimolar, which seems unrealistic. The Figure 1D heatmap does not explain what is plotted. Intensity is neither defined nor is it clear how the first wave front was drawn; the second appears to be convincing. The curvature of what physical object is plotted in Figure 1D, and again, how are the wavefronts on those Figures drawn?

      We carefully reviewed the manuscript and all main and supplementary figures. Figure 1 was redesigned to show the model in 3D, 2D, and 1D and to make the coordinates used in the kymographs explicit. The revised Fig. 1 caption now states that the experimental color scales correspond to Cdk1-reporter intensity (top) and local membrane curvature (bottom), and that the dotted lines mark the tracked front and back. These overlays are intended as visual guides in the adapted experimental kymographs rather than quantitative fits used in our model analysis. Figure 2 was also redesigned and its caption expanded. The diffusion coefficient is now reported in μm<sup>2</sup>/s. In addition, we identified and corrected an error in the conversion of total active nuclear Cyclin B–Cdk1. The corrected control variable is total active nuclear content, reported in pmol and defined explicitly in Eq. 7; the affected main and supplementary plots were regenerated. See Fig. 1D and Fig. 1 caption (p. 3); Fig. 2 and caption (p. 6); Results, Methods, Eq. 7, Table 1 (p. 16) and Supplementary Figs. S3–S4 in the revised manuscript.

      (2) Provide a better intuitive explanation of the proposed mechanism.

      We substantially rewrote the Results section describing geometry-controlled directionality. The revised explanation first establishes the front–back asymmetry and then gives an intuitive description: a constant-speed activation front coexists with a slower diffusive spread of the elevated nuclear pool; because diffusion lags behind the front, distant regions can relax earlier, creating a gradient that drives an inward wave back. Revised Fig. 2B depicts these processes schematically. See Results, especially Fig. 2B and caption (p. 6) and Discussion in the revised manuscript.

      (3) Reduce claims of novelty when not justified. I think that there is a potentially interesting idea in this paper, but also a lot of known facts that are revisited, and being unclear about what was known and what is new does not help the manuscript.

      We agree. The revised Abstract and Introduction sections explicitly say that we couple established models rather than develop new individual modules. The Model section cites the original sources of each module, and the Introduction distinguishes established biological coupling from the question addressed here. We reserve the main contribution for the consequences of the coupled analysis: front–back asymmetry, the joint control by nuclear Cdk1 content and effective system size, and the resulting cortical response. The discussion also mentions the key unvalidated step as a testable prediction. See Abstract, Introduction, Model and Discussion in the revised manuscript.

      (4) The interface of Cdk1 activity with actomyosin contractility (and cortical dynamics) is much better understood in other systems, and discussing those systems will improve the impact of the paper.

      We expanded the Introduction to include Drosophila and zebrafish and to note the established functions of Cdk1-controlled actomyosin dynamics in nuclear positioning and ooplasmic segregation. This broader context makes clear that Cdk1–cortex coupling was already established and that our specific question is how cytoplasmic wave geometry shapes the downstream cortical response in large oocytes and eggs. See Introduction section in the revised manuscript.

      (5) Be clearer about what the goal of this paper is and keep the focus on that. In my opinion, there is too much writing spent describing known facts.

      We revised the Introduction to move more directly from the biological puzzle to the central question and then into the coupled model. The manuscript now explicitly states that we ask whether the opposite SCW directionality can follow from geometry and nuclear Cdk1 content rather than organism-specific cortical mechanisms, and then ask how the resulting cytoplasmic waveforms are transmitted to the cortex through Ect2 inhibition. We also reduced repeated background material and moved the core mathematical specification into a dedicated Model section. See Introduction, Model and Results in the revised manuscript.

      (6) A discussion that the Cdk1 spatiotemporal patterns remain to be analyzed in both Xenopus and starfish embryos would be appropriate.

      We added this limitation to the discussion in a way that distinguishes what is known from what remains to be measured. The revised text summarizes observations supporting nuclear enrichment and wave initiation but also says that whether nuclear active Cyclin B–Cdk1 reaches the levels required for complete wave-back reversal remains experimentally to be tested. We also avoid presenting the starfish intracellular Cdk1 wave as established fact. See Introduction, Results, and Discussion in the revised manuscript.

      Reviewer #2 (Recommendations for the authors):

      (1) I have one main suggestion. I would find it important that the authors present the models in more detail in the main text. In principle, even if they adopted previously published models, the reader should not need to go back to those original papers to find the equations and parameters. Readers should not even need to dig deep into the supplemental material. For example, the main equation used to model the CDK1 gradient should be shown in the main text with critical parameter values listed. For example, the text mentions that the diffusion coefficient of CDK1-Cyclin B has a critical importance (which I very much agree with), but I could not easily find the values used and still had to guess the units.

      We agree. We added a dedicated model section to the main text containing the governing reaction-diffusion equations for both modules and the Cdk1–Ect2 coupling. The variables and roles of the principal parameters are defined there, while Table 1 lists the standard parameter values and units, including the diffusion coefficients used for the cytoplasmic regimes. The total active nuclear Cyclin B–Cdk1 control variable is defined explicitly in Eq. 7 in the Methods section. See Model, Methods, Table 1 (p. 16) and Eq. 7 in the revised manuscript.

      (2) Overall, the manuscript is well written and nicely illustrated. However, the text could be more concise and, as explained above, show more equations rather than trying to describe them in words. Some of the illustrations could also be larger and possibly shown at higher contrast. Finally, the subtitles could be more imaginative, describing the main finding rather than simply stating what has been done.

      We revised the manuscript throughout to reduce repeated background material and to replace lengthy verbal descriptions of the core model with equations in the main text. We standardized figure text and redesigned several panels, especially Figs. 1 and 2, to improve readability and interpretability. We did not replace every subsection title, but we have tried to use clear descriptive titles (with a message where possible). We revised several headings in the Results section so that they communicate the main finding directly, for example “Front–back asymmetry: traveling fronts and gradient-controlled backs,” “System size and diffusion modulate gradient effectiveness,” and “Phase diagram of Cdk1 waves.” See Introduction, Model, Results headings and text, Figs. 1– 2 and captions; supplementary figures in the revised manuscript.

      (3) The starfish work focuses on meiosis I, not meiosis II.

      We reviewed the stage-specific wording throughout. Rather than replacing every reference with “meiosis I,” we removed unnecessary stage labels where the argument concerns starfish oocyte meiosis more generally, and we use stage-specific wording only when it is supported by the cited experiment. In particular, Fig. 1 now labels the experimental panel simply as starfish meiosis rather than meiosis II. See Fig. 1D and caption (p. 3); Introduction and Results in the revised manuscript.

      Reviewer #3 (Recommendations for the authors):

      (1) Figure 1D. Right: experimental kymographs. What are 'intensity' and 'curvature'? I suppose 'intensity' refers to Cdk1 activity and 'curvature' to local curvature of the cell membrane. If so, Cdk1 activity seems to propagate as a wave around the cortex from the animal pole, but (I suppose) these are phase waves rather than trigger waves, because the nucleus is closer to the animal pole, so the cytoplasmic trigger waves reach the cortex sooner there and later at larger values of phi. In the starfish oocyte, the curvature 'bumps' at the animal pole and the equator seem to be stationary. Maybe I am misinterpreting the data; in any case, it might help readers to guide their reading of this data.

      We clarified both the labels and the interpretation. The revised Fig. 1 caption explains the plotted experimental quantities as Cdk1-reporter intensity (top) and local membrane curvature (bottom), and mentions that the dotted lines mark the tracked front and back. We also distinguish the cytoplasmic propagation from the cortical phase-wave readout. Because the nucleus is off-center, the distance from the nuclear source to the cortex varies with angular position, so the radial Cdk1 solution is sampled at different times around the cortex. The Numerical methods now state explicitly that this geometry produces the angle-dependent arrival times shown in Fig. 1D. See Fig. 1D and Fig. 1 caption (p. 3); Model geometry and Numerical methods in the revised manuscript.

      (2A) In panels (ii) and (iii), what is the meaning of the hyperbolic dotted line labelled 'underlying diffusion'?

      The original schematic was replaced by the reworked Fig. 2B. The revised schematic and results now separate the outward trigger-wave-like front from the slower diffusive spread of the elevated nuclear pool. The “underlying diffusion” component is therefore no longer an unexplained fitted-looking curve; it is presented as the diffusive process that establishes the gradient controlling the wave back. See Fig. 2B and caption (p. 6) and Results in the revised manuscript.

      (2B) This panel is very confusing. What is the significance of all the different colored lines? What is the meaning of '◄Time'? This panel needs more explanation. Also, fix 'increaseded'.

      We agree that this was confusing. We now redrew Fig. 2B as a two-dimensional schematic with a consistent activity color scale and explicit labels for the phases and dynamical processes. The ambiguous time-arrow presentation was removed, and the typographical error was corrected. See Fig. 2B and caption (p. 6) and Results in the revised manuscript.

      (2C) Units of diffusion constant are wrong; should be μm2/s. Also, please explain (perhaps in context of Figure S3) how you calculate 'units of active nuclear CycB-Cdk1 (mmol)' in terms of total [CycB-Cdk1] in the nucleus, radius of the nucleus, and model parameter γ.

      The diffusion coefficient is now reported consistently in μm<sup>2</sup>/s. We also identified and corrected an error in the conversion to total nuclear amount. Eq. 7 now defines the total active nuclear Cyclin B–Cdk1 content from the enriched nuclear active concentration and nuclear volume; γ scales the nuclear concentration relative to the cytoplasmic baseline. The corrected quantity is reported in pmol, not mmol, and the corresponding main and supplementary plots were regenerated. Supplementary Fig. S3 shows that varying γ or nuclear radius collapses onto this single control variable. See Fig. 2D and caption (p. 6); Results, Methods, (Eq. 7), Table 1 (p. 16) and Supplementary Fig. S3 in the revised manuscript.

      (2D) Please explicitly indicate the speed of the wave front, because it is difficult to read, given the scale of the vertical axis.

      Agreed. The revised Fig. 2 caption now explicitly states that the wave-front velocities are fitted by a quasiconstant velocity of approximately 23 μm/min. See Fig. 2D caption (p. 6) and Results in the revised manuscript.

      (3) Box 2. C. You might indicate that the Rho-actin dynamics are oscillatory for 0.59 < α < 1.02 and excitable for α slightly larger than 1.02 and (I suppose) slightly smaller than 0.59. Furthermore, I suppose (given the results in Figure 4) that the system does not propagate waves for α {less than or equal to} 0.5. Somehow, the authors should indicate how wave propagation is suppressed for small values of α.

      We clarified the bifurcation structure and the low-α suppression of cortical activity. We did not adopt the proposed regime labels verbatim, because the spatial model supports propagating waves across a broader active window than the homogeneous oscillatory interval alone would suggest. The revised text therefore reports the two Hopf bifurcations at α = 0.59 and α = 1.02, states directly that the cortex is quiescent for low α, and reports that propagating waves persist across 0.59 < α < 1.26 up to the wave instability at α = 1.26. This directly explains how sufficiently strong Cdk1-mediated reduction of effective Ect2 suppresses propagation. See Box 2C (p. 9) and Results in the revised manuscript.

      (4) Lines 273 and 294. "These differences arise...".

      Corrected. The relevant Results text was rewritten during the broader restructuring, so the original wording no longer appears. See Revised Results.

      (5) Lines 380, 381. "...the Hopf bifurcation (at α = 0.59) that separates...".

      We did not retain the sentence in its original form. Instead, the revised text now identifies both Hopf bifurcations explicitly (α = 0.59 and α = 1.02), states the wave-propagating window, and then describes how Cdk1derived inhibition moves the cortical system across the bifurcation during suppression and recovery. We believe this is clearer than adding the parenthetical phrase to the old sentence. See Results and Box 2C (p. 9) in the revised manuscript.

      (6) Table 1. Include a value for α_0.

      Done. Table 1 now lists α<sub>0</sub> = 1 (dimensionless), and the Methods state that α = α<sub>0</sub> = 1 before nuclear envelope breakdown. See Table 1 (p. 16) and Methods in the revised manuscript.

      (7) Line 522. What does 'implemented manually' mean?

      We replaced the ambiguous wording. The Numerical methods now state that both models were integrated with an explicit second-order Runge–Kutta method implemented in custom code; the cytoplasmic and two dimensional cortical simulations use finite differences, and the three-dimensional cortical simulations use a finite element method implemented in FEniCSx. See Numerical methods in the revised manuscript.

      (8) Figure S1. A. The first green dot should be labelled γ = 1. B. Left panel is γ = 1, I suppose.

      Corrected. Revised Supplementary Fig. S1 explicitly labels the baseline γ = 1 condition and the enriched γ = 1.5 condition. Its caption also explains that γ scales the nuclear concentration above the cytoplasmic baseline while preserving the active-to-total ratio. See Supplementary Fig. S1 and caption; Model in the revised manuscript.

      (9) Figure S2. What is X_0? How is it related to γ?

      We addressed this by removing the X<sub>0</sub> notation rather than adding another conversion. The revised supplementary analysis uses γ directly as the nuclear enrichment factor, defined in the main Model section and illustrated in Supplementary Fig. S1. The revised Supplementary Fig. S2 now focuses on the fitted wave-front and wave-back trajectories for different γ values. See Model, lines 123–132; Supplementary Figs. S1–S2; Methods, lines 620–638.

      (10) References. Emphasis is on post-2010 literature. One classic paper on SCWs is mentioned: Hara (1971). The classic publication on Cdk1-driven mitotic waves in fruit fly embryos is Foe & Alberts (1983) J Cell Sci 61:31. The first theoretical prediction of Cdk1 trigger waves in syncytial cells was given by Novak & Tyson (1993) J Theor Biol 165:101. Citing Deneke et al. (2016) Dev Cell 38(4) could also be considered.

      We added the suggested literature. Novak & Tyson (1993) is now cited for the early theoretical prediction of trigger-wave behavior; Foe & Alberts (1983) is cited in the discussion of cell-cycle/cortical waves; and Deneke et al. (2016) is cited in the Introduction both in the mitotic-wave context and in the broader discussion of Cdk1–actomyosin coupling. See Introduction and reference list in the revised manuscript.

    1. Author response:

      The following is the authors’ response to the original reviews.

      eLife Assessment:

      Using genome databases, the authors performed solid bioinformatic analyses to trace the genomic history of the clinically relevant Staphylococcus aureus tetracycline resistance plasmid pT181 over the last seven decades. They discovered that this element has transitioned from a multicopy plasmid to a chromosomally integrated element, and the work represents a valuable demonstration of the use of publicly available data to investigate plasmid biology and inform clinical epidemiology. This work will appeal to researchers interested in staphylococcal evolution and plasmid biology.

      Thank you, we agree with this overview. We also think this work is interesting to people interested in antimicrobial resistance and bacterial genome structure.

      Public Reviews:

      Reviewer #1 (Public review):

      The study provides a robust bioinformatic characterization of the evolution of pT181. My main criticism of the work is the lack of experimental validation for the hypotheses proposed by the authors.

      Comments on the study:

      (1) One potential reason for the decline in pT181 copy number over time may be a high cost associated with the multicopy state. In this sense, it would be interesting if the authors could use (or construct) isogenic strains differing only in the state of the plasmid (multicopy/integrated). With this system, the authors could measure the fitness of the strains in the presence and absence of tetracycline, and they could be able to understand the benefit associated with the plasmid transition. The authors discuss these ideas, but it would be nice to test them.

      We agree that the relative fitness of integrated versus multicopy plasmids is interesting and a costly multicopy state could explain the transition of independent pT181 replicons to chromosomal integration. This is a project we are exploring for a future study. However, we think that this additional experimental work goes beyond the scope of the paper.

      (2) It would be interesting to know the transfer frequencies of the multicopy mobilizable pT181 plasmid, compared to the transfer frequency of the plasmid integrated into the SSCmec element (which can be co-transferred, integrated in conjugative plasmids, or by transduction).

      We agree with the reviewer that this is an interesting question. However, we think inferring these rates from natural sequence data is not feasible in this case given the low heterogeneity of the plasmid sequence. A laboratory-based experimental study could not address the real transfers we observe over the course of decades, as in vitro S. aureus transfer rates are often not good proxies for in vivo (McCarthy et al.). In addition, we do not know what is moving the integrated plasmid. pT181 could be moved by a phage or plasmid, so we are uncertain what the correct experiment would be to explore this.

      (3) One important limitation of the study that should be mentioned is that inferring pT181 PCN from whole genome data can be problematic. For example, some DNA extraction methods may underestimate the copy number of small plasmids because the small, circular plasmids are preferentially depleted during the process (see, for example, https://www.nature.com/articles/srep28063).

      We have further investigated the role of technical variation in influencing measured PCN. The decline in copy number over time within our longest-collected strain remains significant after controlling for a number of technical variables: instrument used, type of DNA extraction technique, and sequencing center. In addition, plasmid copy number estimations between extraction techniques are not significant when comparing contemporaneously collected samples. We have added these supporting analyses to our results (L328-333) and methods (L612-634).

      Reviewer #2 (Public review):

      Summary:

      The authors performed bioinformatic analyses to trace the genomic history of the clinically relevant pT181 plasmid. Specifically, they:

      (1) tracked the presence of pT181 across different S. aureus strain backgrounds through time. It was first found in one, later multiple strains, though this may reflect changes in sampling over time.

      (2) estimated the mutation rate of the chromosome and plasmid.

      (3) estimated the plasmid copy number of pT181, and found that it decreased over time. The latter was supported by two sets of statistical analyses, first showing that the number of single-copy isolates increased over time, and second, that the multicopy isolates demonstrated a lower PCN over time.

      (4) reported the different integration sites at which pT181 integrated into the genome.

      As a caveat, they mentioned that identical plasmid sequences have variable plasmid copy numbers across different genomes in their dataset.

      Strengths:

      This is a very solid, well-considered bioinformatic study on publicly available data. I greatly appreciate the thoughtful approach the authors have taken to their subject matter, neither over- nor underselling their results. It is a strength that the authors focussed on a single plasmid in a single bacterial species, as it allowed them to take into account unique knowledge about the biology of this system and really dive deep into the evolution of this specific plasmid. It makes for a compelling case study. At the same time, I think the introduction and discussion can be strengthened to demonstrate what lessons might be drawn from this case study for other plasmids.

      Weaknesses:

      The finding that the pT181 copy number declined over time is the most interesting claim of the paper to me, and not something that I have seen done before. While the authors have looked at some confounders in this analysis, I think this could be strengthened further in a revision.

      We have investigated this issue further in revisions. The decline in copy number over time within our longest-collected strain remains significant after controlling for a number of technical variables. In addition, plasmid copy number estimations between extraction techniques are not significant. We have mentioned these updates in the results (L327-333) and provided more explanation for the extraction technique in the methods (L612 - 634).

      For the flow of the storyline, I also think the estimation of mutation rates (starting L181) and integration into the chromosome (starting L255) could be moved to the supplement or a later position in the main text.

      We have chosen to keep the structure of the results largely the same.

      Clearly, the use of publicly available data prevents the authors from controlling the growth and sequencing conditions of the isolates. It is striking that they observe a clear signal in spite of this, but I would have loved to see more discussion of the metadata that came with the publicly available sequences and even more use of that metadata to control for confounding.

      We have further investigated the role of technical variation in influencing measured PCN. The decline in copy number over time within our longest-collected strain remains significant after controlling for a number of technical variables: instrument used, type of DNA extraction technique, and sequencing center. In addition, plasmid copy number estimations between extraction techniques are not significant when comparing contemporaneously collected samples. We have added this to our results section (L327-333) and explain further in the methods (L612 - 634). Unfortunately, the metadata is incomplete for many isolates, limiting our ability to control for other possible confounders.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      I would recommend doing some experiments to test the fitness effects of pT181 in multicopy and integrated into an isogenic S. aureus strain. Simple growth curves with and without tetracycline would be extremely informative.

      We think that this is an interesting scientific question but is beyond the scope of this paper.

      Reviewer #2 (Recommendations for the authors):

      Major:

      (1) L160 and Figure 1:

      To what extent is this decrease in pT181 prevalence related to a delay between isolate collection and sequence upload to public databases? In my own work, I have found an average of 2 years difference in the sequence collection and sequence upload date of GenBank sequences. This could explain the decreasing numbers in recent years and may possibly skew relative proportions of pT181 containing/or plasmid-free strains.

      There are fluctuations in collection rates over the years which definitely do not correspond to actual fluctuations in S. aureus prevalence in the population. We would expect delays in uploads in both plasmid-containing and plasmid-free strains, so we would not anticipate a decline in estimated plasmid prevalence due to this delay; however, it could be somewhat noisy for more recent years.

      The large peak of S99.5_27 around 2009 seems oddly reminiscent of targeted sampling during a hospital outbreak, or so? Did you do any checks on where these genomes came from? Could this affect any of the downstream results?

      The 2008 peak in S99.5_27 comes from a single BioProject (PRJEB4140), which contributed approximately 1,000 samples to our analysis. Based on the BioProject description, this BioProject aimed to characterize diversity in S. aureus ST239 diversity in Thailand. We performed the single-copy analysis with this strain excluded and still got the same result that integration has increased over time, so we feel that this is acceptable and should not unduly impact downstream results. We have clarified the results section to more explicitly state that this is the sampling peak that was excluded (L306-311).

      (2) Figure 3: If I understand the analysis correctly, all mutation rate and phylogenetic analyses were conducted based on comparison to a single reference genome. This can bias results: https://academic.oup.com/mbe/article/31/5/1077/2925634 . Please comment.

      Yes, SNPs were calculated relative to a reference genome. We understand this could bias results. However, it is standard practice in the field and we do not think it changes the main findings of the paper.

      We have taken the reference-free SKA alignment and the SKA alignment mapping to a reference plasmid and calculated the SNP distances between all plasmid pairs with the tool snp-dists (Seemann et al.). For given plasmid pairs, the distributions are different by Wilcoxon signed-rank test with continuity correction (p < 2.2 x 10<sup>-16</sup>) though this is due in part to the large sample size for pairwise comparison. The median and modal difference between methods is 0 SNPs detected. The average is 0.1 more SNPs detected in the reference-free method than the mapping method. We have added this analysis to the methods section (L505-511).

      (3) I am not fully convinced by the analysis in Figure 6 (i.e. that the pT181 copy number has declined over time). It is rather confusing how the authors account for strain and bioproject-related influences on their primary regression (L298-306).

      We have edited the explanation of the GLMM in the results section (L320-323). We have moved some of the explanation to the methods section (L592-605).

      (a) What does this analysis look like without S99.5.2?

      The slope is still negative and significant with S99.5_2 excluded. We have added this to the results (L327-328).

      (b) In line 296, it is made clear that 2 separate analyses were carried out, but in the subsequent paragraphs (starting 298 and 315), it would be helpful to repeat that each looks at only one component.

      We have edited this section to explicitly state that separate regressions were carried out for each component (L298-300).

      (c) Figure 6 should include error bars that reflect the different number of samples per collection year (please also comment on how this influences the power/validity of the linear regression!).

      We have modified Fig. 6A to show samples collected per year as the color of the point. Samples collected per year can also be viewed in Fig. 1. In addition, we have changed to logistic regression to assess single-copyness as a function of collection year. The error bar on the regression curve shows the SE range. While there are many more samples collected in recent times than in the more distant past, we still think the signal is real. It does put more emphasis on each early sample. However, the genomic data matches early descriptions of tetracycline resistance in S. aureus being plasmid-mediated, not chromosomal (Gillespie et al.).

      (4) Strains that were isolated in the 60s were presumably sequenced at a much later point in time. Were they grown and isolated from their respective host bacteria following similar protocols as present-day isolates? Growth conditions can have massive effects on PCN, and selective PCR amplification on the relative number of plasmid-related reads. How do you account for this? [Figure 7/8].

      Yes, samples that were collected in the 1960s were sequenced roughly 50 years later. The date of collection could impact storage conditions for the isolate. However, they were grown up for sequencing and actually sequenced much closer together and should have the same growth conditions as isolates collected at a more recent date. Underlying our model of PCN is that it is a property of the isolate and will not fluctuate over time in storage.

      Minor:

      (1) This study is a nice demonstration of the type of genomic epidemiology that can be conducted now that genomes are sequenced and shared more widely. This is already somewhat common for clinically relevant sequence types of pathogenic bacteria, but I have not seen it much for plasmids. This could be nice to highlight. Stressing this more clearly in the abstract and introduction may broaden the audience of this work.

      We have described our approach as genomic epidemiology in the first paragraph of the introduction (L72).

      (2) More generally, the introduction is quite winding. A lot of interesting information is mentioned, but without a clear narrative structure as to why this is important for the study. Some editing may strengthen the message of the paper and invite more people to read it. For instance, starting each paragraph with a topical sentence about the general message the paragraph should convey. Yet, this is entirely a style/personal taste remark, and I leave it to the authors to decide whether to make these changes.

      We have made edits to restructure the text.

      (2a) Similar comment for the discussion (possibly some discussion could be put in the supplement too).

      We have made edits to restructure the text, but have chosen to leave the content in the Discussion section. Additional references to previous research have also been added (L386-388).

      (3) L125: Could you include a reference for this statement?

      We have added a reference for this statement (L109).

      There is interesting existing work on the evolution of genes on multi-copy plasmids (and the evolution of copy-number itself), which seems more pertinent here than the segregation mechanisms of low-copy-number plasmids.

      We have chosen to keep the general background on plasmid copy number regulation and segregation, to keep the paper approachable to readers who have no background on plasmid biology. We have added additional references to work on evolvability of multicopy plasmids and their copy number (L117-120).

      (4) The references are a bit of a mess. Certain entries are in all caps, others are missing titles, etc. I would recommend looking this over again carefully.

      We have resolved this issue.

      (5) L187 CDS is used in line 187 but not defined as a term until line 201.

      We have defined CDS with first usage (L188).

      (6) L189: Do you have any estimate of the error around 1.15 mutations/Mb/year from the linear regression?

      We have added standard error for the 1.15 mut/Mbp/year from the regression to the results (L191): SE = 0.3 mut/Mbp/year.

      (7) Figure 2: It would be helpful to have a visual indication of which areas the authors consider hypervariable.

      We have added a black dash underneath the hypervariable regions on the plot.

      (8) Figure 5: The two colors of grey are hard to distinguish.

      The grey for shared genes has been made darker to better distinguish them.

      (9) L285: Why do you write "could assume the copy number of the larger element"? What other options are possible?

      We have expanded on this section to elaborate on the ways that copy number could be changed by cointegration, and added an additional citation to support these claims (L276-280).

      (10) Figure S1: What does this scale mean? What are the units? This figure is uninformative as it stands. I would possibly consider labelling the tips.

      We have modified the figure and legend to indicate that the scale is in substitutions per site. We are providing these figures to give some idea of scale and shape, showing how star-like they are. Unfortunately, tip labels are illegible on these trees given the large number of samples.

      References

      Gillespie, M. T., et al. “Antibiotic Susceptibilities and Plasmid Profiles of Nosocomial Methicillin-Resistant Staphylococcus aureus: A Retrospective Study.” Journal of Medical Microbiology, vol. 17, no. 3, June 1984, pp. 295–310. DOI.org (Crossref), https://doi.org/10.1099/00222615-17-3-295.

      McCarthy, Alex J., et al. “Extensive Horizontal Gene Transfer during Staphylococcus aureus Co-Colonization in Vivo.” Genome Biology and Evolution, vol. 6, no. 10, 2014, pp. 2697–708, https://doi.org/10.1093/gbe/evu214.

      Seemann, Torsten, et al. Snp-Dists. https://github.com/tseemann/snp-dists.

    1. Author response:

      Reviewer #1 (Public review):

      Summary:

      This manuscript reports exceptionally preserved, millimeter-scale segmented bilaterian microfossils from the Fortunian Kuanchuanpu Formation in South China. The authors propose that these non-biomineralized animals were preserved through microbial pseudomorphs rather than direct phosphatization, filling a critical taphonomic and evolutionary gap in early animal segmentation.

      Strengths:

      This paper filled the critical taphonomic and evolutionary gap in early animal segmentation.

      Weaknesses:

      Extremely similar work has already been published by Xian et al., 2026, PNAS, with specimens from absolutely the same formation, and they also proposed that these animals are segmented. So in this context, this work's significance is eclipsed.

      Thanks the reviewer for the constructive comments. In Xian et al., 2026, PNAS, the taphonomic mechanism has not been explained in details and in our manuscript we propose the mode that how microbes pseudomorph the entire bodies of micro-animals. In addition, the specimens we presented in this manuscript demonstrate the abundance and diversity of segmented bilaterians in the basal Cambrian. In the revision, we will majorly discuss the evolution of body segment based on our new materials and add a new figure to complement the comparison of microbial pseudomorphs vs Ediacaran-type and Burges-Shale type.

      Reviewer #2 (Public review):

      Summary:

      The manuscript by Yang and authors presents an interesting set of new microfossils from the early Cambrian of South China. These are interpreted as segmented bilaterians, and so may be the oldest such examples in the fossil record, with implications for our understanding of early animal evolution. Further, the preservation of these fossils as microbial pseudomorphs is a unique pathway to fossilize such important organisms.

      Strengths:

      The fossils are impressive and arguments for their affinities as segmented bilaterians are convincing. Discussion of somewhat novel preservation is detailed and helpful to understand this taphonomic mode.

      Weaknesses:

      It needs to be clear what the authors' definition of a "segment" is and how that matches (or not) other interpretations. Arguments by Hannibal and Patel (2013, EvoDevo) convincingly define all segmented organisms based on polarity within repeated units of bilaterally symmetrical animals, but others may disagree. The manuscript would benefit from discussion of this in the introduction, laying out a hypothesis for what we might expect to find as evidence of the earliest segmented animals and then describing these new fossils within that context.

      As it currently reads, the definition of a segment is not presented until the discussion and is somewhat ambiguous, seemingly referring to any organism with bilateral symmetry and repeated units. However, modern (e.g. tardigrades) non-segmented animals exhibit these features but are not considered truly segmented. This is critical as various Precambrian fossils (Arborea (Dunn et al., 2019, Palaeontology); Cloudina (Schiffbauer et al., 2020, Nature Communications) Dickinsonia (Gold et al., 2015, Evolution and Development); Parvancorina (Darroch et al., 2017, Biology Letters); Spriggina (Evans et al., 2026, Scientific Reports); Yilingia (Chen et al., 2019, Nature) etc.), have been argued to possess bilateral symmetry ad have bodies composed of repeated units. These older examples should be acknowledged and discussed in detail. Stating that "the identity of these [Precambrian] organisms is controversial" (line 51) is not justification for the main claims of this paper, and it should be clear what distinguishes the new fossils from previously proposed evidence of earlier segmented bilaterians. I believe there is a case to be made in support of the authors' claims, but this context is vital to make that argument convincingly. It is also worth discussing evidence of segmented bilaterians in the early Cambrian trace fossil record, such as Treptichnus pedum (Kesidis et al., 2019, Proceedings B) and Rusophycus (Daley et al., 2018 PNAS), that may predate or be roughly coeval with these fossil remains.

      Thanks for the valuable suggestions and references from the reviewer. In the revision, we will introduce the definition of segment and former researches in the introduction part as suggested. And we will discuss the comparisons of our specimens with the Precambrian fossils mentioned above in more detail. The major difference between our materials and Spriggina and Yilingia is the undisputed bilateral symmetry. While the paired appendages distinguished the Cambrian fossils from Parvancorina, Cloudina, and Dickinsonia. Since the pseudomorphing mechanism caused the lost of internal structures of the original, the well-developed paired appendages and outer segment could be the major evidence of their identity. In addition, we will make a more detailed introduction and discussion on the trace fossils of during the Ediacaran-Cambrian transition.

    1. Author response:

      The following is the authors’ response to the original reviews.

      eLife Assessment

      This valuable study compares hippocampal-cortical functional connectivity to various other brain measures and examines their development across youth. It uses sophisticated analyses replicated in multiple datasets, but provides incomplete evidence to support the primary claim that hippocampal-cortical connectivity relates to cognitive maturation. The manuscript would benefit from a more nuanced consideration of the biological basis of some of the derived imaging measures and the limitations of the cross-sectional design. This work will be of interest to neuroimaging specialists and cognitive neuroscientists.

      We thank the Editors for credits on the value of the multimodal, multi-dataset design and the study’s relevance to cognitive neuroscience. We have revised the manuscript in three corresponding ways:

      (1) Connectivity–cognition interpretation. We now state explicitly that the hippocampal-cortical connectivity–cognition findings are age-related associations with cognitive measures during youth. They do not demonstrate that hippocampal-cortical connectivity causes, mediates, or fully explains cognitive maturation.

      (2) Biological interpretation of imaging measures. We refined the interpretation of derived imaging measures throughout the manuscript. T1w/T2w is described as an indirect, myelin-sensitive but non-specific MRI contrast that may reflect multiple tissue and acquisition factors, rather than direct myelin content. Similarly, transcriptomic findings are described as cross-dataset spatial associations rather than evidence of developmental molecular mechanisms. Consistent with recent guidance on neuroimaging data contextualization, the interpretation of these associations is constrained by the characteristics of the reference atlas and by cross-dataset spatial alignment[1].

      (3) Limits of cross-sectional evidence. We added an explicit limitation that the cross-sectional design does not measure within-person developmental change and cannot establish temporal ordering or causal relationships.

      Together, these revisions address the evidential limitations identified in the Assessment while preserving the supported contribution of the replicated multimodal associations.

      Reviewer #1 (Public Review):

      Summary:

      The authors studied the development of hippocampal connectivity gradients based on open datasets and performed correlation analyses with other MRI features as well as gene expression information from other datasets. Although the main findings are correlational and cross-sectional, the analyses are overall sophisticated and replicated in several datasets.

      Strengths:

      The hippocampus is a key region in understanding large-scale brain organization and cognition, and the authors applied advanced and suitable analytics to study its development. The paper is overall well-organized and well-written, and the findings are relevant for studying large-scale brain development.

      Weaknesses:

      While sophisticated, several of the analyses appear mainly correlational, cross-sectional, and rely on cross-dataset contextualization, which should also be stated as a limitation of the current work.

      We are grateful to Reviewer #1 for recognizing the importance of the hippocampus, the suitability of the analytical framework, and the value of the replicated developmental design. We agree that the public-review concern about correlational, cross-sectional, and cross-dataset evidence is central to how the findings should be interpreted. In particular, consistent with recent recommendations for neuroimaging data contextualization, we now explicitly identify the transcriptomic component as group-level spatial contextualization and state that its interpretation is limited by the properties of the adult post-mortem reference atlas and by cross-dataset spatial alignment[1]. It therefore cannot provide individual-level developmental inference or establish causal molecular mechanisms. We have addressed these boundaries in detail in our response to Reviewer #1, Recommendation 1, and in the revised Limitations section, so that the same qualification is applied consistently throughout the manuscript.

      Revised manuscript text (Page 29-30): “Although key findings were replicated across two independent longitudinal datasets, the primary developmental analyses were cross-sectional and therefore did not measure within-person change. The absence of pubertal hormone measures in the HCP-D dataset also limited assessment of hormonal contributions to the observed age-related associations. The observed patterns should be interpreted as age-related associations rather than individual developmental trajectories or causal developmental mechanisms. T1w/T2w intensity was treated as an indirect, myelin-sensitive MRI proxy influenced by multiple tissue and acquisition factors, not as direct histological myelin content. Transcriptomic results were based on post-mortem samples from a separate dataset and were interpreted as cross-dataset spatial associations rather than developmental mechanisms. More generally, the interpretation of such cross-dataset map correspondence is constrained by the properties and representativeness of the source atlas and by cross-dataset spatial alignment[1]. These limitations motivate future longitudinal, multimodal, and biologically validated studies.”

      Reviewer #1 (Recommendations for the Authors):

      (1) Some language suggests causality, but the associated findings were mainly derived from correlational analysis. I would suggest verifying the wording and toning down causal terms ('shape', 'impact', 'linked' ...).

      We thank the reviewer for identifying this important mismatch between the strength of the wording and the correlational nature of the evidence. We have completed a manuscript-wide terminology review and replaced causal or mechanistic verbs with relational language throughout the Abstract, Introduction, Results, Discussion, and figure captions. We have used terms such as associated with, corresponds to, covaries with, and is consistent with when describing relationships among gradients, geometry, T1w/T2w intensity, transcriptomic measures, and cognition. Stronger terms have been retained only when they describe a mathematical operation or the construction of an analysis, and the revised Discussion now explicitly states that cross-sectional associations do not establish directionality or causation.

      (2) Please also provide the following citations when referring to hippunold: https://elifesciences.org/articles/88404 (which describes additional advanced registrations). If the authors have the ability to quickly rerun some processing, then I would recommend a sensitivity analysis based on hippunfold v2, which also provides more homogenous vertex spacing, fewer distortions during unfolding, and some additional improvements.

      We thank the reviewer for pointing out the missing registration reference and for recommending a HippUnfold v2 sensitivity analysis. We have added the requested eLife study on surface-based hippocampal registration and have included the relevant surface-generation and registration procedures for our study.

      We carefully considered reprocessing the data with HippUnfold v2. The official release notes indicate that v2 includes important changes to surface precision, surface re-tessellation, Laplace coordinate generation, and robustness to topological breaks. These changes could affect surface coordinates and the precise spatial sampling of imaging data. A meaningful v2 sensitivity analysis would therefore require reprocessing the original MRI data and repeating the downstream connectivity, gradient, developmental, cognitive, and cross-dataset analyses. We did not perform this complete reprocessing in the present revision because it would represent a new version-wide analysis rather than a limited sensitivity check.

      We did not consider a partial rerun of selected downstream analyses to provide a sufficiently informative or internally consistent test of version sensitivity. Rather than present an incomplete comparison, we retained the original HippUnfold v1.2.1 pipeline, explicitly identified version dependence as a limitation, and removed wording that could imply that the findings are fully insensitive to preprocessing choices.

      We appreciate that a preregistered comparison across HippUnfold versions would be valuable in future work, particularly for analyses in which fine-scale surface correspondence or registration precision is the primary scientific focus.

      Revised manuscript text (Page 33): “We employed HippUnfold (v1.2.1)[2] (https://hippunfold.readthedocs.io; advanced surface-registration procedures are described by DeKraker et al.[3]), which integrated a deep learning method with a topological constraint strategy.”

      (3) Are there changes in motion parameters across developmental time windows/age? Are findings consistent when fMRI motion parameters are regressed out in the statistical models, and do the 3 derived gradients correlate with head motion?

      We thank the reviewer for raising this important potential confound. We noted that the original developmental GAMs already included mean framewise displacement (mFD). First, we tested whether head motion changed with age. In the 601 included HCP-D participants, we fitted mFD as the outcome using mFD ~ s(Age, k = 4) + Sex + site + s(hemi,bs = “re”) with REML estimation. mFD showed a robust nonlinear decrease with age (edf = 2.66, F = 125.13, smooth-term p < 2.2 × 10<sup>-16</sup>; likelihood-ratio p < 2.97 × 10<sup>-78</sup>; Supplementary Fig. 3a). Importantly, the original developmental models for hippocampal gradient statistics already included mFD as a covariate. We therefore directly examined the mFD coefficients from those same 18 models, which used Feature ~ s(Age, k = 4) + Sex + site + s(hemi,bs = “re”) + <mFD.

      After Benjamini–Hochberg correction across the 18 mFD coefficients, mFD was associated with explained variance for lLG (β = −0.0412, SE = 0.0147, FDR q = 0.047) and qLG (β = 0.0280, SE = 0.00818, FDR q = 0.011), but with nocIG feature (all FDR q ≥ 0.101; Supplementary Fig. 3b). Thus, head motion is strongly age-related and is associated with a limited subset of the analyzed gradient-distribution features, supporting its inclusion as a covariate. The developmental effects reported in Figure 2e–f are already estimated after adjustment for mFD; we do not claim that every gradient feature is motion-independent.

      Revised manuscript text

      (Page 9): “We fit the model with a smooth term for age as a fixed effect; sex, scanning site, and in-scanner head motion (mean framewise displacement, mFD) as linear covariates”

      (Page 10): “The age-related mFD trajectory and direct mFD coefficients from the original gradient feature models are shown in Supplementary Fig. 3.”

      (4) Did the authors also observe morphological changes in the hippocampus? Are there changes in hippocampal cortical thickness that could explain some of the changes in functional coupling as well?

      We thank the reviewer for this important suggestion. We performed additional HippUnfold surface-morphology analyses and a thickness-adjusted reanalysis of the same gradient features examined in Figure 2 and Extended Data Fig. 4. Morphological measures were calculated separately for each hemisphere after pooling the hippocampal-proper (label-hipp) and dentate-gyrus (label-dentate) surfaces. Thickness, curvature, and gyrification were native-surface-area-weighted, surface area was summed across both labels, and left-hemisphere curvature was sign-oriented to match the right-hemisphere convention.

      For each morphology measure, we fitted Metric ~ s(Age, k = 4) + Sex + site + s(hemi,bs = “re”) in 601 included participants, using the same GAM framework as the primary gradient-feature analyses but without mFD. Thickness, oriented curvature, gyrification, and surface area all showed age-related change after FDR correction (all q ≤ 0.000304). Hippocampal thickness decreased from childhood through adolescence and then plateaued, whereas surface area and gyrification increased before reaching late-adolescent plateaus.

      To test whether morphology accounted for the functional findings, we refitted each of the 18 original gradient feature models with hemisphere-matched thickness added: Feature ~ s(Age, k = 4) + Sex + site + s(hemi,bs = “re”) + <mFD + thickness. No individual thickness coefficient survived FDR correction across the 18 features (minimum q = 0.061). Thus, developmental changes in hippocampal and dentate morphology are present, but surface thickness does not account for the principal age-related functional gradient effects.

      Revised manuscript text (Page 10):

      “Given the age-related variation in hippocampal functional-gradient features, we next assessed whether concurrent changes in global hippocampal morphology could account for these patterns. Surface-area-weighted thickness, curvature, gyrification, and surface area of the pooled hippocampal proper and dentate gyrus showed significant age-related associations (Supplementary Fig. 5). However, after adding hemisphere-matched thickness to the corresponding hippocampal gradient feature models, no thickness association survived FDR correction (minimum q = 0.061). Thus, although global hippocampal morphology changes across youth, these results do not support global thickness as an explanation for the primary functional-gradient patterns.”

      (5) The authors corrected for sex in several of their models. It would be interesting to show, in a supplemental form, sex-disaggregated analyses that outline the consistency and/or potential shifts in developmental patterns in males and females.

      We thank the reviewer for this valuable suggestion. We first performed formal sex-by-age interaction tests in the three existing main-text age-GAM families, rather than introducing new outcomes. For each outcome, we compared the original additive model, Measure ~ s(Age, k = 4) + Sex + site + s(hemi,bs = “re”) + <mFD, with a sex-specific age-trajectory model, Measure ~ s(Age, k = 4) + Sex + site + s(hemi,bs = “re”) + <mFD. Nested-model interaction tests were conducted using ML fits, whereas the displayed trajectories were estimated with REML, consistent with the primary analyses.

      After BH correction within each original analysis family, sex-by-age interactions were detected only for three Figure2 gradient-distribution features:lLG explained variance (q = 0.00272), cIG range (q = 0.0449), and cIG standard deviation (q = 0.0449). No interaction survived correction among the six Figure 3 hippocampus–cortical-hierarchy measures or the three Figure 4 geometry–function coupling measures.

      In the sex-specific trajectories, the clearest difference concerned lLG explained variance: females showed a lower childhood level followed by a steeper increase and higher adolescent values, whereas males exhibited a more gradual increase. For cIG range and standard deviation, both sexes showed broadly similar inverted-U-shaped trajectories; the male trajectory was modestly higher through mid-to-late adolescence, with substantial overlap of the confidence intervals. The original combined-sex trajectory lay between, or closely followed, the two sex-specific curves. Thus, the principal developmental patterns are broadly consistent across sexes, while sex-related shifts are limited to a small subset of gradient-distribution features.

      Revised manuscript text (Page 10):

      “We additionally tested sex-by-age interactions across the previously reported developmental models. After FDR correction, significant interactions were identified for lLG explained variance and the range and standard deviation of cIG, whereas no sex-by-age interaction survived correction for the remaining primary developmental outcomes. Sex-disaggregated trajectories for these significant interactions are shown in Supplementary Fig. 4.”

      (6) There have been reports of some distortions in inferior temporal regions after non-linear alignment to standard space in the HCP processing, which may affect hippocampal data sampling. Did the authors verify registration accuracy and absence of such distortions in their samples?

      We thank the reviewer for raising this important concern regarding potential registration-related distortion. We clarified the registration and sampling chain and now explicitly distinguish native-space signal sampling from the subsequent use of a common coordinate system for group-level correspondence.

      Crucially, the hippocampal fMRI time series were sampled in each participant’s native space: BOLD data were mapped back to the native anatomical space and sampled within the participant-specific hippocampal grey-matter ribbon onto the native HippUnfold mid-thickness surface. Likewise, hippocampal T1w/T2w measurements were sampled from the participant-specific native hippocampal surfaces. Thus, neither the fMRI nor the T1w/T2w hippocampal measurements was obtained by sampling voxels after nonlinear transformation into a standard medial-temporal-lobe space. This design avoids standard-space deformation influencing the extraction of these hippocampal signals and intensity measures. The subsequent common surface coordinate is used to establish vertex correspondence across participants for group-level analyses, rather than to define the native-space signal samples themselves.

      We also performed visual quality control of the HippUnfold registration and surface reconstruction, inspecting the alignment of each participant’s hippocampal segmentation and reconstructed surfaces with the native T1-weighted anatomy. The documented mask-overlap quality-control procedure further showed Dice coefficients above 0.7. The paired inner and outer surfaces define the mid-thickness sheet used for ribbon-constrained sampling, which is particularly suitable for the variable folding geometry of the hippocampus.

      (7) Can the authors clarify how gene expression was analyzed for the hippocampus? Were HippUnfold models run across all donors separately, and probes were then sampled and co-registered? How did the authors handle data sparsity?

      We thank the reviewer for this request for clarification. The full hippocampal transcriptomic workflow is described in the Methods subsection “Transcriptomic association analysis of the hippocampal gradients”. We clarify the procedure here to make the correspondence between the Allen Human Brain Atlas (AHBA) samples and the hippocampal gradients explicit.

      We used AHBA microarray data from six donors. Donor-specific age- and sex-related effects were regressed from each probe before the normalized residual expression values were combined. We selected samples annotated as CA1, CA2, CA3, CA4, subiculum, or dentate gyrus from both hemispheres, yielding 188 hippocampal samples. The participant-specific native HippUnfold mid-thickness surfaces were transformed to MNI space and averaged to generate the group template mid-thickness surfaces. Each AHBA hippocampal sample was then matched to its nearest vertex on this template. Fifteen samples located more than 6 mm from the template surface were excluded, leaving 173 samples from six donors. The group-averaged hippocampal gradient value at the matched template vertex was assigned to each retained tissue sample.

      We then used LASSO-PCR to model each gradient from the 173 × 58,692 normalized expression matrix. Principal-component analysis was first used to represent the correlated probe-expression structure, and LASSO regression was fitted on the retained component scores. The penalty parameter was selected by nested five-fold cross-validation, and generalizability was evaluated using ten repeated ten-fold cross-validation. Probe weights were subsequently reconstructed from the fitted component weights for the feature-deconstruction and enrichment analyses.

      Thus, the transcriptomic analyses are group-template spatial associations between adult post-mortem AHBA samples and the group-averaged hippocampal gradients. They are not donor-specific developmental measurements, nor do they establish a causal molecular mechanism. We have retained the complete methodological description in the Methods subsection cited above and clarify the workflow here for ease of reference.

      Reviewer #2 (Public Review):

      Summary:

      In this manuscript, the authors aim to assess how the functional organisation of the hippocampus is related to the geometry and neurobiological differences of the hippocampus. In particular, the authors focus on the first three eigenvectors of hippocampal-cortical functional connectivity, based on non-linear dimensionality reduction on resting-state functional MRI data. Furthermore, the work aims to describe changes in these functional axes and their relation to other factors throughout youth and evaluate whether they are predictive of individual variations in cognition.

      Strengths:

      A major strength of this study is the attempt to replicate key findings across multiple developmental cohorts.

      Weaknesses:

      The major weaknesses of the manuscript center on gaps in technical transparency and several conceptual inaccuracies. The machine learning methodology used for cognitive prediction is scarce, leaving little means to evaluate whether the behavioral results suffer from data leakage or overfitting. The introduction sets up an oversimplified historical premise regarding the field's understanding and appreciation of hippocampal connectivity, and contains several incorrect references that throw doubt on the argumentation. Additionally, T1w/T2w signal intensity is incorrectly used as synonymous with myelin, despite gold-standard histological validation showing a non-significant correlation between T1w/T2w and myelin staining (Sandrone et al., 2013).

      Appraisal of Aims and Conclusions:

      The authors partially achieve their aims by illustrating certain age-related changes in hippocampal function; however, the correlative study design is not equipped to examine how these changes are "shaped" by geometry, myelination, or gene expression (especially the latter two). Furthermore, conclusions were often overstated based on small effect sizes.

      Context and Field Impact:

      This work adds to a growing body of literature focused on gradient-based representations of hippocampal topology. By applying these methods across a wide developmental age bracket, it provides a useful reference point for how the hippocampus and wider cortex interact during maturation. To improve utility to the neuroimaging and cognitive neuroscience communities, the nesting of subfields within the eigenvector topology should be addressed, too.

      We thank Reviewer #2 for the careful assessment and for recognizing the value of replicating key findings across multiple developmental cohorts. We have addressed the specific concerns regarding cognitive prediction, historical framing, biological interpretation, effect-size interpretation, citation placement, and T1w/T2w signal in the detailed responses below. These revisions expand the prediction methods, clarify the interpretation of hippocampal gradients and subfields, recalibrate the developmental claims, and improve the precision of the supporting citations.

      We also thank the reviewer for raising the need for a more precise interpretation of T1w/T2w signal. We agree that T1w/T2w intensity should not be used synonymously with myelin, and we have revised the manuscript throughout to refer to it as a myelin-sensitive but non-specific MRI contrast that may reflect multiple tissue properties. We respectfully clarify the interpretation of the cited Sandrone et al. study. We believe that the intended reference is Sandrone et al. (2023)[4], rather than 2013. This study tested the correspondence between T1w/T2w and Luxol Fast Blue staining specifically in corpus-callosum white matter; it did not include cortical gray matter or hippocampal tissue. Its callosal analysis did not show the expected positive correspondence between T1w/T2w and histological myelin staining (indeed, it reported a significant inverse correlation), but this result cannot establish the validity or invalidity of T1w/T2w as an index of myelin-sensitive microstructural variation in hippocampal gray matter. The authors also distinguished this white-matter result from prior evidence of cortical co-localization between high T1w/T2w signal and myelin-rich regions.

      Accordingly, we do not interpret our hippocampal T1w/T2w findings as direct measurements of myelin content or cellular myelination. Rather, they indicate associations with an indirect MRI contrast that is sensitive to myelin-related, as well as other, tissue properties. We have revised the relevant Introduction, Results, Discussion, figure text, and Methods language to reflect this distinction.

      We thank the reviewer for highlighting the importance of considering how hippocampal subfields are nested within the connectivity-eigenvector topology. This question has been addressed in our related subfield-specific study using the same HCP-D cohort and HippUnfold surface framework. We explicitly examined the distribution of the two long-axis gradients across the cytoarchitectonic subfields (Sub, CA1, CA2/3, and CA4–DG), their distinct cortical-connectome organization, and their associations with episodic memory (Zeng et al., 2025[5]). We have added a citation to this work to provide the relevant subfield-level context. The present study focuses on the continuous whole-surface organization and developmental trajectories of the three hippocampal functional gradients.

      Revised manuscript text (Page 29):

      “Continuous hippocampal gradients and cytoarchitectonic subfields

      The continuous whole-surface topology examined here should not be viewed as separate from hippocampal cytoarchitectonic subfield architecture. Rather, it characterizes hippocampal-cortical connectivity organization across the unfolded hippocampal surface, including variation that extends across subfield boundaries. The proximal-distal association of cIG provides one link between this continuous topology and the Sub-CA-DG axis. Complementing the present whole-surface analysis, our recent subfield-specific study of the same HCP-D cohort examined how the two long-axis gradients are distributed across Sub, CA1, CA2/3, and CA4-DG. It further showed that their subfield-specific cortical-connectome organization was associated with episodic memory[5]. Taken together, these findings indicate that hippocampal functional gradients provide a unifying framework that relates continuous topology and cytoarchitectonic architecture to hippocampal-cortical network organization, developmental reconfiguration, and cognition.”

      Reviewer #2 (Recommendations for the Authors):

      (Methodological and Statistical Revisions)

      (1) Prediction of Cognitive Performance:

      Provide a comprehensive, step-by-step description of the machine learning pipeline used for cognitive prediction. Explicitly specify the features extracted, the exact estimator employed, the cross-validation strategy, and the precise measures taken to prevent data leakage.

      We thank the reviewer for requesting clarification of the cognitive prediction analysis. We have added a dedicated Methods subsection describing the prediction framework and its safeguards against data leakage. We used hippocampal–cortical projection features to estimate episodic memory, cognitive flexibility, working memory, and inhibitory control, while including age, sex, scanning site, and mean framewise displacement as linear covariates.

      To address the high dimensionality and correlation structure of the projection features, we used a PCA–LASSO framework. PCA generated component scores from the hippocampal–cortical projection features, and LASSO regression was fitted to these scores. The LASSO regularization parameter was selected using nested five-fold cross-validation.

      Predictive performance was evaluated with age-balanced 10-fold cross-validation, using rounded age solely to stratify the outer folds. To prevent information leakage, all data-adaptive steps were completed using only the outer training data. These steps included feature transformations, estimation of linear covariate effects, PCA, and LASSO penalty selection. The fitted processing steps and model were then applied to the held-out fold. Performance was quantified by the squared Pearson correlation between cross-validated predicted and observed cognitive scores. We applied FDR correction across the 12 resulting gradient–cognition tests.

      Revised manuscript text (Page 37-38):

      “Cognitive prediction analyses

      We used hippocampal–cortical projection features to predict episodic memory, cognitive flexibility, working memory, and inhibitory control. Age, sex, scanning site, and mean framewise displacement were included as linear covariates.

      The model used a PCA–LASSO framework to address the high dimensionality and correlation structure of the projection-feature matrix. Principal-component analysis generated component scores from the hippocampal–cortical projection features. LASSO regression was then fitted to these scores.

      Predictive performance was evaluated using age-balanced 10-fold cross-validation. Rounded age was used solely as the stratification label for the outer folds. Within each outer training fold, feature transformations, principal-component estimation, linear covariate effects, and LASSO penalty selection were fitted using training data only. These fitted transformations and model parameters were then applied to the held-out fold. Thus, held-out participants did not contribute to feature preprocessing, covariate estimation, component construction, or model tuning.

      The LASSO regularization parameter was selected using nested five-fold cross-validation within each outer training set. Predictive performance was quantified as the squared Pearson correlation between cross-validated predicted and observed cognitive scores. We tested 12 gradient–cognition pairs from three hippocampal gradients and four cognitive measures. False-discovery-rate correction was applied across all resulting p-values.”

      (2) Integration of Core Statistics:

      Move the relevant test statistics, degrees of freedom, and FDR-corrected p-values for primary developmental claims from the Extended Data figures into the main text body to ensure transparency.

      We thank the reviewer for emphasizing the need to make the statistical evidence underlying the extended developmental displays directly traceable. We have now added quantitative reporting for the three gradient-distribution features displayed in Extended Data Fig. 4 but not in Figure 2e, f. Specifically, the revised Results text reports the FDR-corrected age-related changes in range, skewness, and kurtosis.

      We also created Supplementary Data 1 for the parcel-wise developmental trajectories shown in Extended Data Fig. 5f. This table provides the GAM statistics for all 360 cortical parcels for each hippocampal gradient, including the age-smooth F statistic, Δ adjusted R<sup>2</sup>, raw and FDR-adjusted p values, and Yeo seven-network assignment. We added an explicit reference to this table immediately after the Extended Data Fig. 5f citation in the Results. These changes enable readers to inspect the numerical evidence underlying the Extended Data displays without inferring statistics from the figures alone.

      Revised manuscript text

      (Page 10):

      “Beyond these features shown above, the ranges of lLG and qLG changed with age (lLG: ΔAdj. R<sup>2</sup> = 0.0098, p = 0.0017; qLG: ΔAdj. R<sup>2</sup> = 0.0044, q = 0.0148). lLG skewness and lLG / qLG kurtosis also changed with age, whereas qLG skewness and all three cIG measures did not survive FDR correction across the six distributional features of each gradient (Extended Data Fig. 4).”

      (Page 15):

      “Complete parcel-wise GAM statistics are provided in Supplementary Data 1.”

      (3) Signal-to-Noise Ratio (SNR) Justification:

      Provide an analytical justification demonstrating why vertex-wise probing at a 483-vertex density within the hippocampus does not suffer from too severe spatial oversampling or low SNR problems.

      We thank the reviewer for raising the important concern that a dense hippocampal surface representation could create spatial oversampling or unstable vertex-level measurements. We have now added a quantitative assessment of the native HippUnfold mesh spacing. The 483-vertex representation is the den-2mm HippUnfold template, comprising 419 hippocampal and 64 dentate vertices per hemisphere. We measured distances between adjacent vertices on all 2,608 un-smoothed native T1w mid-thickness surfaces from the 652 HCP-D participants. Across 1,765,616 unique mesh edges, the pooled median distance was 2.01 mm (IQR, 1.43–2.57 mm), and 78.3% of edges were between 1 and 3 mm. Thus, the native mesh is centered on the 2-mm spatial scale of the BOLD acquisition rather than constituting a submillimeter sampling grid. The remaining local variability reflects individual anatomy and the triangular surface geometry. These results are shown in Supplementary Fig. 7.

      We noted that BOLD data were sampled in each participant’s native anatomical space using partial-volume-weighted ribbon-constrained mapping between the paired inner and outer hippocampal surfaces. Each vertex value is therefore a weighted estimate from voxels within the hippocampal grey-matter ribbon, rather than a nearest-voxel sample. Importantly, the 483 vertices were not treated as independent fMRI observations. Spatial dependence among neighboring vertices is expected, whereas the developmental inference was performed on participant-level gradient-derived features and cortical-projection measures, with sex, site, hemisphere, and mean framewise displacement included as covariates. Replication of the principal organizational patterns in the independent NKI-RS and CBD samples provides additional evidence that the reported gradient findings are unlikely to be materially driven by low-SNR or spatial-oversampling artefacts.

      Revised manuscript text (Page 35): “The vertex spacing was set at approximately 2 mm, close to the 2.0 mm isotropic fMRI voxel size. The distribution of distances between adjacent vertices across all native-space mid-thickness surfaces was centered near this target spacing (median, 2.01 mm; interquartile range, 1.43–2.57 mm; 78.27% of edges, 1–3 mm; Supplementary Fig. 7).”

      (4) Justification for Eigenvector Exclusion:

      Strengthen and clarify the rationale for excluding eigenvectors 4 and 5 from subsequent analyses, particularly since they appear above the "knee" of the variance explained plot.

      We thank the reviewer for pointing out that the variance-explained profile and the decision about biological interpretability are distinct considerations. We have clarified that G4 and G5 were excluded from the primary interpretation because their biological meaning and spatial interpretation were not sufficiently clear, not because their variance contribution was negligible. We have added this distinction to the Results.

      Revised manuscript text (Page 9): “We did not include G4 and G5 in the current interpretation because their biological significance was not sufficiently clear; this decision reflected interpretability rather than negligible explained variance.”

      (Interpretation)

      (1) Eigenvector Interpretation and Topography:

      Delineating how continuous gradients relate to or interact with discrete histological subfields would provide a more biologically grounded interpretation than relying strictly on geometry. Naming the eigenvectors based on weak geometric associations (especially in the case of G3) risks obfuscating the complex variation within the data. For full transparency, all linear and quadratic associations with all anatomical axes should be systematically reported, and a more descriptive or neutral nomenclature should be considered.

      We thank the reviewer for this important comment. We agree that the biological interpretation of continuous hippocampal gradients should not be framed as geometry in isolation. We have therefore clarified that the posterior–anterior and proximal–distal coordinates are complementary anatomical descriptions of hippocampal biological organization, rather than biologically empty geometric axes.

      In particular, the posterior–anterior axis captures the hippocampal long-axis organization, whereas the proximal–distal axis follows the iso-to-allocortical topology from subiculum through the Cornu Ammonis fields to dentate gyrus. This latter direction is topologically aligned with the discrete hippocampal subfields, which are themselves defined by differences in cytoarchitecture. Thus, the geometric coordinate system and the cytoarchitectonic organization provide two complementary descriptions of the same underlying hippocampal topology, rather than mutually exclusive interpretations. We revised the text to make this relationship explicit and to avoid implying that the observed gradients provide a direct histological measurement.

      We also clarify that the reported gradient–axis relationships were not selected post hoc from a single geometric comparison. We systematically evaluated linear and quadratic associations between each of the three functional gradients and both intrinsic anatomical axes, and additionally assessed higher-order relationships where warranted. Figure 2b–d shows the strongest statistically supported relationship for each gradient: a linear posterior–anterior association for G1, a quadratic posterior–anterior association for G2, and a cubic proximal–distal association for G3. The remaining axis associations are reported in Extended Data Fig. 2. Accordingly, the descriptive names are based on comparative assessment of the full set of candidate geometric models, while G1–G3 remain the primary neutral identifiers throughout the manuscript.

      Revised manuscript text (Page 9): “This gradient follows the medial–lateral, iso-allocortical organization of the hippocampus and is topologically aligned with cytoarchitectonically differentiated subiculum, CA fields and dentate gyrus.”

      (2) Balanced Nomenclature:

      Elevating the cortical component to a higher-order conceptual term ("hierarchy") while leaving the hippocampal counterpart strictly geometric ("gradients"), given that both metrics are derived using equivalent non-linear dimensionality reduction.

      We thank the reviewer for highlighting this asymmetry in terminology. We agree that applying the term “hierarchy” to the cortical component without defining its evidential basis could be confusing, particularly because both cortical and hippocampal maps are obtained using nonlinear dimensionality-reduction methods.

      The term cortical functional hierarchy does not arise simply from estimating a cortical gradient. It originates from longstanding models of cortical organization in which sensory systems occupy relatively lower-order positions and progressively integrated association systems occupy higher-order positions. This framework has subsequently been formalized at the macroscale as the reproducible unimodal-to-transmodal axis of functional connectivity and has been supported by convergent evidence from cortical microstructure, structure-function coupling, connectivity architecture, and transcriptomic specialization[6-9]. We have clarified this historical and evidential basis in the revised manuscript.

      In the present study, the cortical functional-hierarchy map is therefore used as an independently established reference map of continuous cortical organization, rather than as a new hierarchy inferred from our hippocampal data. We use this term operationally and non-causally: it indexes each cortical region’s position along the established unimodal-to-transmodal functional-connectivity axis.

      Crucially, this terminology does not assign greater biological importance to the cortical measure. Hippocampal functional gradients are the primary object of the present study, and determining their structural and functional significance is a central aim. We therefore examine their associations with hippocampal anatomical coordinates and geometric modes, myelin-sensitive MRI, transcriptomic variation, cortical functional organization, and cognition. We retain the neutral labels lLG, qLG, cIG and “hippocampal functional gradients” because they describe empirically derived axes without presupposing a biological interpretation. As convergent anatomical, microstructural, functional, and comparative evidence accumulates, a more specific organizational terminology for particular hippocampal gradients may become justified. Thus, the present distinction between “cortical functional hierarchy” and “hippocampal functional gradients” reflects the evidential role of each measure in this study, rather than a difference in scientific importance or in the legitimacy of their structure-function interpretation.

      Revised manuscript text (Page 14): “Here, FH denotes the established unimodal-to-transmodal ordering of macroscale cortical functional organization, rooted in longstanding models of hierarchical cortical processing and subsequently formalized using functional-connectivity gradients.”

      (3) Refinement of Textual Tone and Claims:

      • Remove causal verbs (e.g., "sculpts", "constrains") when describing correlations between functional gradients, structural metrics, and cognitive scores, replacing them with appropriate relational or correlational language.

      We thank the Reviewer for reinforcing the need for this terminology correction. We agree that the request to remove causal verbs describes the same manuscript-wide claim-calibration issue addressed in our response to Reviewer #1, Recommendation 1. We have therefore applied the consolidated terminology revision across the overlapping sections, including the descriptions of functional gradients, structural measures, MRI intensity, and cognitive scores.

      • Temper the interpretation of the ~5% variance explained in the maturation analyses, ensuring that this modest effect size is not framed as a massive macroscale reorganization or "decoupling."

      We thank the reviewer for noting that the age-related variance explained by some global gradient features is modest. We agree that the reported ∆Adjusted R<sup>2</sup> values quantify age-related variation in a specific descriptive summary—for example, the explained variance or standard deviation of a gradient, or a summary measure of geometry–function coupling—after accounting for the covariates in the model. They should therefore not be interpreted as the proportion of the entire hippocampal functional-connectivity organization that changes with age, nor as a standalone measure of the magnitude of hippocampal reorganization.

      Our interpretation of developmental reorganization does not rely on these global summary statistics alone. The spatially resolved hippocampal–cortical connectivity organization shows complex variation across the hippocampal surface (Extended Data Fig. 3). In addition, the age-related analyses of hippocampal gradient projections identify distributed and system-specific developmental changes across the cortex (Figure3e–g; Extended Data Fig. 5f). Together, these complementary analyses support the interpretation that hippocampal–cortical functional organization undergoes a distributed developmental reorganization. We thus retained the description of a distributed developmental reorganization of hippocampal–cortical functional organization, while clarifying that this conclusion is supported by the spatially resolved analyses rather than by the magnitude of any individual global-summary effect size.

      Revised manuscript text (Page 15): “This distributed developmental reorganization of hippocampal–cortical functional organization, which correlates with increasingly complex hierarchical cortical processing, may link to the maturation of episodic memory and executive function (EF)—a set of top-down mental processes potentially associated with cortical hierarchical organization.”

      Correction of Inaccuracies

      (1) Historical Context:

      Revise the introduction to accurately reflect that distributed network connectivity has long been recognized as central to hippocampal function and memory, rather than framing it as a highly novel realization.

      We appreciate the opportunity to clarify the historical framing. The manuscript did not intend to present distributed hippocampal-cortical connectivity as a newly discovered concept; its intended contribution is a developmental, topographic analysis of hippocampal functional gradients. We revised the surrounding wording to make this distinction explicit while retaining the established literature on distributed hippocampal connectivity.

      Revised manuscript text (Page 4): “Distributed hippocampal-cortical connectivity has long been central to models of memory and cognition[10-15].”

      (2) Citation Accuracy:

      Address several inaccuracies where cited literature does not support the accompanying claims. I would like to highlight that this is one of the most concerning aspects of the paper, as it suggests that (at best) the primary authors made several mistakes in their citations that went unnoticed by co-authors, or (worse) it could appear as if the authors have not read the papers they cited, despite them being key to the field.

      We thank the reviewer for emphasizing the importance of citation accuracy and take this concern seriously. We re-checked the source papers and the placement of the citations underlying the three statements raised below. We identified one genuine citation-placement error introduced during iterative revision: Shohamy and Turk-Browne (2013) was inadvertently retained with a developmental statement after being moved from the preceding statement on the hippocampus’s broad cognitive involvement. We have corrected this placement.

      The other two cases were not instances of uncited or unread literature, but the cited papers did not support the precise wording used in the manuscript. Strange et al. was relevant to longitudinal-axis functional organization but not to the proximal–distal cytoarchitectonic context, and Vos de Wael et al. identified medial–lateral variation within separately analyzed subfields but did not establish a whole-hippocampus myelin gradient. We have therefore removed or replaced these citations, revised the associated claims, and now use Genon et al. (2021)[16] for the appropriate anatomical and microstructural-organizational context. These revisions distinguish direct evidence, anatomical interpretation, and indirect MRI-based microstructural measures more clearly.

      a) "It was traditionally assumed that the hippocampus undergoes its most significant development in infancy and early childhood and achieves full maturity by the end of this period13" - Shohamy et al. do not discuss hippocampal development.

      We thank the reviewer for identifying this citation mismatch. We agree that Shohamy and Turk-Browne (2013) does not support a claim about hippocampal developmental timing. During iterative manuscript revision, this reference was inadvertently retained with the developmental statement after being moved from the preceding sentence concerning the hippocampus’s broad involvement in cognition. We have restored it to that preceding sentence.

      The revised historical statement is now supported by and Ghetti and Bunge (2012)[17] and Bauer (2007)[18], which describe earlier accounts emphasizing hippocampal development in infancy and early childhood. We further clarify immediately thereafter that more recent evidence supports continuing, regionally differentiated hippocampal development beyond early childhood.

      Revised manuscript text (insert on Page 4): “Earlier accounts proposed that hippocampal development was most consequential in infancy and early childhood[17-18].”

      b) "This gradient exhibits similarities to the previously established cytoarchitectonic variations within the hippocampus4,27. We hence termed it the cubic iso-allocortical gradient (𝑐𝐼𝐺)." - Strange et al., does not mention cytoarchitecture, and Genon et al., is only a secondary source on the matter.

      We thank the reviewer for this important citation correction. We agree that Strange et al. primarily concerns functional specialization along the hippocampal longitudinal axis and does not provide appropriate support for a claim regarding the proximal–distal or medial–lateral cytoarchitectonic organization. We have therefore removed this citation from the relevant sentence.

      We retained Genon et al.[16] because this review systematically synthesizes the major dimensions of human hippocampal organization and identifies the medial–lateral dimension as a key organizational axis associated with cytoarchitectonic differentiation. In our data, cIG showed a significant cubic association with the proximal–distal coordinate (Figure 2b). This coordinate is topologically aligned with the medial–lateral, iso-allocortical organization spanning subiculum, CA fields and dentate gyrus. We have clarified that Genon et al. is cited to provide this anatomical-organizational context, rather than as direct histological validation that the fMRI-derived cIG measures cytoarchitecture.

      Revised manuscript text (insert on Page 9): “This gradient follows the medial–lateral, iso-allocortical organization of the hippocampus and is topologically aligned with cytoarchitectonically differentiated subiculum, CA fields and dentate gyrus[16].”

      c) "Moving to the mesoscopic scale, myelin content has been found to exhibit a significant medial-lateral gradient along the hippocampus26." - this is not evidenced by the referenced paper (Vos de Wael et al.), and it is not true (see Abrahim et al., 2010).

      We thank the reviewer for raising this important distinction. We agree that Vos de Wael et al. does not support a claim of a continuous medial–lateral gradient in hippocampal myelin content. Although that study identified medial–lateral variation in functional-connectivity organization when hippocampal subfields were examined separately, it was not designed to establish a whole-hippocampus myelin gradient. We have therefore removed Vos de Wael et al. as support for this statement and revised the text to remove the unsupported myelin interpretation.

      We now cite Genon et al. (2021), which synthesizes evidence that local hippocampal microstructural variation, including T1w/T2w-intensities-based estimates that are sensitive to myelin, is organized predominantly along the medial–lateral and ventrodorsal axes. The review further notes partial spatial overlap between medial–lateral functional gradients, myelin-sensitive MRI estimates, and subfield differentiation.

      We respectfully note that Ábrahám et al. (2010) does not contradict this spatial interpretation. Its histological study examined the developmental timing and layer-specific distribution of myelination across ages; it did not test a surface-wide medial–lateral spatial pattern across the hippocampal formation. It is therefore not evidence for a continuous medial–lateral myelin gradient, but neither does it provide evidence against such an organizational pattern.

      Revised manuscript text (insert on Page 5): “local microstructural variation in the hippocampal formation, including myelin-sensitive T1w/T2w intensities, is organized predominantly along the medial–lateral and ventrodorsal axes along the hippocampus and partially overlaps with subfield differentiation[16].”

      (3) Other:

      a) Clearly define or rephrase ambiguous phrasing, such as "Myelination during nurturing process."

      We thank the reviewer for identifying this ambiguous wording. We agree that “nurturing process” was imprecise in this general background statement. We have therefore revised the Introduction to state: “Myelination during brain development has been identified as a key factor in neural plasticity and circuit refinement, affecting neural activity synchronization[19-23].”

      b) Re-evaluate the evolutionary claim in the discussion. It's unclear why the authors assert that the longitudinal axis is uniquely more conserved. The iso-to-allocortical axis is highly conserved, observed even in reptiles.

      We thank the reviewer for this important clarification. We agree that the original Discussion conflated the evolutionary conservation of hippocampal anatomical axes with the interpretation of the functional gradients. We have therefore removed the statements that the linear long-axis gradient is more evolutionarily conserved and may consequently depend more on shared gene-expression patterns, as well as the statement that cIG reflects the portion of the hippocampal–cortical connectome influenced by cytoarchitectonic differentiation.

      We retained the broader comparative interpretation, but revised it to make its evidential status explicit. G2 showed the strongest association with cortical functional hierarchy. Given the greater prominence of hierarchical cortical processing in humans and macaques than in marmosets or rodents, this association raises the possibility that G2 is less evolutionarily conserved than G1 and G3. However, this is a hypothesis motivated by the observed cortical association, rather than a conclusion directly tested by the present human developmental data. We now state this limitation explicitly and identify direct cross-species comparisons as necessary to evaluate it.

      Revised manuscript text (insert on Page 25): “Given the greater dominance of hierarchical processing in humans[24] and macaques[25] in contrast to other species such as marmosets[26] or rodents[27], the strong association of quadratic long-axis gradient with cortical functional hierarchy raises the possibility that it is less evolutionarily conserved than linear long-axis gradient and cubic iso-allocortical gradient. Future cross-species comparisons could test this hypothesis.”

      c) Frame the T1w/T2w intensity variations cautiously as an indirect proxy reflecting multiple tissue properties, incorporating recent literature (e.g., Sandrone et al., 2023) to explicitly acknowledge the confounding effects (e.g., transmit field bias).

      We thank the reviewer for emphasizing the need for a cautious interpretation of T1w/T2w intensity. We agree that it should not be treated as synonymous with myelin or as a direct measure of myelin content. Following its established use as a myelin-sensitive cortical MRI contrast (Glasser and Van Essen, 2011), we now consistently describe T1w/T2w as myelin-sensitive measures. Its variation may reflect myelin-related tissue properties, as well as other tissue and acquisition factors, including transmit-field bias.

      We have incorporated Sandrone et al. (2023)[4] as an important qualification. We respectfully note that this study evaluated corpus-callosum white matter and did not examine cortical gray matter or hippocampal tissue. It therefore supports caution in interpreting T1w/T2w, but cannot itself establish or invalidate the hippocampal gray-matter association reported here. Accordingly, we interpret our result only as an association between hippocampal functional gradients and an indirect MRI contrast, not as evidence of myelin, cellular myelination, or a myelin-mediated developmental mechanism. We revised the relevant Introduction, Results, Figure 5 legend, Discussion, and Limitations accordingly.

      Revised manuscript text (insert on Page 30): “T1w/T2w intensity was treated as an indirect, myelin-sensitive MRI proxy influenced by multiple tissue and acquisition factors, not as direct histological myelin content.”

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      (22) de Faria, O. et al. Periods of synchronized myelin changes shape brain function and plasticity. Nature Neuroscience 24, 1508-1521, doi:10.1038/s41593-021-00917-2 (2021).

      (23) Fields, R. D. A new mechanism of nervous system plasticity: activity-dependent myelination. Nature Reviews Neuroscience 16, 756-767, doi:10.1038/nrn4023 (2015).

      (24) Dong, H.-M., Margulies, D. S., Zuo, X.-N. & Holmes, A. J. Shifting gradients of macroscale cortical organization mark the transition from childhood to adolescence. Proceedings of the National Academy of Sciences 118, e2024448118, doi:doi:10.1073/pnas.2024448118 (2021).

      (25) Xu, T. et al. Cross-species functional alignment reveals evolutionary hierarchy within the connectome. NeuroImage 223, 117346, doi:https://doi.org/10.1016/j.neuroimage.2020.117346 (2020).

      (26) Tong, C. et al. Multimodal analysis demonstrating the shaping of functional gradients in the marmoset brain. Nature Communications 13, 6584, doi:10.1038/s41467-022-34371-w (2022).

      (27) Huntenburg, J. M., Yeow, L. Y., Mandino, F. & Grandjean, J. Gradients of functional connectivity in the mouse cortex reflect neocortical evolution. NeuroImage 225, 117528, doi:https://doi.org/10.1016/j.neuroimage.2020.117528 (2021).

    1. Author response:

      We thank the Editors and reviewers for their close reading of our work and valuable comments. We appreciate their recognition of the foundational nature of our study. The reviews suggest multiple improvements that we plan to implement in a revised version, including the following: validation of appearance labels; short self-contained example code for analysing the dataset; greater comparison with prior work in the discussion; more details in the methods. The reviews also make many suggestions for improving the presentation, wording, and clarity of the work. In particular, we acknowledge that we used incorrect terminology in referring to the axes rather than the semi-axes of fitted ellipsoids. The revision will correct this error and provide the full parameters of the ellipsoid fits (r0, r1, r2) in the supplementary data, allowing the consistency of these fits with mitochondrial volume to be appreciated. We did identify that the values of one of the mitochondrial variables not used for the analysis in the paper (r2) had been corrupted in the uploading of the publicly available hemibrain:v1.2.1 dataset to neuprint. Accordingly, we have generated hemibrain:v1.2.3 which restores the original, correct and uncorrupted values of this variable.

    1. Author response:

      We thank the reviewers and the Reviewing Editor for their careful and constructive assessments. We find the reviews fair and helpful, and we plan to revise the manuscript along the lines they suggest. In brief:

      Scope of the conclusions (Reviewer #1):

      We can see how a reader may get the impression that some of our conclusions go beyond what the experiments directly establish. In the revision we will:

      - Describe the genetic tools as targeting neuronal populations (DAN clusters) rather than identified single neurons, and adjust statements about neuronal identity accordingly.

      - Rephrase the description of the time-course results, to emphasize that the shift from aversive to appetitive only appears across experiments and that some single experiments may only show a shift to neutrality. This should help moderate claims about positive valence.

      - State explicitly that our non-contingent comparison used continuous pre-exposure rather than a yoked control. It therefore shows that simple non-contingent exposure is insufficient but does not isolate agency as the causal variable.

      - Better motivate the design changes between the original screen and follow-up joystick experiments.

      - Frame the “common currency” hypothesis more cautiously throughout.

      Clarity and accessibility (Reviewer #2):

      We appreciate that the manuscript is hard to follow for readers outside the field. We will revise the final sentence of the Abstract and clarify what we mean by a dopaminergic “reporter for a specific goal”. We will also spell out how the contrast between a tethered fly and a free-flying fly in a maze bears on this, and what we mean by “control” versus “lack of control” of the environment. In the Introduction and Discussion we will make clearer which cited studies propose or favor the “common currency” view, including Jovanoski and Waddell (2025), and which ones merely bear on it.

      Conceptual framework (Reviewer #3):

      We will make our assumptions linking the role of DANs in classical conditioning to their expected effects in operant paradigms more explicit. The reference to the Heisenberg and Wolf (1991) scheme as a suitable level of explanation was particularly helpful and we will thrive to develop our hypotheses at the same level. At least for the designers of the original screen (BB and CR), the lack of consistent effects was clearly unexpected, or we would have designed the experiments differently. We will justify these expectations and from this why we consider this negative result to be so informative.

      Code availability (Reviewing Editor): We will deposit the code in a repository with a permanent DOI, such as Zenodo, in addition to GitHub.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Olmstead et al. present a single-cell nuclear sequencing dataset that interrogates how hippocampal gene expression changes in response to distinct physiological stimuli and across circadian time. The authors perform single-nucleus RNA sequencing on mouse hippocampal tissue after (1) kainic acid-induced seizure, (2) exposure to an enriched environment, and (3) at multiple circadian phases.

      The dataset is rigorously collected, and a major strength is the use of the previously established ABC taxonomy from Yao et al. (2023) to define cell types. The authors further show that this taxonomy is largely independent of activity-driven transcriptional programs. Using these annotations, they examine activity-regulated gene expression across neuronal and glial subclasses. They identify ZT12, corresponding to the transition from the light to the dark period, as transcriptionally distinct from other circadian time points, and show that this pattern is conserved across many cell types. Finally, they test how circadian phase influences activity-dependent gene expression by exposing mice to an enriched environment at different times of day, and report no significant interaction between circadian phase and enriched environment exposure.

      A crucial consideration for users of this dataset is the potential confounding effect between circadian phase and locomotor activity. This is particularly relevant because dentate gyrus activity is strongly modulated by locomotion. The authors acknowledge this issue in the Discussion and provide useful guidance for how to interpret their findings, considering this confound.

      We thank the reviewer for their accurate and thoughtful summary of the ACT-DEPP dataset and the key experimental design and analytical choices that form the basis of the study. We agree that circadian phase and locomotor activity are major confounders that are irreconcilable in the current study. We have modified our Discussion of this point to consider future studies which would be able to delineate the two (lines 403-406)

      Taken together, this dataset represents a useful resource for the neuroscience community, particularly for investigators interested in how novel experience and circadian phase shape activity-related and immediate early gene expression in the hippocampus

      Reviewer #2 (Public review):

      This manuscript presents the ACT-DEPP dataset, a comprehensive single-nucleus RNA-sequencing atlas of the mouse hippocampus that examines how activity-dependent and circadian transcriptional programs intersect. The dataset spans multiple experimental conditions and circadian time points, clarifying how cell-type identity relates to transcriptional state. In particular, the authors compare stimulus-evoked activity programs (environmental enrichment and kainite-induced seizures) with circadian phase-dependent transcriptional oscillations. They also identify a transcriptional inflection point near ZT12 and argue that immediate early gene (IEG) induction is broadly maintained across circadian phases, with minimal ZT-dependent modulation.

      Strengths:

      The study is ambitious in scope and data volume, and outlines the data-processing and atlasregistration workflows. The side-by-side treatment of stimulus paradigms and ZT sampling provides a coherent framework for parsing state (activity) from phase (circadian) across diverse neuronal and non-neuronal classes. Several findings - especially the ZT12 "inflection" and the differential sensitivity of pathways across subclasses - are intriguing.

      Weaknesses:

      (1) The authors acknowledge, but do not adequately address, the fundamental confounding factor between circadian phase and spontaneous locomotor activity. The assertion that these represent "orthogonal regulatory axes," based on largely non-overlapping DEGs, may be overstated. The absence of behavioral monitoring during baseline is a major limitation.

      We agree that circadian phase and locomotor activity are irreconcilable confounders in the current study. We have removed the phrase “orthogonal regulatory logic.” This point is disclaimed as the leading point in our Limitations section. We expand on this section to consider future studies which would be able to delineate the two (lines 403-406).

      (2) The statement "Thus, novel experiences and seizures trigger categorically distinct transcriptional responses-with respect to both magnitude and specific genes-in these hippocampal sub regions" is overstated, given the data presented. Figure 2A-B shows that approximately one-third of EE-induced DEGs at 30 minutes overlap with KA DEGs, and this overlap increases substantially at 6 hours in CA1 (where EE and KA responses become "fully shared"). This suggests the responses are quantitatively different rather than "categorically distinct."

      We have modified the sentence (lines 127-129) to state: “Thus, novel experience and seizure induce transcriptional programs that differ greatly in magnitude and, apart from CA1 after 6 hours, contain stimulus-specific genes.” We have additionally modified the section title to de-emphasize stimulus-specificity.

      (3) In Figure 4B, "active cells" are defined as those with >=3 of 15 IEGs above the 90th percentile, with thresholds apparently calibrated in CA1. Because baseline expression distributions differ across subclasses, this rule can bias activation rates across cell types.

      The baseline expression thresholds were computed for each CA1 Supertype, e.g. CA1 69-1, 702, etc. (Figure 4D).

      (4) Few genes show significant ZT × stimulus (EE or seizure) interactions, concentrated in neuronal populations. Given unequal nucleus counts and biological replicates across subclasses, small effects may be underpowered.

      We agree with the observation that our measurements may be underpowered to observe small effects. The nuances of our DGE methodology are discussed below under Reviewer 2’s Recommendation #3.

      (5) In Figure 6 I, J, the relationship between the highlighted pathways/functions and circadian phase is not yet explicit.

      We agree that there is no obvious relationship for ZT-based changes in expression among genes in shared sets highlighted in Figures 6I-J. However, their enrichment among the small set of 13 significantly interacting genes genome-wide merits remark as we have done so here. What functional implications these observations have is the subject of future experiments.

      (6) Line 276-280: The enrichment of lncRNAs at ZT12 in CA1 is intriguing but underdeveloped. What are these lncRNAs, and what might they regulate?

      Gene symbols were ascertained by mapping reads to the GRCm39-113 mouse genome in Parse Bioscience’s Trailmaker pipeline (Methods). GRCm39 returns gene biotype annotations, which is how we determined these genes were lncRNAs. A literature search for these gene symbols found that all 12 are predicted or uncharacterized loci without functional experimental data.

      Overall, most descriptive conclusions are supported (e.g., broad phase-robustness of classical IEGs; an inflection near ZT12). Claims about the separability/orthogonality of activity vs circadian programs, and about categorical distinctions between EE and KA responses, would benefit from more conservative wording or additional analyses to rule out behavioral and power-related alternatives.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      I have a few suggestions for additional analyses and clarifications that could further strengthen the study:

      (1) KA responsive populations and spatial context

      In Figure 2, the authors show that KA-responsive cells cluster within two supertypes, which may 99 represent seizure-specific populations. Could the authors leverage the spatial transcriptomic data 100 from Yao et al. to ask whether there is a specific cell type or subregion within the dentate gyrus 101 that is predisposed to express the seizure-associated gene programs identified in Figure 2?

      We thank the reviewers for this interesting analysis suggestion. We have added Figure 2—figure supplement 6 as an exploration of the spatial distribution of DG Supertype 138-3. We find that these cells are predominantly located in dorsal hippocampus, although are sparsely distributed throughout all of hippocampus.

      (2) Baseline circadian modulation of canonical IEGs

      In the Discussion, the authors note that canonical immediate early genes do not overlap with circadian differentially expressed genes, citing results from Figure 5. However, the current 109 analyses do not directly show how canonical IEG expression varies across the circadian cycle at 110 baseline. It would be helpful to include a focused visualization, for example, a heatmap or line plot 111 of IEG expression across circadian time points, to more directly support this conclusion.

      We have added Figure 6—figure supplements 1-2. These plots demonstrate low variation of IEG expression within the standard environment across ZTs. EE-induction is likewise similar across ZTs in CA1. DG demonstrates less consistent induction relationships, likely due to dramatically low abundances leading to noisy expression estimates.

      (3) Neurogenesis-related signatures

      Given that dentate gyrus cells are included in the dataset, it may be informative to comment on neurogenesis-related transcriptional programs. For example, can the authors report whether markers of adult-born granule cells or progenitor populations are detected, and whether genes associated with neurogenesis are modulated by experience (seizure or enriched environment) or circadian phase? Even a brief analysis or summary would likely be of interest to the community.

      We do capture a small population of immature neuronal cells (IMNs) in our dataset that are likely the product of dentate neurogenesis (Figure 1B). Our experiment was not adequately designed to detect the origin of these cells, nor determine whether EE induces changes in rate of neurogenesis or cell fates. However, we can measure the effects of acute EE on the preexisting IMN population present at the time of experimentation. We have added Figure 2—figure supplement 7 to examine this topic. We observe that hours of EE exposure instead of minutes is necessary to induce transcriptional changes. Interestingly, many of the DEGs observed encode neurotransmitter receptor subunits or intercellular adhesion proteins.

      Reviewer #2 (Recommendations for the authors):

      Behavioral confounding factor: Please provide locomotor activity measures aligned to ZT for the relevant cohorts (e.g., wheel counts or video tracking), or at minimum, discuss how ZT-dependent changes in arousal/locomotion could contribute to the observed transcriptional differences and how your analyses mitigate this confounding factor. Including locomotion as a covariate in pseudobulk models or presenting matched restraint controls would be helpful.

      We did not collect locomotion data on the mice and so are unable to include it as a covariate in any analyses. We place the Limitations subsection at the beginning of our Discussion and disclose the confounding effect of locomotion/arousal as a main limitation of this study. 

      It is well established that mice increase locomotor activity in the hour preceding the dark phase (i.e. during ZT 11-12) [1]. Similarly, in vivo neurophysiological studies of hippocampus during locomotion consistently demonstrate that neuronal cells in hippocampus exhibit spatially tuned activity that increases as an animal navigates an environment compared to when it is stationary [2]. If locomotion were to exhibit major influence on gene expression in our experiment, it is reasonable to assume that we would observe such effects in IEGs. Nevertheless, we do not observe changes in baseline IEG expression across ZTs (Figure 6—figure supplement 1-2). Based on this albeit circumstantial evidence, we conclude that circadian influences on gene expression are likely to predominate over locomotor ones in the absence of other manipulations.

      What may explain this lack of IEG induction across dramatically different locomotor phases? It is possible that locomotion-dependent effects on neuronal activity are insufficient to drive activity-dependent changes without instructive learning signals within the hippocampal circuit. One speculative mechanism for this could be that, in the standard environment (i.e. the animal’s home cage), the lack of strong plasticity events such as dendritic plateau potentials [3] fails to overcome the signaling threshold(s) necessary to induce activity-dependent transcriptional programs. It also remains possible that locomotion-induced transcriptional changes involving hundreds of genes such as that observed in Figure 5 are coordinated through processes independent of canonical IEG induction.

      (2) "Active cell" definition: Please provide (i) a sensitivity analysis varying the percentile cutoff (e.g., 80/85/95%) and the number of IEGs required (2-4), and (ii) a complementary analysis using continuous activity scores (e.g., AUCell or ssGSEA) with concordance to the binary call reported (ROC/PR or agreement metrics). Subclass-specific thresholding or normalization would further mitigate bias; reporting the fraction of "active" cells per subclass under each parameter set would be helpful.

      We have added Figure 4— figures supplements 1-2 to incorporate all these requested analyses. Rather than rely on an external library to construct an IEG module score, we employ a simple z-scoring index of the 15 IEGs used in Figure 4B, D, E to overcome the technical challenges unique to this set of low-abundance genes.

      From these requested analyses, we find that ROC curves were extremely accurate at classifying active and inactive cells based on a continuous activity IEG score (AUC > 0.985, Figure 4 — figure supplement 2). Precision-recall curves were also constructed, which demonstrated decreased—although still robust—classification of cell activity state in SE. This is consistent with the performance of precision/recall tradeoff between conditions when there is an imbalance of active/inactive cells in the underlying populations (see Figure 4B). When investigating the decreased PR-accuracy in SE, we observed that discordant classifications were likely to arise when a single IEG was elevated enough to significantly increase the composite score, leading to a spurious classification as “active” with the continuous scoring method when it would not meet the 3-gene threshold in the other method.

      Finally, we note that we already employed supertype-specific thresholding to set baseline thresholds for each CA1 sub-population.

      (3) Interaction effects and power: Please (a) report per-subclass effective sample sizes and replicate numbers, (b) re-analyze with a complementary framework (limma-voom or edgeR) and, where possible, (c) include sample-level mixed-effects models (animal as a random effect; pseudobulk counts or cell-fraction outcomes). Presenting effect sizes with uncertainty (e.g., forest plots) would improve interpretability beyond binary FDR thresholds.

      We have added Figure 2—figure supplements 1-5; and Figure 3—figure supplement 1 to address these requests and included a new paragraph in the Results section (lines 130-146) describing how these different methods perform comparatively on our dataset. We observe that these methods perform similarly under most conditions, but that DESeq2 shrinkage—the method used for all DGE analysis in the main figures—aggressively forces estimated fold-change toward zero in certain conditions with high variance. We maintain our original conclusion that Type I error rate is adequately minimized. However, Type II error rate in our DGE analyses may be higher with DESeq2 under certain conditions compared to other frameworks.

      We modified our Discussion to expand on these findings (lines 415-424) and disclose to the reader that “Our findings should be interpreted as a conservative observation of activity- and circadian-dependent changes in gene expression.” We thank the reviewer for these suggestions which have significantly improved the analytic rigor of the project and revealed its potential technical shortcomings.

      (4) Figure 6 I,J : Please make clear whether these pathways are simply enriched among DE genes or whether they exhibit bona fide circadian modulation.

      The 13 significant genes ascertained through the interaction analysis presented in Figure 6I-J were manually annotated through literature review, given the feasibility from such a small number of DEGs. The pathways described—endocannabinoid synthesis, signaling and excitability, and chromatin remodeling/gene expression—were all cellular processes implicated by literature review of the gene list. From this, we conclude that these processes are influenced by an interaction between circadian- and activity-dependent induction of gene expression after controlling for their individual effects.

      References

      (1) Eckel-Mahan, K. L. et al. Circadian oscillation of hippocampal MAPK activity and cAMP: implications for memory persistence. Nat Neurosci 11, 1074–1082 (2008).

      (2) Buzsáki, G. Theta Oscillations in the Hippocampus. Neuron 33, 325–340 (2002).

      (3) Bittner, K. C., Milstein, A. D., Grienberger, C., Romani, S. & Magee, J. C. Behavioral time scale synaptic plasticity underlies CA1 place fields. Science 357, 1033–1036 (2017).

  3. Oct 2026
    1. Author response:  

      The following is the authors’ response to the previous reviews

      Public Reviews:

      Reviewer #1 (Public review):

      Comments on revised version.

      The authors have revised their manuscript to clarify that molecular analyses have not yet occurred and have resolved the technical/publication issues with the figures. I look forward to seeing these tools used in future publications to answer important questions in Blastocystis research.

      We are grateful to Reviewer 1 for their careful and constructive assessment of our revised manuscript. We are pleased that the revisions have satisfactorily addressed their previous concerns, and we sincerely appreciate their recognition of the value of our work.

      Reviewer #3 (Public review):

      Comments on revised version.

      The revised version provides sufficient clarity and appropriate visual presentation. Some confusion evidently arose due to my misunderstanding, so I thank the authors for their comprehensive clarifications and patience.

      We are grateful to Reviewer 3 for their careful reading of the revised manuscript and for the additional constructive suggestions. We appreciate that these recommendations are aimed at improving clarity, accessibility, and presentation, and we have addressed them as detailed below.

      Recommendations for the authors:

      Reviewer #3 (Recommendations for the authors):

      (1) Table 1

      (1a) The description of the column "Promoter Lengths Tested" is a bit confusing because it actually shows acronyms of the used promoters. Suggestion for clarity: either keep the name and mention just the lengths, or rename to "Promoter abbreviation" or "Promoter acronym".

      We thank the reviewer for pointing this out. To avoid confusion, we have renamed this column “Promoters Tested”, which better captures the information presented. The column contains both promoter identifiers and the corresponding promoter lengths, which are further clarified in the table notes.

      (1b) It is not entirely clear based on the formatting of the table, which columns are relevant for "Blastocystis ST4-WR1" and which for "Blastocystis ST7-B".

      We thank the reviewer for this helpful suggestion. We have revised the formatting of Table 1 to more clearly distinguish the data corresponding to Blastocystis ST7-B and Blastocystis ST4-WR1. Specifically, we have added a vertical divider between the relevant column groups to improve readability and make the species-specific information easier to follow.

      (2) Figure 2:

      If the authors wish to preserve the decorative colouring in the parts B and C, it would be better to at least keep the datapoint and boxplot hues consistent for individual conditions (or plot the datapoints in the same, neutral hue throughout, e.g., black or grey). Currently, this is only the case in the part C, but not in the part B.

      We thank the reviewer for this useful suggestion. We have revised Figure 2B to improve visual consistency between the data points and boxplots while preserving the overall colour scheme of the figure. This adjustment improves readability without changing the data or its interpretation.

      (3) Figure 3: With the modifications everything is clear. However, two issues are now apparent.

      (3a) After the part A was modified, the arrow colours changed (had been yellow and red, now are cyan and magenta), but the description in the legend remained (yellow and red), so the text should be corrected. [By the way, the original colours worked well.]

      We apologise for overlooking this inconsistency. The Figure 3 legend has now been corrected to match the revised arrow colours in panel A.

      (3b) The care taken by the authors to make the images more accessible is really greatly appreciated, but being a person on the colourblind spectrum, I can attest that the issue is not always just about red and green discrimination: the greyscale and blueish green used in the part A photo in particular are discernible only at huge magnification (to some people). If the signal in the part A were of the same hue as in the part B (yellowish green instead of blueish green), it would readily pop out. For that matter, what is the reason for the use of a different colour profile of the UnaG fluorescence in these two images?

      We sincerely thank the reviewer for this important accessibility-related comment. The difference in colour profiles between panels A and B was intentional because the images were acquired using different imaging modalities, as indicated in the figure legend. We wanted to avoid implying that the two panels were generated under identical imaging conditions. However, we appreciate the reviewer’s point that this distinction should not come at the expense of readability. We have therefore adjusted the display of the UnaG signal in panel A to improve contrast and visibility. 

      (4) Conclusion:

      The expression "bringing endogenous regulatory part discovery, namely the identification of native promoter and terminator elements" feels a bit clunky. What the part "endogenous regulatory part discovery" alludes to is now clearer, but consider reformulating it to "discovery of endogenous regulatory elements". This would make it clear without the need to add the explanation "namely the identification of native promoter and terminator elements". [It is now clear that the accumulation of noun adjectives and the significance of the word "part" was what originally blurred the overall meaning.

      We thank the reviewer for this valuable suggestion. We agree that the original phrasing was unnecessarily clunky and have revised the sentence for clarity and flow. Lines 682–684 now read:

      “By integrating endogenous promoter and terminator discovery, DNA delivery, selection, clonal recovery, and reporter validation into a single pipeline, we provide a flexible foundation for routine transgene-based studies.”

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      This is an interesting study that addresses whether mitochondrial DNA (mitoDNA) variants impact telomere length (TL), which may be relevant to potential maternal inheritance of TL in offspring. The study addresses this question using a cybrid model approach in which mitochondria from donor platelets from 7 individuals that vary in TL and differ in mitoDNA variants are introduced into 143B cells that lack mitochondria. MitoDNA variants that exhibited reduced complex I activity showed telomere shortening in cybrids and increased telomere dysfunction. Interestingly, these phenotypes could be reduced with NAC antioxidant and NAD+ supplementation, suggesting that ROS and oxidative DNA damage at telomeres contributed to the telomere shortening. They further showed that cybrids with lower levels of ROS correlated with longer TL in the lymphocytes of the mitochondrial donors.

      Strengths:

      This study provides compelling evidence that mtDNA variants influence TL through a mechanism involving mitochondrial-derived ROS, potentially causing telomeric oxidative damage. The data are robust, and the manuscript is well written. However, the study could be strengthened by addressing the following questions and minor weaknesses below.

      We thank the reviewer for this very positive evaluation of our work.

      Weaknesses:

      (1) Introduction. Line 81, the relationship between TL and the risk of lymphoid and myeloid leukemia is not straightforward. POT1 variants associated with long TL increase the risk for lymphoid and myeloproliferative neoplasms (see PMID: 41564438 for example).

      We appreciate the reviewer raising the important link between pathogenic POT1 variants and lymphoid malignancies driven by elongated telomeres. We would like to clarify, however, that our introduction focused not on the pathological telomere attrition characteristic of telomere biology disorders, but rather on the natural, non-pathological variations observed in individuals with baseline telomere lengths on the shorter end of the spectrum.

      Nevertheless, the two following publications by the Armanios lab have been added in the introduction to underscore the complex relationship between telomere length and tumorigenesis:

      DeBoy EA et al. Familial clonal hematopoiesis in a long telomere syndrome. 2023. N Engl J Med 388, 2422-2433.

      Davidson-Swinton HR et al. Lymphoid malignancy and clonality in the POT1-mediated long telomere syndrome. 2026. Blood 147, 2226-2237.

      Here is the corresponding sentence in the revised manuscript:

      “However, some pathogenic mutations in POT1 gene, linked to very long telomeres, were also previously associated with increased risk for lymphoid and myeloproliferative neoplasms (5,6), underscoring the complex relationship between TL and cancer predisposition.”

      (2) Figure 1. Since sex also influences TL, it would be good to know the sex of the selected individuals or explain why this is not necessary.

      Because this study investigated the potential maternal inheritance of TL via the mitochondrial genome, our cohort consisted predominantly of female donors (6/7). Donor #5, the husband of Donor #7, was the only male included. We have added the information in the text:

      “All were of European origin, thus excluding a possible bias linked to African ethnic groups (7), and the seven donors belonged to distinct mitochondrial subhaplogroups (Fig 1D). All but one (#5) were female donors.”

      Notably, our analysis revealed minimal influence of sex on TL, which cannot account for the observed differences between the extreme groups.

      (3) Please include a description of the 143B cells that were used for cybrid formation in the Results section when introducing the cybrids.

      We did it:

      “To evaluate the impact of distinct mitochondrial genomes on TL in human cells, we used a transmitochondrial cybrid strategy in which mtDNA-depleted Rho<sup>0</sup> (ρ<sup>0</sup>) cells, derived from 143B human osteosarcoma cancer cells, are fused with donor platelets, thereby restoring functional mitochondria carrying donor-specific mtDNA variants (21).”

      (4) Lines 155-156. The authors note that cybrids from donors 1 and 2 show "pronounced" telomere damage. This result indicates an increase in 53BP1-positive telomeres, which could be indicative of telomere dysfunction or damage. Quantification of the increased chromosome end fusions for cybrids 1 and 2 would strengthen the result.

      We thank the reviewer for this suggestion. Following their advice, we used our metaphase spread FISH analyses to quantify chromosome end fusions in the parental 143B Rho0, Cyb1 and Cyb6 cells. However, because Cyb2 metaphase spreads were of insufficient quality for adequate chromosome analysis, we restricted our telomere fusion comments exclusively to Cyb1 and included the quantifications in our revised manuscript (Fig 2E).

      Do the increased fusions correlate with an increase in telomere signal-free ends? These should be apparent in the telomere FISH images of metaphase chromosomes.

      While this is a strong argument, the telomeres within these cybrid models are critically short. Consequently, the FISH signal intensity falls below the threshold required for reliable quantification of telomere-free ends.

      (5) Lines 168-169. What is the evidence that the "in vitro metabolic shift" causes acute oxidative stress?

      The reviewer is correct that we have not formally demonstrated this in our experimental system. Instead, our assumption was based on the fact that the initial phase of Rho0 cell repopulation involves a temporary ROS burst, partly driven by incompletely assembled ETC supercomplexes that are known to elevate ROS levels (Maranzana et al., 2013). This is supported by our experimental observation that the NAC antioxidant, combined with NR, potently inhibits telomere shortening in cybrids with low CI activity. We added the following sentence in the revised manuscript:

      “When mitochondria are replenished in ρ<sup>0</sup> cells during the formation of transmitochondrial cybrids, a shift from glycolysis to OXPHOS occurs (Fig S4A-B) and cells need to adapt to this metabolic change. Notably, the initial phase of ρ<sup>0</sup> cell repopulation involves a temporary ROS burst, partly driven by incompletely assembled ETC supercomplexes that are known to elevate ROS levels (22).”

      (6) Why did the elevated ROS in cybrid #3 (Figure 4C) not translate to shorter telomeres in the cybrid (Figure 2A)? Perhaps there is a difference between factors that determine TL in the cybrid vs the donor's lymphocytes?

      We cannot fully explain the discrepancy, but we indeed suspect in vivo oxidative stress differs significantly from cell cultures (21% O<sub>2</sub>). Additionally, early cybrid replenishment involves an unknown telomere elongation step that may offset mitochondrial ROS-induced shortening.

      To further investigate this question, we measured telomere length across varying population doublings (PDs) and observed the following shortening after 66-67 PDs:

      - Cyb3: about 1.6 kb reduction

      - Cyb6: about 1.2 kb reduction

      - Cyb7: about 0.8 kb reduction

      These results suggest that the rate of telomere shortening in culture may be higher in Cyb3 cells, possibly due to increased ROS levels.

      We included these results as Supplementary Figure 7 and have discussed these data in the revised manuscript:

      “Consistently, tracking TL over sequential population doublings revealed that Cyb3 cells are more vulnerable to progressive telomere shortening than Cyb6 or Cyb7 cells (Fig S7). Together, these findings support a role for mitochondrial ROS in human TL regulation.”

      In Figure 4B, it appears that the statistical comparisons for mitochondrial superoxide are all relative to Cyb3. If so, why are the comparisons not with the parental 143B rho0 cell line? Please clarify.

      We excluded Rho0 cells from our superoxide measurements because these cells were grown in a different culture medium. Instead, we focused on comparing mitochondrial ROS across cybrids to accurately correlate these values with the telomere length of the corresponding donors’ lymphocytes. Consequently, Rho0 cell measurements would not have contributed to this correlation analysis.

      We have discussed this in the revised manuscript:

      “Mitochondrial superoxide production was measured by electron paramagnetic resonance (27) in clones #1 of all cybrids and in 143B cells (Fig 4B). We excluded 143B ρ<sup>0</sup> cells from our superoxide measurements because these cells were grown in a different culture medium.”

      (7) Given the heterogeneity in TL and mtDNA variants in the human population, the conclusions could be further strengthened by increasing the number of donors and cybrids analyzed. However, there are admittedly practical factors. Overall, these findings are compelling and provide a solid foundation for expanding this analysis in the future. This is more of a comment than a weakness.

      We thank the reviewer for this constructive feedback and entirely agree that including more donors would have added depth to our findings. While we acknowledge this limitation, pursuing this further is currently impossible without acquiring new ethical approvals and establishing fresh collaborations with clinicians.

      Reviewer #2 (Public review):

      Summary:

      The authors aim to determine whether mitochondrial genotype influences telomere length. By generating cybrids harboring different mitochondrial backgrounds, the authors seek to establish a mechanistic link between mitochondrial status and telomere biology.

      Strengths:

      A major strength of the study is the use of cybrid technology, which provides a great approach to investigate the role of mitochondrial DNA independently of the nuclear genome. The authors also employ multiple complementary assays to assess telomere-related phenotypes associated with mitochondrial dysfunction. Together, these experiments generate an interesting dataset that will be of value to researchers interested in the intersection between mitochondrial biology, genome stability, aging, and development. These results also build on previous work supporting roles for ROS/mitochondria in driving telomere shortening.

      We thank the reviewer for this very positive evaluation of our work.

      Weaknesses:

      The data support the conclusion that mitochondrial background is associated with differences in telomere length and telomere-related phenotypes. However, some of the mechanistic interpretations would benefit from additional evidence. In particular, the manuscript discusses mitochondrial influences on telomere shortening, yet telomere length in some experiments is assessed at a single time point. Consequently, the current data do not directly address the rate of telomere attrition. Differences observed between cybrid lines could potentially arise from events occurring during cybrid formation, clonal selection, or subsequent cell expansion. Longitudinal analyses across multiple passages, ideally beginning immediately after cybrid generation and controlling for population doublings, would help establish whether mitochondrial function directly affects telomere shortening dynamics. Some experimental results would also benefit from additional quantification, clarification, and some biological replicates are missing.

      We limited our TL measurements to the earliest viable time point after cybrid formation to avoid the confounding effects of cellular adaptation in culture. For instance, the early telomere shortening observed in Cyb1 and Cyb2 cells was later alleviated—likely due to the upregulation of the NAD+ salvage pathway genes NAMPT and NAPRT1. To accurately capture the effects specific to cybrid formation, we isolated 4 independent clones per donor, all of which showed highly consistent TL values, as shown in Figure 2A and S3D.

      While we acknowledge the reviewer's point about multi-passage longitudinal analyses, we did, in fact, measure telomere length across varying population doublings (PDs) in Cyb3 (high mito ROS levels), Cyb6 and Cyb7 (moderate to low mito ROS levels) and observed the following shortening after 66-67 PDs:

      - Cybrid 3: about 1.6 kb reduction

      - Cybrid 6: about 1.2 kb reduction

      - Cybrid 7: about 0.8 kb reduction

      These results suggest that the rate of telomere shortening in culture may be higher in Cyb3 cells, possibly due to increased ROS levels.

      We included these results as Supplementary Figure 7 and have discussed these data in the revised manuscript:

      “Consistently, tracking TL over sequential population doublings revealed that Cyb3 cells are more vulnerable to progressive telomere shortening than Cyb6 or Cyb7 cells (Fig S7). Together, these findings support a role for mitochondrial ROS in human TL regulation.”

      We have also carefully edited the manuscript so as to clarify the text and, whenever possible, have added quantifications. Among others, as suggested by Reviewer #1, we added the quantification of chromosome end fusions in the parental 143B Rho0, Cyb1 and Cyb6 cells in our revised manuscript:

      Author response image 1.

      Overall, this study provides interesting evidence linking mitochondrial background to telomere biology. The cybrid models represent a useful resource for the field, and the work raises important questions regarding mitochondria-telomere communication.

      Reviewer #3 (Public review):

      Strengths:

      Mahieu and colleagues address an interesting and underexplored question: whether non-pathogenic variation in the mitochondrial genome contributes to the inter-individual variability of human telomere length (TL). Using a Belgian Flow-FISH reference cohort (n=491) to identify donors at TL extremes, they generate trans mitochondrial cybrids from platelets of seven donors of distinct mtDNA subhaplogroups and characterize the resulting cells with a broad and well-executed toolkit (TRF, TeSLA, ddTRAP, EPR-based mitoROS, Seahorse with permeabilized-cell ETC dissection, LC-MS metabolomics, telomeric PARFISH). The most compelling finding is that cybrids derived from donors with low complex I (CI) activity undergo rapid telomere shortening during the glycolysis-to-OXPHOS transition of cybrid formation, and that this is largely prevented by co-treatment with NAC and the NAD<sup>+</sup> precursor nicotinamide riboside, supporting a model in which CI sustains the NAD<sup>+</sup> pool required for PARP1-mediated repair of oxidative damage at telomeres. The authors further report an inverse correlation between donor lymphocyte TL and mitoROS in the corresponding cybrids, and provide preliminary evidence that the K1a-defining ATP6 A177T variant (m.G9055>A) may be enriched in long-telomere individuals.

      We thank the reviewer for this very positive evaluation of our work.

      Weaknesses:

      (1) Statistical support and donor sampling for the central in vivo correlation (Figure 4C).

      The inverse correlation between donor lymphocyte TL and cybrid mitoROS (R<sup>2</sup>=0.794, p=0.007) is the principal in vivo claim of the paper, but it is built on seven donors deliberately selected from the extremes of the Flow-FISH distribution. Sampling at the tails of the outcome variable can substantially inflate apparent correlation strength and significance. I would encourage the authors to (i) explicitly state this sampling structure where the correlation is introduced, (ii) report a leave-one-out sensitivity analysis to confirm the relationship is not driven by one or two donors (Cyb3 and Cyb6 appear to anchor the line), and (iii) where feasible, extend the analysis to additional donors with intermediate TL to test whether the relationship holds across the full distribution. Even a modest expansion (e.g., 4 to 5 additional donors at P25 to P75) would substantially strengthen this central claim.

      We thank the reviewer for this insightful comment. We have conducted the requested leave-one-out analysis:

      - removing Cyb3: R<sup>2</sup>=0.730; p=0.0302

      - removing Cyb6 : R<sup>2</sup>=0.782 ; p=0.0194

      - removing Cyb1 : R<sup>2</sup>=0.740; p=0.0278

      While we agree that additional donors would enhance the study, further experiments are however currently impossible without new ethical clearances and additional clinical partnerships.

      (2) Reconciling the cybrid CI / TL relationship (Fig 3B) with the absence of a CI / TL relationship in donor lymphocytes (Figure 4A).

      Figure 3B shows a strong correlation between CI activity and TL in cybrids (R<sup>2</sup>=0.87), while Figure 4A shows no correlation between donor CI activity (measured in the same cybrids) and donor lymphocyte TL. The authors acknowledge this, but the manuscript subsequently builds toward a CI-centric model of in vivo TL regulation, which seems to outrun the data. The most internally consistent interpretation is that the cybrid CI phenotype reports a sensitized in vitro response to the acute oxidative stress of the metabolic shift, rather than a steady-state determinant of leukocyte TL. I would suggest reframing the abstract, significance statement, and Discussion to make this distinction clearer. The in vitro CI / NAD<sup>+</sup> / PARP1 axis is a strong finding on its own, while the in vivo role of CI activity (as opposed to ROS more broadly) is not yet established here. Donor #1's profile (very long lymphocyte TL, low CI activity, severe shortening in cybrids, no telomere inheritance in offspring) is informative in this regard and could be discussed more directly as a case that helps delineate where the cybrid model does and does not recapitulate in vivo biology.

      We acknowledge that our study does not establish the in vivo role of CI activity in TL regulation. Our abstract specifically highlights an in vitro phenomenon: “Under the specific conditions of cybrid formation, which involve a metabolic shift from glycolysis to oxidative phosphorylation, mtDNA variants associated with reduced CI activity induced rapid telomere shortening, …”.

      We nevertheless extensively revised the Abstract/Significance Statement to clearly separate our in vitro results from in vivo biology as requested:

      “Abstract

      Telomere shortening is a hallmark of aging, yet telomere length (TL) varies considerably among individuals and is strongly influenced by inheritance. In mice, efficient mitochondrial function, characterised by low reactive oxygen species (ROS) production, is critical for telomere elongation during early embryogenesis. Since mitochondrial DNA (mtDNA) encodes several subunits of the electron transport chain, it may influence TL at birth by regulating mitochondrial function in utero. To explore the relationship between mtDNA and TL in human, we used a transmitochondrial cybrid approach, introducing mitochondria from donor platelets with varying telomere lengths into mtDNA-depleted cells. This revealed an inverse correlation between donor blood TL and mitochondrial ROS levels measured in the resulting cybrids, suggesting that specific mtDNA variants may contribute to the maintenance of long telomeres in humans by enhancing mitochondrial fitness. During in vitro cybrid formation, a transient phase of oxidative stress precedes cellular adaptation. In this specific window, mtDNA variants associated with reduced complex I (CI) activity induced rapid telomere shortening—an effect rescued by antioxidant and NAD<sup>+</sup> precursor supplementation. While these variants occur naturally in certain individuals with long telomeres, our data suggest that, at least under in vitro conditions of acute oxidative stress, CI is critical to support PARP1 activity by maintaining the NAD<sup>+</sup>/NADH balance, thereby preserving telomere integrity. Collectively, these findings solidify the link between mtDNA variants and human TL regulation, highlighting potential therapeutic opportunities for mitochondrial replacement strategies.”

      “Significance Statement

      “Telomere length at birth influences aging trajectories and disease risk later in life, yet the mechanisms governing this trait remain incompletely understood. Using a trans mitochondrial cybrid approach, we show that single-nucleotide variants in the mitochondrial genome of healthy donors directly affect mitochondrial metabolism and reactive oxygen species production. In addition, mitochondrial ROS levels measured in cybrids inversely correlate with blood cell telomere length in donors. During cybrid formation, mitochondrial DNA variants associated with reduced CI activity promote telomere shortening. Attrition was reversed by antioxidant and NAD<sup>+</sup> precursor supplementation, pointing to an essential role for robust CI function in sustaining telomere length during acute oxidative stress, at least under in vitro conditions. Together, these findings establish a direct link between mitochondrial genetics, redox homeostasis, and telomere maintenance in human cells.”

      Overall, the manuscript has also been carefully edited to account for this comment.

      (3) The K1a / ATP6 A177T inheritance claim.

      The proposal that K1a (and specifically ATP6 A177T) contributes to maternal inheritance of long telomeres is intriguing but currently rests on three pedigrees (one of which, donor #1, does not support the hypothesis) and a chi-square test that does not reach significance (p=0.153, Figure 4F). The supporting evidence is also limited by the fact that platelet-mediated mitochondrial transfer delivers donor mitochondrial proteins, lipids, and residual mtRNA in addition to mtDNA, making it difficult to attribute the cybrid phenotype of donor #6 specifically to the ATP6 A177T variant. I would recommend either: (a) extending the genotyping screen to additional unrelated donors and, if feasible, confirming the effect of ATP6 A177T through an isogenic approach (e.g., mtDNA base editing in a clean background), or (b) softening the relevant statements to "suggestive trend warranting larger studies," and presenting the K1a observation as hypothesis-generating rather than supportive. The Ashkenazi-centenarian connection raised in the Discussion is an excellent direction for follow-up and could be framed accordingly.

      We agree that the evidence for the AT6 A177T inheritance claim remains inconclusive. To clarify, we do not argue that this mitochondrial variant is solely responsible for longer telomeres; indeed, the mtDNA genome of donor #1 suggests otherwise. Furthermore, the phenotypic impact of such mtDNA variants likely depends on nuclear variants in other telomere-related genes (e.g., hTERT or hTR), meaning AT6 A177T may not consistently result in elongated telomeres. Unfortunately, our ethical protocol precludes screening additional unrelated donors. We have revised the text to soften our statements accordingly.

      New references:

      DeBoy EA et al. Familial clonal hematopoiesis in a long telomere syndrome. 2023. N Engl J Med 388, 2422-2433.

      Davidson-Swinton HR et al. Lymphoid malignancy and clonality in the POT1-mediated long telomere syndrome. 2026. Blood 147, 2226-2237.

      Maranzana E et al. Mitochondrial respiratory supercomplex association limits production of reactive oxygen species from complex I. 2013. Antioxid Redox Signal 19, 1469-1480.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      Figure 3C. Please clarify. Do the first two bars represent NAMPT, and bars 3-4 represent NAPRT1?

      We thank the reviewer for pointing this out, and we have fixed the problem.

      Reviewer #2 (Recommendations for the authors):

      The authors discuss telomere shortening throughout the manuscript, but telomere length is measured only at a single time point. It would be more informative to pass the cells over several population doublings and determine the rate of telomere shortening. Longitudinal analysis across multiple passages, ideally starting immediately after cybrid generation and controlling for population doublings, would be required to determine whether mitochondria directly influence telomere attrition rates. Overall, I like the manuscript- I think it is interesting and impactful, but some controls are missing.

      We thank the reviewer for this positive evaluation of our work and have inserted the TRF results of our longitudinal analysis of telomere length in Cybrids #3 (high ROS), #6 (low ROS) and #7 (very low ROS) cultured until PD 66-67 after cloning. Data are shown as Fig S7.

      We observed the following shortening after 66-67 PDs:

      - Cyb3: about 1.6 kb reduction

      - Cyb6: about 1.2 kb reduction

      - Cyb7: about 0.8 kb reduction

      These results suggest that the rate of telomere shortening in culture may be higher in Cyb3 cells, possibly due to increased ROS levels.

      (1) Why would rho (0) have shorter telomeres than parental cells? Or decreased telomerase activity?

      We will look at this soon. Our current hypothesis, based on the recent work by the Agarwal’s lab, is that the short telomeres in 143B Rho0 cells happen because these cells lack the nuclear-encoded TK1 enzyme and cannot make pyrimidines through the salvage pathway or de novo (since dihydroorotate dehydrogenase needs working mitochondria). When mitochondria return, thymidine levels may rise and help telomerase work again, potentially through an allosteric mechanism as previosuly suggested (Mannherz and Agarwal, Nat Genet 2023).

      This was already discussed in our manuscript (Discussion):

      “Our study also unexpectedly revealed a reduction in telomere length in 143B cells following mitochondrial depletion. This telomere shortening was associated with decreased telomerase activity, as measured by ddTRAP, but not with reduced expression of the telomerase subunits hTERT or hTR. 143B osteosarcoma cells are deficient in thymidine kinase 1 and therefore lack an effective pyrimidine salvage pathway. In the absence of oxidative phosphorylation, the de novo thymidine synthesis pathway is also compromised, rendering 143B r<sup>0</sup> cells dependent on uridine supplementation for survival. Although this hypothesis requires further investigation, we propose that the shorter telomeres observed in 143B r<sup>0</sup> cells may be linked to the emerging role of thymidine nucleotide metabolism in the regulation of human telomere length, potentially through an allosteric effect of dTTP on telomerase activity (4143).”

      (2) Why does 2C data show no variation? How many biological replicates?

      We showed hTR and hTERT expression levels in one biological replicate of two independent cybrid clones from each donor, with technical replicates for each measurement. Measurements of hTERT and hTR expression levels over successive PDs were performed for some clones and showed good consistency.

      (3) Why did the TIF analysis not compare parental and Rho (0) cells?

      We have now added the data in Fig 2D.

      Figure 2E is only a representative image; no quantification is provided, so no conclusions about fusion can be made.

      We have now quantified chromosome end fusions in the parental 143B Rho0, Cyb1 and Cyb6 cells and have included the quantifications in our revised manuscript (Fig 2E):

      “E. Left: Visualisation of telomere fusions (white arrowheads) in Cyb1 cells at PD7. 143B r<sup>0</sup> and Cyb6 cells are shown as controls. Telomeres are detected by FISH (red) and DAPI stains DNA (blue). Scale bar: 5 µm. Right: Quantification of telomere fusions. The total number of analyzed chromosomes is shown for each cell line. Χ<sup>2</sup> test. ns: p>0.05.”

      (4) In Figure 3, I found it difficult to interpret the data shown in D (what is each lane?).

      Each lane shows TL of an independent hybrid clone. We have clarified the legend accordingly.

      Why is the data in E shown this way? How many biological replicates, and why no experimental validation?

      Panel E quantifies the TRF analyses conducted on independent cybrid clones. These clones were isolated from new cybridizations of donor 2’s platelets with 143B Rho0 cells under the specified conditions. The specific number of independent cybrid clones (which we consider as biological replicates) for each condition is shown in the graph: NAA: 5, NAC: 7, NAC + NR: 8, NAA + NR: 8. We have clarified the legend as follows. We hope this is clearer now.

      “E. Quantification of the TRF analyses conducted on independent cybrid clones isolated in the conditions detailed in D. The percentage of clones with average TL>2.5 kb was calculated. The specific number of independent cybrid clones analyzed for each condition is shown in the graph: NAA: 5, NAC: 7, NAC + NR: 8, NAA + NR: 8.”

      (5) Did NAC and NR also reduce TIF or telomere fusions?

      We did not test this. We expect NAC/NR treatment to reduce TIF and telomere fusions indeed.

      For the Parylation experiments, how many independent experiments were performed?

      Eight independent cybrid clones obtained from 4 independent cybridisations were analyzed. This has now been detailed in the legend as follows :

      “F. Representative images and quantification of telomeric parylation in 8 independent Cyb2 clones obtained from 4 independent cybridisations, comparing cells that did or did not exhibit telomere shortening during the initial PDs following cybridisation (from panel D-E).”

      (6) Figure 4. Why were mitochondrial superoxide levels not measured in parental cells?

      We excluded Rho0 cells from our superoxide measurements because these cells were grown in a different culture medium. Instead, we focused on comparing mitochondrial ROS across cybrids to accurately correlate these values with the telomere length of the corresponding donors’ lymphocytes. Consequently, Rho0 cell measurements would not have contributed to this correlation analysis.

      We have discussed this in the revised manuscript:

      “Mitochondrial superoxide production was measured by electron paramagnetic resonance (24) in clones #1 of all cybrids and in 143B cells (Fig 4B). We excluded 143B r<sup>0</sup> cells from our superoxide measurements because these cells were grown in a different culture medium.”

      Reviewer #3 (Recommendations for the authors):

      Additional analyses for Figure 4C. Please report a leave-one-out sensitivity analysis for the lymphocyte TL versus cybrid mitoROS correlation,

      We have conducted the requested leave-one-out analysis:

      - removing Cyb3: R<sup>2</sup>=0.730; p=0.0302

      - removing Cyb6: R<sup>2</sup>=0.782; p=0.0194

      - removing Cyb1: R<sup>2</sup>=0.740; p=0.0278

      We chose not to include this analysis in the revised manuscript.

      and state in the legend that donors were selected at the extremes of the Flow-FISH distribution.

      This is not exactly the case, but we nevertheless added this sentence in the legend:

      “TL in the donor lymphocytes was distributed as follows: >P90 (#1, #6 and #7), around P50 (#2 and #4), between P10 and P50 (#5) and at P10 (#3).”

      If feasible, extend the analysis to 4 or 5 additional donors with intermediate TL (P25 to P75) to test whether the relationship holds across the full distribution.

      While we agree that additional donors would enhance the study, further experiments are however currently impossible without new ethical clearances and additional clinical partnerships.

      Reframing of the in vivo claims. Please calibrate the language in the abstract, significance statement, and Discussion so that the in vitro complex I / NAD<sup>+</sup> / PARP1 mechanism and the in vivo role of the mitochondrial genome are presented at the appropriate levels of evidence. A brief paragraph in the Discussion explicitly addressing donor #1 (long lymphocyte telomeres, low complex I activity, telomere shortening in cybrids, no inheritance of long telomeres in offspring) would be helpful in delineating where the cybrid model does and does not recapitulate in vivo biology.

      The text has been thoroughly revised in accordance with this suggestion. We kindly invite you to review the updated manuscript for full details.

      Strengthening the K1a / ATP6 A177T claim. Two options would address the concern raised in the public review. First, extending the genotyping screen to additional unrelated donors until the chi-square test reaches the level of evidence consistent with the wording in the abstract.

      Unfortunately, further experiments are currently impossible without new ethical clearances.

      Second, if a collaboration is available, an isogenic introduction of the m. G9055>A variant in a clean mitochondrial background through mitochondrial base editing or mitoTALENs would directly test causality.

      This would certainly be an excellent approach to test causality indeed and we fully agree that future collaborations with specialized labs would be highly relevant in this context.

      If neither is feasible, please soften the statements to a suggestive trend warranting larger studies.

      We chose to soften our claims instead; please see the revised manuscript for details.

      Direct test of PARP1 involvement. A PARP1 knockdown or a PARP inhibitor co-treatment in Cyb2 during fusion would directly test whether the NAC + nicotinamide riboside rescue depends on PARP1 activity, as the model proposes. If this experiment is not feasible, please state so in the Discussion.

      Again, redoing cybridisations is currently impossible without new ethical clearances. We nevertheless acknowledge that the suggested experiment is interesting and we discussed it in the revised manuscript as follows:

      “Mitochondrial platelets with low CI activity triggered significant telomere shortening in recipient cells during early cybrid formation -a loss that was prevented by co-treatment with an antioxidant and an NAD<sup>+</sup> precursor. Although we did not determine whether the rescue was dependent on PARP1, these results support the essential role of CI in maintaining PARP1 activity via regulation of the NAD<sup>+</sup>/NADH balance.”

      Figure 1C/D legend says "eight selected donors" twice (lines 635, 636), but the text says "seven donors" (lines 132, 258), and donors are numbered #1-#7 throughout. This is a real internal inconsistency in the manuscript that the authors should fix.

      We have fixed this mistake. Thanks for bringing this to our attention.

    1. Author response:

      The following is the authors’ response to the original reviews.

      eLife Assessment:

      This study presents a valuable investigation of how inhibition of the WNK-SPAK/OSR1 pathway influences neuronal chloride homeostasis and seizure-like activity in organotypic hippocampal slice cultures. The evidence supporting the principal mechanistic conclusions is incomplete because several proposed mechanisms are inferred from changes in chloride dynamics rather than directly demonstrated. The work will be of interest to researchers studying chloride homeostasis, inhibitory neurotransmission, and epilepsy.

      We appreciate the thoughtful reviews and assessment. Additional data analysis has been performed, and the paper has been carefully modified to address each concern, as described below.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      The authors used extracellular field potential recordings and two-photon imaging to monitor neuronal network activity and intracellular chloride concentration ([Cl-]i) in organotypic hippocampal slices from mice expressing the genetically encoded chloride fluorophore Clomeleon. These slices were used as a model of acute traumatic brain injury and epileptogenesis in vitro. The study provides evidence that blocking the WNK-SPAK/OSR1 pathway with WNK463 alleviates epileptic activity, and that this anticonvulsant effect involves suppression of the chloride loader NKCC1 and enhancement of chloride extrusion via KCC2. Overall, this is a solid study with a comprehensive pharmacological analysis.

      Strengths:

      The conclusions are well supported by the detailed pharmacological analysis.

      Weaknesses:

      The only weakness I see is the absence of cellular-level electrophysiology, which precludes interpretation of the imaging data in the context of GABA action polarity.

      The referee correctly points out that we did not perform cellular-level electrophysiological measurements. Before the advent of transgenic ratiometric chloride-sensitive fluorophores, we conducted detailed studies of neuronal cation-chloride transport using electrophysiological measures (Staley and Proctor, 1999). We did not measure membrane potential in the current study because this data is not needed for characterization of cation-chloride membrane cotransport, which is electroneutral. Electroneutral processes are not affected by membrane potential, and electroneutral processes in turn do not alter the membrane potential. We did not measure membrane GABA currents because the polarity of GABA currents was clearly demonstrated by our fluorometric measures of the corresponding increases or decreases in cytoplasmic chloride concentration (Figure 2). We have added the following sentence to the Discussion (Page 16): “In this fluorometric study, we did not measure RMP and E<sub>GABA</sub> directly, but rather inferred the impact of electroneutral cation-chloride transport on these parameters from the effects on [Cl<sup>-</sup>]<sub>i</sub> (Figure 2) and seizure activity (Figures 1, 3-9)”.

      Reviewer #2 (Public review):

      Summary:

      The authors investigate whether inhibition of the WNK-SPAK/OSR1 pathway using the allosteric inhibitor WNK463 improves neuronal chloride homeostasis and suppresses epileptiform activity in organotypic hippocampal slice cultures. Using Super Clomeleon imaging combined with extracellular field recordings, they demonstrate that WNK463 accelerates recovery of intracellular chloride following chloride loading, reduces interictal chloride accumulation, and progressively suppresses recurrent ictal-like discharges. Pharmacological inhibition and siRNA-mediated knockdown of NKCC1 and KCC2 are then used to investigate the contribution of these transporters to the anti-ictal effects of WNK463.

      Strengths:

      The study addresses an important question in the field of chloride homeostasis and epilepsy and combines complementary experimental approaches. In particular, the distinction between baseline chloride measured in the presence of TTX and activity-dependent interictal chloride accumulation provides a useful conceptual framework for interpreting previous studies of WNK-SPAK inhibition. The imaging, electrophysiological, and pharmacological data are internally consistent and support the conclusion that WNK463 alters chloride dynamics and substantially suppresses ictal-like activity in this model.

      Weaknesses:

      The principal limitation of the manuscript is that several mechanistic conclusions extend beyond the experimental observations. Throughout the results and discussion, the authors interpret the observed changes in intracellular chloride dynamics as evidence of enhanced CCC-mediated chloride extrusion, while the pharmacological and siRNA-mediated experiments are interpreted as supporting coordinated NKCC1 inhibition and KCC2 activation, ultimately leading to restoration of GABAergic inhibition and negative shifts in EGABA. While these interpretations are plausible and consistent with the data, they remain inferential because transporter phosphorylation or activity, EGABA, and inhibitory synaptic function were not directly assessed in the current study. Moreover, although the pharmacological and knockdown experiments support a contribution of NKCC1 and KCC2 to the actions of WNK463, they do not definitively establish coordinated modulation of both transporters as the primary mechanism underlying seizure suppression. These mechanistic conclusions should therefore be presented more cautiously.

      The referee correctly points that we did not definitively establish the link between coordinated modulation of NKCC1 and KCC2 transporter activity, changes in EGABA and GABA function to the anti-ictal action of WNK463. Indeed we have an entire section of results dedicated to the anti-ictal effects of WNK463 that persist after block of NKCC1 and KCC2. The primarily biochemical study by Lee et al (2022) demonstrated that the WNK-SPAK/OSR1 inhibitor WNK463 reduced KCC2-T1007 phosphorylation and EGABA in cultured cortical neurons challenged with high 30 mM [Cl<sup>-</sup>]<sub>i</sub> in vitro, and limited KA-induced status epilepticus in vivo. We are studying the same system with different pharmacological, electrophysiological, optogenetic and morphological tools during spontaneous ictal-like epileptiform discharges in organotypic hippocampal slices in vitro. We prominently cite the previous study and clearly report new findings and demonstrate underlying mechanisms. We have also modified the language surrounding our conclusions (e.g. last sentence of abstract, and last sentence of first paragraph of Discussion).

      The manuscript would also benefit from broader contextualization within the current literature. The introduction largely focuses on previous work from the authors' group and provides a relatively narrow overview of chloride homeostasis in epilepsy. In particular, the discussion would benefit from broader consideration of studies examining KCC2 dysfunction in human epilepsy and experimental models, alternative mechanisms regulating KCC2 activity following seizures, and recent therapeutic strategies targeting KCC2.

      We agree. We have added the following paragraph to the Discussion (p. 16-17): “The KCC2 protein is a potassium-chloride co-transporter that maintains low [Cl<sup>-</sup>]<sub>i</sub> (Rivera et al., 1999). KCC2 dysfunction has been implicated in epilepsy across human and experimental studies. Reduced KCC2 expression and impaired chloride extrusion have been demonstrated in resected tissue from patients with temporal lobe epilepsy, and pathogenic variants in SLC12A5 further support a causal role for impaired KCC2 function in human epilepsy (Huberfeld et al., 2007; Puskarjov et al., 2014). Experimental seizures can suppress KCC2 through several mechanisms in addition to WNK-SPAK/OSR1 signaling, including BDNF-TrkB-dependent downregulation, dephosphorylation of the stabilizing Ser940 site with subsequent internalization, and calpain-mediated proteolysis (Rivera et al., 2004; Silayeva et al., 2015; Puskarjov et al., 2012). These convergent mechanisms suggest that loss of KCC2 function may both result from and amplify seizure activity by weakening GABAergic inhibition. Accordingly, KCC2 has emerged as a therapeutic target: strategies include modulation of regulatory phosphorylation, enhancement of KCC2 expression, and direct pharmacological potentiation. Notably, the KCC2 activator OV350 enhances chloride extrusion and suppresses experimental seizures, including benzodiazepine-refractory status epilepticus, providing proof-of-concept for direct KCC2 activation as an antiseizure strategy (Jarvis et al., 2023).”

      Finally, although the authors appropriately acknowledge that the experiments were performed exclusively in vitro, the discussion could more explicitly address the limitations of the organotypic hippocampal slice model, including how culture-induced network reorganization and spontaneous epileptiform activity may influence chloride homeostasis and the extent to which these findings generalize to traumatic brain injury and chronic epilepsy in vivo. In addition, the statistical analysis would benefit from clarification regarding the experimental unit and the treatment of repeated measurements.

      Thank you. We addressed the limitation of organotypic hippocampal slices in vitro in the Limitation and Future Directions paragraph (p. 18-19): “Our experiments were conducted in organotypic hippocampal slices in vitro. Advantages of this preparation include homogenous injury and consistent epileptogenesis. This provides excellent control of the extracellular environment and imaging but does not replicate the in vivo vascular supply and maintenance of ionic homeostasis. While we find that increased WNK-SPAK/OSR1-mediated KCC2 activity via enhanced Cl<sup>-</sup> extrusion rates robustly reduces seizure activity in vitro, it is possible that in vivo, increased KCC2 activity could lead to extracellular potassium accumulations (Viitanen et al., 2010) that would limit Cl<sup>-</sup> extrusion independently of the velocity of KCC2 transport (Thompson et al., 1988; Staley and Proctor, 1999). Thus, it will be important to assess these findings in vivo.”

      We provided better clarification regarding the treatment of repeated measurements (p. 22): “Experimental data were analyzed using a repeated measures ANOVA for two types of study design. Studies that investigated either (1) changes in mean (median) parameters over three or more time points or consecutive time intervals; or (2) differences in mean (median) parameters under three or more different conditions”.

      Reviewer #3 (Public review):

      Summary:

      Dzhala and colleagues present findings from organotypic slice cultures suggesting that simultaneous modulation of the complementary cation-chloride cotransporters NKCC1 and KCC2 through inhibition of the WNK-SPAK/OSR1 pathway reduces seizure-like activity. The manuscript is generally well written, and the data support the conclusion that WNK463 exerts robust anti-ictal effects in this model. However, several issues should be addressed to strengthen the mechanistic interpretation and statistical rigor of the study, and improve confidence in the conclusions.

      Strengths:

      (1) The study addresses an important mechanistic question by investigating how inhibition of the WNK-SPAK/OSR1 pathway with WNK463 influences seizure activity and neuronal chloride homeostasis.

      (2) The experimental design is logical and comprehensive, progressing from characterization of chloride dynamics to pharmacological and genetic interrogation of the underlying mechanism using multiple complementary approaches, including pharmacological inhibition, siRNA-mediated knockdown, electrophysiology, and chloride imaging.

      (3) The combination of simultaneous extracellular electrophysiology and two-photon chloride imaging provides complementary functional and mechanistic information and represents a major technical strength of the study.

      (4) The TTX experiments elegantly distinguish activity-dependent chloride accumulation from resting intracellular chloride concentration, substantially strengthening the central mechanistic conclusions.

      Weaknesses:

      (1) The mechanistic conclusions regarding KCC2 activation and NKCC1 inhibition are stronger than the data directly support. Throughout the manuscript, the authors conclude that WNK463 activates KCC2 and inhibits NKCC1. Although this interpretation is consistent with the established biology of the WNK-SPAK/OSR1 pathway, the evidence presented here is indirect. Specifically, the authors infer KCC2 activation and NKCC1 inhibition from the observation that pharmacological inhibition or siRNA-mediated knockdown of these transporters alters the effects of WNK463, together with measurements of chloride dynamics. While these findings are compatible with a KCC2- and NKCC1-dependent mechanism, they do not directly establish that WNK463 regulates either transporter. Direct evidence would require measurements of transporter activity, phosphorylation state, membrane expression, or other biochemical indices of transporter regulation. I therefore recommend that the authors both temper the mechanistic language throughout the manuscript and explicitly acknowledge in the Discussion that the proposed regulation of KCC2 and NKCC1 is inferred from indirect evidence rather than directly demonstrated in the present study.

      We agree. We modified the key conclusory sentences in the Abstract and Discussion as described in the response to referee 2. The referee correctly points that we did not directly establish the link between the action of WNK463 and coordinated activation of KCC2 and inhibition NKCC1. We highlighted the established link in the discussion (p. 17-18): “NKCC1 and KCC2 are rapidly stimulated and inhibited, respectively, by direct phosphorylation mediated by the Cl<sup>-</sup>-sensitive WNK-SPAK/OSR1 complex (Alessi et al., 2014). The WNK family senses changes in the [Cl<sup>-</sup>]<sub>i</sub>, cell volume, extracellular osmolarity and transduces this information to CCCs (Shekarabi et al., 2017). WNKs stimulate the kinases SPAK and OSR1, which directly phosphorylate and stimulate NKCC1 or inhibit KCC2 (Kahle et al., 2013), providing compensatory and reciprocal regulation between transporters activity to maintain chloride homeostasis and neuronal excitability (Hartmann and Nothwang, 2022). Conversely, inhibiting the WNK-SPAK/OSR1 pathway might be an especially potent strategy to reduce neuronal Cl<sup>-</sup> elevation and facilitate neuronal Cl<sup>-</sup> extrusion by coincident NKCC1 inhibition and KCC2 activation…” Consistently with the established biology of the WNK-SPAK/OSR1 pathway we found that (p.15): “…WNK463 improved [Cl<sup>-</sup>]<sub>i</sub> homeostasis, progressively enhanced postictal [Cl<sup>-</sup>]<sub>i</sub> extrusion rates, reduced ictal duration and abolished recurrent ILDs. Our pharmacological investigations suggest that the powerful anti-ictal effects of WNK463 are mediated by reduced NKCC1 and enhanced KCC2 transport activity...”

      (2) The conclusions drawn from the siRNA-mediated knockdown experiments should be interpreted more cautiously. First, it is unclear whether silencing NKCC1 or KCC2 induced compensatory changes in the expression or function of the complementary cotransporter. Given the well-established interplay between NKCC1 and KCC2 in regulating intracellular chloride homeostasis, compensatory adaptations could influence the interpretation of these experiments and should be addressed or acknowledged as a limitation. Second, the sample size for the siRNA experiments appears relatively small. It is unclear how many independent animals contributed slices to each experimental group, making it difficult to assess the degree of biological replication. In addition, effect sizes are not reported. Clarifying the number of biological replicates and reporting effect sizes would improve the rigor of the statistical analysis and increase confidence in these findings.

      We agree and now address this in the discussion (p. 17-18): “WNKs stimulate the kinases SPAK and OSR1, which directly phosphorylate and stimulate NKCC1 or inhibit KCC2 (Kahle et al., 2013), providing compensatory and reciprocal regulation between transporters activity to maintain chloride homeostasis and neuronal excitability (Hartmann and Nothwang, 2022). ”

      We agree that the sample size for the siRNA electrophysiological experiments is relatively small (n=3-4 slices). We now clarify the number of mice were used per each experimental group (p.19). We provide the n (number of slices) and the number of paired cells in the Results and for every experimental conditions.

      (3) The final pharmacological experiments require clarification, as the conclusions appear internally inconsistent. Earlier experiments suggest that the anticonvulsant effects of WNK463 depend on coordinated regulation of both NKCC1 and KCC2. However, in the final experiment, the authors state that simultaneous pharmacological inhibition of NKCC1 and KCC2 does not prevent the anticonvulsant effects of WNK463. In contrast, the accompanying statistical analysis indicates that combined transporter inhibition significantly reduces the effect of WNK463 relative to control conditions. These interpretations appear inconsistent and make it difficult to determine the extent to which the anticonvulsant action of WNK463 depends on NKCC1 and KCC2. The authors should clarify whether simultaneous inhibition of both transporters completely abolishes, partially attenuates, or merely reduces the magnitude of the WNK463 response, and revise the text accordingly. If the effect is only partially attenuated, alternative mechanisms contributing to the anticonvulsant actions of WNK463 should also be considered and discussed.

      We agree. Our data demonstrated that WNK463 had no effect in the presence of high concentration of bumetanide (500 µM) that nonspecifically blocks CCCs (NKCC1 and KCC2-3) (Figure 6). In contrast (p. 15): ”Simultaneous inhibition of NKCC1 and KCC2 by the combination of bumetanide (10 µM) and VU0463271 (1 µM) significantly reduced the anti-ictal effects of WNK463 (Figure 9).” The conclusory sentence in the Results indicates (p.15): “These results suggest that the anti-ictal effects of WNK-SPAK/OSR1 inhibitor WNK463 are mainly due to downstream interactions with NKCC1 inhibition and KCC2 activation, with additional effects due to interactions with an unidentified Cl<sup>-</sup> transporter (e.g. KCC3) or exchanger, or channel.”

      (4) The statistical analysis and reporting require further attention. First, median values should not be reported with standard deviations, as standard deviation describes variability around the mean rather than the median. For non-normally distributed data, the authors should report median values together with an appropriate measure of variability, such as the interquartile range (25th-75th percentile) or another suitable summary. Second, in several instances, ANOVA results are reported using only a single degree of freedom value (e.g., page 6, DF = 53). This is incomplete, as an F statistic is defined by two degrees of freedom: the numerator degrees of freedom (between-group variability) and the denominator degrees of freedom (within-group variability). Reporting statistical results using standard notation (F(df_between, df_within) = F statistic, p = value) would improve clarity and allow proper interpretation of the analyses.

      Thank you. Group measures are expressed now as mean ± standard deviation (SD) or median (25%-75%) as indicated. In a one-way RM ANOVA, (DF) represents the between-groups degree of freedom, and (F) represents the F-statistic and reported as F(DF<sub>treatment</sub>, DF<sub>residual</sub>)=value. In the Friedman RM ANOVA on Ranks, the chi-square statistic was used to assess the differences between the groups. The Tukey Test or Holm-Sidak Test was used for all pairwise comparisons of the responses to the different treatment groups. Please see Statistical Analysis in the Methods section (p.23-24).

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      I have only minor comments/suggestions.

      (1) While [Cl<sup>-</sup>]i and ECl are informative parameters, interpreting the GABA driving force and determining whether depolarizing/excitatory GABA actions during seizures or interictal states are alleviated by treatment requires knowledge of the membrane potential and its dynamics during epileptic events. I would recommend including this information if available. Gramicidin perforated-patch recordings (ideally) would substantially strengthen the conclusions, at least for a critical subset of experiments.

      Please see our response above. We have added the following sentence to the discussion (page 16): “In this fluorometric study, we did not measure RMP and EGABA directly, but rather inferred the impact of electroneutral cation-chloride transport on these parameters from the effects on [Cl<sup>-</sup>]<sub>i</sub> (Figure 2) and seizure activity (Figures 1, 3-9)”.

      (2) Did the authors observe any signs of cell shrinkage in response to WNK463, or transient cellular swelling during interictal-like discharges (ILDs) and its prevention by WNK463? Given that cytotoxic edema is typically associated with increased tissue light transparency and shrinkage of the extracellular space (e.g., as measured with TMA⁺), this reviewer wonders whether such approaches could be used as a proxy for cell swelling. Tissue edema, which manifests as increased tissue volume, could also be assessed by measuring slice thickness.

      These are excellent ideas and cell volume is an area of interest for us, but we would argue that assessment of volume effects are outside the scope of the current 9-figure study. We observed cell volume (transverse area) increases during prolonged ictal-like discharges. This effect was prevented by WNK463 during suppression of ictal-like discharges. However, we did not provide the volume analysis in this paper.

      (3) The paper should be corrected for spelling and grammar (e.g., Figure 2 legend: "(b) Linier regression analysis revealed that... " - probably should be "Linear... "?).

      Thank you. Corrected.

      Reviewer #2 (Recommendations for the authors):

      (1) Temper mechanistic statements throughout the manuscript by clearly distinguishing experimental observations from inferred mechanisms and by explicitly framing conclusions regarding coordinated NKCC1/KCC2 modulation, chloride extrusion, EGABA, and restoration of GABAergic inhibition as interpretations supported by, rather than directly demonstrated by, the current data.

      We have softened the key conclusory sentences in the Abstract and Discussion as described above. In the introduction, we highlighted the potential of both NKCC1 and KCC2 targeting for control of seizures (p. 2): “Previous studies have demonstrated that inhibition of NKCC1 reduced [Cl<sup>-</sup>]<sub>i</sub> in injured neurons, enhanced GABAergic inhibition and the efficacy of anticonvulsants (Pond et al., 2006; Dzhala et al., 2008; Dzhala et al., 2024; Nardou et al., 2011; Cleary et al., 2013; Sivakumaran and Maguire, 2016; Soul et al., 2021). Conversely, enhancement of KCC2 activity improved [Cl<sup>-</sup>]<sub>i</sub> extrusion and control of seizures (Gagnon et al., 2013; Moore et al., 2018; Dzhala and Staley, 2021).”

      In the discussion we highlighted the potential of coordinated NKCC1 and KCC2 modulation (p. 17-18): “NKCC1 and KCC2 are rapidly stimulated and inhibited, respectively, by direct phosphorylation mediated by the Cl<sup>-</sup>-sensitive WNK-SPAK/OSR1 complex (Alessi et al., 2014). The WNK family senses changes in the [Cl<sup>-</sup>]<sub>i</sub>, cell volume, extracellular osmolarity and transduces this information to CCCs (Shekarabi et al., 2017). WNKs stimulate the kinases SPAK and OSR1, which directly phosphorylate and stimulate NKCC1 or inhibit KCC2 (Kahle et al., 2013). Conversely, inhibiting the WNK-SPAK/OSR1 pathway might be an especially potent strategy to reduce neuronal Cl<sup>-</sup> elevation and facilitate neuronal Cl<sup>-</sup> extrusion by coincident NKCC1 inhibition and KCC2 activation…”

      (2) Expand the introduction and discussion to provide a more balanced overview of the current literature on chloride homeostasis in epilepsy, including alternative mechanisms regulating KCC2 dysfunction and recent therapeutic strategies targeting KCC2.

      In the introduction, we highlighted the potential of both NKCC1 and KCC2 targeting for control of seizures (p. 2): “Previous studies have demonstrated that inhibition of NKCC1 reduced [Cl<sup>-</sup>]<sub>i</sub> in injured neurons, enhanced GABAergic inhibition and the efficacy of anticonvulsants (Pond et al., 2006; Dzhala et al., 2008; Dzhala et al., 2024; Nardou et al., 2011; Cleary et al., 2013; Sivakumaran and Maguire, 2016; Soul et al., 2021). Conversely, enhancement of KCC2 activity improved [Cl<sup>-</sup>]<sub>i</sub> extrusion and control of seizures (Gagnon et al., 2013; Moore et al., 2018; Dzhala and Staley, 2021).” We did not provide additional references to comply with the word limit. We have added a paragraph and citations (pp. 16-17) to the Discussion to address this issue.

      (3) Discuss more explicitly the limitations of the organotypic hippocampal slice model when extrapolating the findings to traumatic brain injury and chronic epilepsy in vivo.

      Please see our response above. We discussed the limitation of the organotypic hippocampal slice model in the Limitations and future directions section (p. 18-19): “Our experiments were conducted in organotypic hippocampal slices in vitro. Advantages of this preparation include homogenous injury and consistent epileptogenesis (Berdichevsky et al., 2012). This provides excellent control of the extracellular environment and imaging but does not replicate the in vivo vascular supply and maintenance of ionic homeostasis. While we find that increased WNK-SPAK/OSR1-mediated KCC2 activity via enhanced Cl<sup>-</sup> extrusion rates robustly reduces seizure activity in vitro, it is possible that in vivo, increased KCC2 activity could lead to extracellular potassium accumulations (Viitanen et al., 2010) that would limit Cl<sup>-</sup> extrusion independently of the velocity of KCC2 transport (Thompson et al., 1988; Staley and Proctor, 1999). Thus, it will be important to assess these findings in vivo.”

      (4) Clarify how repeated measurements from individual cells and slices were handled in the statistical analyses, including the experimental unit for each analysis.

      We clarified in the methods (p.22): “Experimental data were analyzed using a repeated measures ANOVA for two types of study design. Studies that investigated either (1) changes in mean (or median) parameters over three or more time points or consecutive time intervals); or (2) differences in mean (or median) parameters under three or more different conditions”.

      Reviewer #3 (Recommendations for the authors):

      (1) The manuscript would also benefit from including statements regarding randomization, blinding (beyond the immunohistochemistry analysis), and any inclusion or exclusion criteria, as these details are increasingly expected to improve transparency and reproducibility.

      We agree. Images were blinded for the immunohistochemistry analysis (p. 21) and quantitative analysis of intracellular chloride changes (p. 23). Cells that did not respond to GABA/L-glutamate puff applications (Figure 2) and chloride transients that failed to fit an exponential decay function (p. 5) were excluded from the analysis. All other data generated or analyzed during this study were included in the manuscript.

      (2) The duration of baseline recordings prior to drug application should be specified in the Methods.

      Thank you. This information included in the Method section (p.19): “Slices were stabilized for 10-20 min in ACSF prior recordings and/or imaging”.

      (3) Some wording could be refined for readability. For example, "insignificantly reduced " on pages 8 and 14 would be more appropriately stated as "did not significantly reduce. "

      Thank you. Corrected.

      (4) The first sentence of the Introduction refers to "anticonvulsant (AED)-resistant seizures. " I suspect the authors intended "antiepileptic drug (AED)-resistant seizures, " as the current wording does not match the acronym.

      Thank you. Corrected.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Review:

      Reviewer #1 (Public review):

      Leukemia-driving NUP98 oncofusion proteins form chromatin-associated biomolecular condensates in the nucleus, and these structures are important for oncogenic transformation. Most NUP98 fusions do not contain domains that mediate the recognition of specific DNA elements. Instead, they entail domains that are important for chromatin regulation. For instance, the NUP98::KDM5A fusion features a fusion of the NUP98 N-terminus with the third PHD domain of the histone demethylase KDM5A. As PHD domains are critical for the recognition of methylated histones without any sequence specificity, it is not clear what controls the condensation and chromatin binding of NUP98::KDM5A, leading to the induction of oncogenic transcriptional programs.

      In this work, the authors use a combination of cellular and in vitro studies to show that biomolecular condensation of NUP98::KDM5A is dependent on H3K4me3 binding. Their model proposes that concentration-dependent chromatin-associated condensation of NUP98::KDM5A depends on local densities of H3K4me3 on chromatin and the levels of the fusion oncoprotein. In line with this, the analysis of gene expression data from NUP98::KDM5A-positive AML cells shows a positive correlation between differentially expressed genes and H3K4me3 levels.

      This is an interesting manuscript that aims to dissect the molecular mechanisms underlying biomolecular condensation of the NUP98::KDM5A oncoprotein. The work is solid, and the results are well explained and presented in a logical order. However, the study suffers from several weaknesses that if addressed would improve the study.

      Major points:

      (1) All cellular experiments are performed in settings of transient transfection of NUP98::KDM5A in non-hematopoietic cell types. These conditions are not physiologically relevant, as these cells do not depend on the fusion oncogene. Therefore, any claims about concentration-dependent effects on condensation need to be validated in AML cells that are driven by NUP98::KDM5A. While this may not be possible in primary patient-derived cells, several groups have published AML models of NUP98::KDM5A-driven AML that could be used.

      We appreciate the reviewer’s point regarding physiological relevance. Our goal in these cellular microscopy experiments was to dissect the biophysical principles of NUP98::KDM5A (including its mutants) condensate formation under controlled expression levels (concentration). While AML model systems driven by NUP98::KDM5A are available, they do not offer this possibility because of pre-existing NUP98::KDM5A expression. Suspension culture of hematopoietic cells also poses practical challenges for correlative FISH+IF and high-resolution microscopy analysis. We agree that validating our observed behaviors in AML models would be valuable, e.g. by creating HSPC lines with inducible expression of tagged NUP98::KDM5A and its mutants, but such experiments fall outside the scope of the current study. We will add text acknowledging this limitation and clarifying that our mechanistic conclusions are grounded in biophysical principles that should generalize across cell types.

      In the revised manuscript, we have added a section on study limitations at the end of the discussion section:

      Study limitations: Cellular experiments in this study were performed using transient transfection of WT NUP98::KDM5A and its mutants in HEK293 and U2OS cells. While these non-hematopoietic cell models limit physiological relevance, they allowed for controlled expression levels in the absence of endogenous oncofusion and the ease of imaging, enabling investigation of the biophysical principles of condensate formation, the main objective of our study.

      (2) The results presented in Figure 4 are not entirely supportive of the mechanism. It is known that active gene expression correlates with high H3K4me3 levels; therefore, the correlations shown by the authors are expected. Yet, the authors do not discuss the fact that many H3K4me3-positive genomic regions do not show NUP98::KDM5A binding. This should be elaborated on in the discussion section.

      We agree that active transcription correlates with H3K4me3, and that this baseline relationship must be considered. Our analysis explicitly uses fold-change between patient cells and healthy controls as the readout. This comparison inherently accounts for the activating effect of H3K4me3 itself. Regarding the reviewer’s comment that “many H3K4me3-positive genomic regions do not show NUP98::KDM5Abinding”, we would like to clarify that this point is exactly what our manuscript aims to explain. Our cell line studies show that, at patient-relevant expression levels, NUP98::KDM5A condensates form preferentially at H3K4me3 loci with high local mark density. Considering that NUP98::KDM5A concentration in the nucleus is lower than the KD between KDM5A PHD3 and H3K4me3, this means that H3K4me3 loci with lower mark density will not see NUP98::KDM5A binding without the high local concentration of the fusion protein (as a result of condensate formation). This is consistent with our observation that genes with the highest local density show disproportionately stronger upregulation.

      We have modified the final paragraph of the section describing our analysis of gene expression in patient samples to add:

      Importantly, to account for the activating effect of H3K4me3 itself, our analysis explicitly uses fold-change between patient cells and healthy controls as the readout.

      (3) While the focus of the manuscript is on NUP98::KDM5A, this oncofusion is part of a family of >30 fusions that join the NUP98 N-terminus to a variety of factors with roles in epigenetic control and transcription. While the repertoire of NUP98 fusion partners is diverse with regard to functional domains, they all induce a conserved set of target genes that is characteristic of this leukemia subtype. How can this be achieved in the context of NUP98 fusion proteins that do not contain a PHD domain, such as NUP98::NSD1 or NUP98::HOXA9? Please discuss this.

      We appreciate this important conceptual question. Many NUP98 fusions, despite diverse partner domains, produce similar transcriptional programs. Our current hypothesis is that the highly active status of the HOX cluster genes in HSPC attracts NUP98 oncofusions targeting H3K4me3 (e.g., KDM5A and PHF23), while NUP98::HOXA9 and other transcription factor fusions directly target the HOX cluster via DNA sequence recognition. This convergence and the broad targets of the dysregulated HOX transcription factors explain the transcriptional program similarity, sustained by the previously described enrichment of transcriptional co-activators by NUP98 oncofusion condensates. Of note, while several fusion partners of NUP98 lack PHD domains, the NUP98::NSD1 oncofusion includes several PHD domains of NSD1, which have previously been suggested to be important for leukemogenesis (PMID: 17589499). The discussion section has been modified to add:

      We envision that a similar mechanism targets other NUP98 fusions containing H3K4me3-recognizing reader domains (e.g., NUP98::PHF23) to leukemogenic loci, complementing direct targeting of the HOX genes through DNA sequence recognition in fusions containing DNA-binding domains (e.g., NUP98::HOXA9).

      Reviewer #2 (Public review):

      In this manuscript, the authors investigate how the oncogenic fusion protein NUP98KDM5Aalters gene expression in leukemia, using a combination of cellular experiments with model and patient cell lines, as well as in vitro studies. Upon transfection of U2OS cells with mEGFP-tagged NUP98-KDM5A, the authors show that the fusion proteins form sub-micrometre puncta, whereas KDM5A alone does not. These foci are also observed at expected native expression levels (using OpenCell data). The tag has an effect here, as switching to an mCherry tag raises the apparent saturation concentration for phase separation. Finally, the authors show via super-resolution imaging that the foci correlate with H3K4me3 distribution.

      In vitro, the fusion protein forms amorphous, gel-like condensates at double-digit nanomolar concentrations. Truncation analysis identifies PHD3 of KDM5A as required for maximal phase separation, consistent with the ability of the protein to bind H3K4me3 peptides. Addition of polynucleosomes increases the amount of fusion protein partitioning into the condensate in anH3K4me3-binding-dependent manner. Condensates are gel-like with slow internal dynamics in vitro; in cells, however, the dynamics depend on the position of the EGFP tag (no corresponding experiments with mCherry are shown). Reconstitution with H3K4me3- and H3K4me0-modifiedarrays shows colocalization with both wild-type NUP98-KDM5A and the binding mutant. Here, H3K4me3 arrays recruit ~20% more protein and yield gel-like structures in a manner dependent on the PTM and on the PHD finger.

      In cells, the fusion protein colocalizes with H3K4me3-marked loci, including the HOX clusters, as confirmed by FISH. Finally, re-analysis of published expression datasets from patient cells shows that genes are predominantly upregulated and that the upregulated genes are H3K4me3-marked.

      This is a well-executed mechanistic study. The data convincingly establish that NUP98KDM5A forms sub-micrometre foci at realistic expression levels, that these foci correlate with H3K4me3-marked sites, that the PHD3-H3K4me3 interaction mediates chromatin binding while the NUP98moiety drives phase separation in vitro, that foci in cells overlap genes heavily decorated with H3K4me3, and that H3K4me3-marked genes are those found to be upregulated in patient datasets. These are important mechanistic findings and of interest to the community.

      Still, the functional/causal link is a bit more tentative, as the data is mostly correlative, since it is not directly established that there is feedback between H3K4 methylation, NUP98KDM5Arecruitment, phase separation and target gene overexpression. An experiment that could further bolster this claim would be a direct test of whether NUP98-KDM5A expression drives overexpression of bound genes, e.g. expression of the fusion protein vs PHD- and NUP98-mutant variants, followed by qPCR of target genes, such as the HOX cluster, and possibly H3K4me3 ChIP at the same loci. As all the constructs and cell lines exist, this could be feasible and would substantially strengthen the manuscript.

      We thank the reviewer for the thoughtful evaluation and agree that the causal link betweenH3K4me3 recognition, condensate formation, and gene activation remains partly correlative. Experiments such as qPCR or ChIP following expression of WT versus mutant constructs would indeed strengthen the causal chain. However, performing these assays across multiple constructs and loci in a physiologically relevant system is not feasible within the current revision cycle. We have added text acknowledging this limitation and clarifying that our study focuses on establishing the biophysical mechanism of targeting, while functional consequences are inferred from patient datasets rather than new perturbation experiments.

      We modified the Study limitations section of the Discussion to add:

      Similarly, our study focuses on the biophysical mechanism of chromatin targeting by the NUP98::KDM5A oncofusion, with functional consequences inferred from patient-derived datasets rather than defined perturbation experiments.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      (1) Figure 1 - Figure Supplement 2: show co-localisation of large droplets of the chromatin-binding mutant with nucleoli by co-immunostainings, using nucleolar markers.

      (2) Figure 1E: Show another histone mark as a control, ideally H3K27me3.

      (3) The authors are encouraged to stick to the recommended nomenclature of fusion genes(https://www.nature.com/articles/s41375-021-01458-0).

      Reviewer #2 (Recommendations for the authors):

      (1) The phase-separation behaviour clearly depends on the fusion FP, as the switch from mEGFP to mCherry shifts the apparent saturation concentration to ~200 nM. The authors should discuss, and where possible test, how much of the observed behaviour is attributable to the FP itself: what happens in the absence of any FP, and which construct (mCherry- or mEGFP-tagged) the authors consider the better proxy for the untagged fusion protein.

      (2) This is particularly relevant given that the in-cell dynamics (FRAP) are reported to depend on the position of the EGFP tag, and no corresponding mCherry experiments are shown.

      (3) The authors claim a patient NUP98-KDM5A concentration of ~180 nM. This is based on data for NUP98 in HEK293 cells, with the added correction factor for having only one allele mutated in patients. Still, the direct jump from HEK293 to patient leukemia cells is big; so the authors should formulate this more carefully: no conc. determination was done directly in patients.

      (4) Chicken erythrocyte chromatin: What is the endogenous H3K4me3 level in the chicken erythrocyte chromatin used here?

      (5) Figure 1 - Figure Supplement 3B. The legend defines the square as the mean but does not explain the remaining symbols (vertical lines, horizontal lines, grey versus black dots). Please define these plot elements.

      (6) In the reconstitution experiments, the arrays and the condensates appear to colocalize only weakly, and, a bit counterintuitively, the strongest apparent colocalization is seen for the NUP98KDM5A binding mutant. Can the colocalization be quantified and interpreted?

      (7) Figure 2 - Figure Supplement 3. Raising the chromatin concentration from 12.5 to 100 nM produces little visible change in the images. Where does the additional chromatin go? Does it stay in solution? As in point 4, the best colocalization again appears to be obtained with the mutant, which is unexpected and a bit difficult to reconcile with the proposed H3K4me3-PHDdrivenrecruitment model.

      (8) That highly expressed genes in patients carry H3K4me3 is basically expected and is not by itself informative. The relevant question is the origin of the effect: is H3K4me3, and the associated upregulation, a consequence of NUP98-KDM5A condensate formation? Analyzing the direct effects of NUP98-KDM5A (and mutants) on specific target gene expression profiles could help to dissect this further.

      We thank the reviewers for these recommendations. We have made the following revisions to the manuscript:

      We replaced NUP98-KDM5A with NUP98::KDM5A, in accordance with the recommended nomenclature. We made this change in both the text and the figures. We also corrected other NUP98 on confusions to reflect this recommendation.

      We have revised Figure 1 – Figure Supplement 3B and the accompanying legend to describe the symbols used in this figure.

    1. Author response:

      I am writing to provide a description of our planned revisions. We thank the reviewers for their thoughtful comments on the manuscript. All three reviewers had the primary concern of “lack of saline-treated control.” We had, in fact, included saline-treated control in our design, and shown some of this data in the original submission (Supplemental data Fig 1G). We agree with the Editor’s note that more analysis for saline sessions should be provided. The planned revisions will include additional saline data to compare saline injections on behavior (as shown for psilocybin on figure 1), on reward-preferring and non-preferring cluster analysis (as shown for psilocybin on figure 3), and on action decoding and encoding (as shown for psilocybin on figure 6).

      It should be emphasized that the work involved outbred rats performing a complex probability-shifting decision-making task while freely moving in an operant box. Some of the comments by reviewer 1 (such as considering long/changing latencies to retrieve reward as “extraordinarily” or “abnormally” long) suggest that there may have been a mix-up with what is common in freely-moving rats versus simpler and head-fixed mouse paradigms. This distinction is relevant to some of the concerns raised by reviewer 1. First, our n is well within the range seen in electrophysiological studies in behaving rats as most these studies utilize n=5-9 (e.g., Sias et al., Nature Neuro, 2024; Maor et al., Nature Comm, 2026). Second, our analysis dealt with shifting latencies accordingly (e.g. time-locking to action) and focused on within subject performance because in complex cognitive tasks such as ours, there is a considerable amount of baseline performance variability in outbred rats. It is, therefore, common, and clinically relevant, to focus on within subject analysis of drug or vehicle effects. This has been the case with previous studies on the effect of psilocybin on cognitive flexibility (e.g. Torrado Pacheco et al, NPP 2023) and was our approach here. The additional saline data will hopefully convince the reviewers and interested readers that the reported effects of psilocybin were not an artifact of i.p. injections

    1. Author response:

      The following is the authors’ response to the original reviews.

      eLife Assessment:

      This study provides valuable insights into humans' ability to generalize knowledge of learned graph structures to new experiences that share the same structure but are built from different stimuli. However, the evidence for the authors' claims is incomplete, with the main claims of structural generalization and compositionality only partially supported by MEG and behavioral data. This study will be of interest to cognitive neuroscientists studying structure learning and generalization.

      We thank the editor and reviewers for a positive evaluation of our work and constructive suggestions to improve our manuscript.

      The reviewers' comments motivated textual modifications to the manuscript, changes and additions to figures and conduct of further analyses.

      We believe that the changes made in response to the reviewers' comments and suggestions provide for a substantially improved revised manuscript.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary of the paper:

      The paper presents an elegant task designed to investigate humans' ability to generalize knowledge of learned graph structures to new experiences that share the same structure but are built from different stimuli. Using behavior and MEG recordings, the authors test evidence for neural representation and application of structural knowledge.

      We appreciate this overall positive evaluation of our work and suggestions to strengthen the empirical support for the claims made in the paper.

      (1) While the task design is elegant, it isn't clear to me that the data support all the claims made in the paper. I have detailed my concerns below.

      The authors claim that their findings reveal "striking learning and generalization abilities based on factorization of complex experiences into underlying structural elements, parsing these into distinct sub processes derived from past experience, and forming a representation of the dynamical roles these features play within distinct subprocesses." And "neural dynamics that support compositional generalisation, consistent with a structural scaffolding mechanism that facilitates efficient adaption within new contexts".

      (a) First, terms used in these example quotes (but also throughout the paper) do not seem to be well supported by data or the task design. For example, terms such as 'compositional generalisation' and 'building blocks' have important relevance in other papers by (some of) the same authors (e.g., Schwartenbeck et al., 2023), but in the context of this experiment, what is 'composition'?

      We agree that our use of composition is less technical and formal than the nested and recursive forms of composition using “building blocks” reported in previous work (e.g., Schwartenbeck et al., 2023). In this experiment we study composition of smaller graphs via superimposition of their outputs. The superimposed “compound” outputs can be viewed as outputs of a single, more complex, graph. This is a special case of all possible ways that graphs can be composed from other graphs, and does not depend on a complex syntax for their combination (although more complex combination rules, other than multiplication are theoretically possible). Nevertheless, in accordance with common definitions of compositionality, this leads to a generative setup, given that a huge number of graphs can be expressed as the product of smaller graphs in this way.

      Figure panel (Fig 1A) illustrates this precise point. Importantly, we argue this kind of composition is ubiquitous in real-world learning scenarios where multiple independent processes contribute to the holistic experience of a situation.

      Based on the reviewer’s suggestion we have now amended the manuscript introduction to render the distinction between different definitions, and usage, of the term composition more salient.

      It is our understanding that this form of flexible, combinatorial, reuse of factorized prior knowledge is considered a specific instance of composition. Indeed, this understanding is supported by a cognitive-computational neuroscience literature that adheres to similar conceptualizations of compositionality, e.g., Barron et al., 2013 Nat Neuro; Rubino et al., 2023 PsyArxiv; Luettgau et al., 2024 PNAS.

      We add a paragraph to the introduction section elaborating on what we mean by graph factorization and its relevance for questions of compositional generalization (reproduced below for convenience).

      To address these questions, we developed a sequence learning paradigm based on a graph theoretical concept of graph factorization, emulating environments whose dynamics are the product of multiple simultaneous subprocesses. “Product graphs (Cartesian product), wherein the joint dynamics of two or more graph factors create complex product state space dynamics that can be factorized (and simplified) into constitutive factors, provides a compelling and flexible test bed for probing compositional generalization of multiple (independent) and simultaneously unfolding subprocesses.” Examples of such graph products and their factorizations, from a vast space of possible combinations, are provided in Figure 1A. Here we take inspiration from prior studies in neuroscience (e.g., Barron et al., 2013; Rubino et al., 2023; Schwartenbeck et al., 2023) and a prior cognitive literature, e.g., recursive operations over hierarchies (O’Donnell et al., 2009, 2011), hierarchical function composition, or rich forms of semantic composition in language to create complex concepts (Murphy, 1988).

      (2) Can the authors demonstrate clear behavioural or neural evidence for compositional use of multiple graph structures, or alternatively remove reference to these terms? In the current paper, it seems to me that the authors are investigating abstract knowledge for singular graph structures (together with the influence of prior learning), as opposed to knowledge for the compound, more complex graph formed from the product of two simpler graphs.

      We thank the reviewer for this important clarification, and agree our language should more precisely distinguish what the task design requires from what our data directly demonstrate. The reviewer is correct that our analyses primarily provide evidence for the abstraction and transfer of a single previously-experienced graph structure to novel stimuli, rather than direct evidence that participants combine two independently learned structures into a novel compound representation. We agree this distinction is important, and we have revised our language throughout the manuscript accordingly, reserving "compositional generalization" to describe the broader task structure (in which every compound stimulus is the joint product of two simultaneously evolving subprocesses, and the specific compound experienced during transfer learning was never observed during prior learning) and using more precise language: "decomposition," "abstraction," and "transfer" of single structural components to describe what our behavioral and neural evidence actually establishes. We have not claimed direct evidence that participants compositionally construct novel joint representations from two previously separate structures; rather, our evidence concerns the selective reuse of one such component when it recurs across learning phases, embedded in a novel pairing with another, entirely new structural component. We have adjusted the manuscript throughout and changed the title of the paper to “A neural mechanism for compositional structure transfer in humans”, to more adequately reflect the evidence presented.

      (3) While I would like to be convinced that this data provides evidence for the transfer of abstract, structural knowledge, I think the authors either need to provide more convincing evidence or tone down their claims.

      Can the increase in neural similarity between stimuli mapping to the same abstract structural sub-process not be explained by temporal proximity in experiencing the transitions (e.g., Cai et al., 2016)? Indeed, behavior seems to be dominated by direct experience of the structure as opposed to applying abstract knowledge of equivalent structures (and, as a result, there is little difference in behavioural performance between experience and inference probes).

      The reviewer makes an astute observation while providing a constructive challenge. We agree that distinguishing transfer of abstract structural knowledge from effects driven by direct temporal experience is critical, and we appreciate this opportunity to clarify our reasoning on this point.

      The reviewer suggests that increased neural similarity between stimuli that map to the same abstract structural sub-process might be explained by a temporal proximity in experience, as shown in prior work (e.g., Cai et al., 2016). We agree that temporal proximity is a potentially powerful determinant of representational similarity. Likewise, we do not dispute that temporal statistics of experience play an important role in shaping such neural representations. Nevertheless, we believe these accounts do not provide a sufficient explanation for our results, which we consider reflects a consequence of being exposed to the outputs produced by sequences drawn from an underlying graph structure and a prior learning of these sequences.

      In our task, the temporal statistics of stimulus experience are fully dictated by the transition structure of the graph. Different graph structures necessarily impose different constraints on temporal proximity (e.g., how many steps it takes to revisit a given node, which nodes are encountered at similar temporal distances, etc.). Thus, if stimuli that occupy equivalent structural roles across different graphs come to be represented more similarly, this is precisely because learners have abstracted over the specific transition structure that governs these temporal relationships. In other words, consistent with our previous computational findings that models based on temporal difference learning mechanisms account well for behavioural response patterns (Luettgau et al., 2024 PNAS), temporal proximity is not a confound but instead is a likely mechanism through which structural knowledge is acquired. Critically, our key claims concern transfer across learning contexts, and not sensitivity to temporal proximity within a single experience stream. By design, the selective learning improvements observed in each group during transfer cannot be explained by temporal proximity alone, because the relevant temporal statistics in the transfer phase are novel and differ across groups. The fact that prior learning selectively facilitates subsequent learning depending on an earlier experience of an abstract structure indicates participants are not simply tracking local temporal regularities, but instead are reusing previously learned structural knowledge to guide learning within a new context.

      We agree that behavior in our task is strongly influenced by direct experience, and we do not claim that participants rely exclusively on abstract structural knowledge. Indeed, the relatively small differences between experience and inference probes are consistent with the view that abstraction complements and facilitates, rather than replaces, learning from direct experience. Our claims are therefore deliberately modest: we argue for the transfer of abstract structural knowledge that shapes learning dynamics and neural representations, not for behavior dominated by explicit inference over abstract graphs.

      To avoid any criticism related to over-interpretation, we have toned down our language and clarify throughout introduction, results and discussion section of the manuscript that (i) temporal proximity is an intrinsic feature of graph structure, (ii) neural effects reflect (in part) abstraction over these structured temporal relationships, and (iii) that our results provide evidence for transfer of structural knowledge that biases learning, rather than for fully context-independent representations or strong behavioral generalization.

      (4) The strongest evidence for neural representation of abstract task structures seems to be the increase in similarity by transition type. But this common code for 'transition type' is only observed for 6-bridge graphs and only for experienced transitions. There was no significant effect in inference probes. Therefore, there doesn't seem to be evidence for the application of a knowledge scaffold to facilitate transfer learning. Instead, the data reflects learning from direct experience and not generalisation.

      We appreciate the reviewer's point, and agree it deserves a careful investigation. We carefully considered how this correlation could be interpreted under a non-transfer, pure direct-experience account. Our interpretation is that even if all graph learning relies entirely on direct experience, a correlation is still expected due to individual differences in learning ability. Under this framework, higher-ability participants are simply more likely to directly discover the same structural component (the 6-bridge) across both sessions (prior and transfer learning), which in turn supports higher MEG transition decodability. Concurrently, these same participants will exhibit higher behavioral accuracy due to their superior learning capacity. Importantly, under this account, these higher-ability participants should also show higher behavioural accuracy during the transfer phase for the 4-cycle component, predicting (a) a positive correlation between our transition decoding signal and 4-cycle behavioural accuracy, and (b) a positive correlation between 4-cycle and 6-bridge behavioural accuracy themselves, within each prior learning group.

      We tested both predictions directly. For (a), in the 6-bridge prior group, average decoding strength at timepoints showing a selective significant group difference correlated with experience probe performance on the 6-bridge graph during transfer learning (ρ = .48, p = .016, surviving correction for two comparisons, α = .025), but the corresponding correlation with 4-cycle behavioural accuracy did not reach significance (ρ = .38, p = .071). We acknowledge, however, that a direct comparison of these two dependent correlations (Steiger's test) did not reach significance (p = .66).

      For (b), we directly correlated 4-cycle and 6-bridge transfer accuracy within each prior learning group. For experience probes, this correlation was significant in the 4-cycle prior group (ρ = .51, p = .010) but not in the 6-bridge prior group (ρ = .24, p = .257); for inference probes, the pattern reversed, with a significant correlation in the 6-bridge prior group (ρ = .42, p = .035) but not the 4-cycle prior group (ρ = .16, p = .452). In neither probe type did a direct comparison of the two groups' correlation coefficients reach significance (experience probes: Z = -1.06, p = .291; inference probes: Z = .95, p = .340). Given that two of these four single-group correlations were nominally significant (without correction for multiple comparisons) while the corresponding between-group comparisons were not, and given the inconsistency in which group/probe-type combination shows the effect, we consider this pattern inconclusive rather than supportive of a clear general-ability signal linking performance on the two graph components.

      We therefore cannot statistically rule out the general-ability account with the current sample, and have revised our interpretation accordingly: rather than claiming strict specificity to the 6-bridge structure, we now describe the correlation as selective to 6-bridge experience probes in this sample, while acknowledging that distinguishing structural reuse from a more general learning ability to represent novel relational structure remains an open question. We have added the decoding-strength comparison as a new Supplementary Figure 5, showing decoding-strength correlations with both 4-state and 6-bridge graph performance side by side, and report the direct behavioural correlation between graph components in the text, and have revised the relevant main-text passage to match these updated values.

      We also wish to address why this correlation was selective to experience probes and did not extend to inference probes. We agree that, under an assumption of perfectly learned and context-independent abstract representations, one might expect performance on experience and inference probes to relate equally to the decoding signal. We believe the reviewer's concern is valid only under an assumption of perfect abstraction. In our task, abstract roles correspond to latent structural variables that are learned gradually and with uncertainty. Under such conditions, role inference is inherently context-dependent: the role of a given stimulus is not inferred in isolation, but in relation to the compound within which it appears. For example, if one element of a compound is already known with high confidence to belong to a particular subgraph, the role of the second element can be inferred more reliably; in contrast, when both elements are themselves uncertain, role inference becomes less precise. Critically, learning is unlikely to be uniform across compounds, as structural knowledge may be acquired with variable precision for different stimulus pairings depending on their frequency, co-occurrence statistics, and position within a sequence. This variability in learning precision means we would expect corresponding variability in a participant's ability to infer dynamical roles across different compound types, and consequently in their ability to make accurate predictions about those compounds. Under this account, our MEG signal, which indexes role-based representational structure specifically for experienced compounds, most directly reflects knowledge precision for those items; a correlation with inference probe accuracy requires an additional inferential step from experienced to novel compounds, introducing noise proportional to uncertainty in the underlying learned representations. We have revised the Discussion to make this reasoning more explicit.

      (5) The authors frequently suggest that they are providing insight into temporal dynamics, but there is no mention of particular oscillations or particular temporal sequences of neural representation that support task performance.

      We thank the reviewer for highlighting this. We agree our use of the term "temporal dynamics" is potentially misleading, and we have now revised the manuscript accordingly. Our analyses did set out to identify specific neural oscillations, rhythmic processes, or temporally ordered stages of computation that support task performance. Rather, time-resolved MEG analyses is a method that allows us to track when representational content is expressed during stimulus processing, serving three research questions about subprocess-specific representational similarity, dynamical role representations, and relationship to behavioral transfer performance; as opposed to characterizing the temporal organization of underlying computations per se.

      We have now removed or replaced references to "temporal dynamics" and "neural dynamics" throughout the manuscript where these might be interpreted as claims about oscillatory or sequentially structured neural mechanisms. Instead, we now frame our conclusions in terms of representational content and its modulation by prior learning experience. We believe this aligns our language with what the data actually support and removes potential confusion regarding the scope of our claims.

      (6) Regardless of point (b), can the authors provide more convincing evidence for a graph structure being represented per se (regardless of whether this representation is directly experienced or inferred)? From Figure 3C, it seems that the model RDM doesn't account for relative distance within the graph. Do they see evidence for distance coding? Can they reconstruct the graph from representational patterns using MDS?

      We thank the reviewer for raising this point. The reviewer is correct that the model RDM shown in (previous) Figure 3C does not specifically capture relative distance within the graph and asks whether there is evidence for distance coding or whether the graph can be reconstructed using techniques such as MDS. We agree that distance-based representations are one possible signature of graph knowledge, with such effects reported in a prior literature. However, our theoretical focus is on an investigation of a more functionally relevant aspect of graph structure learning and reuse of abstracted knowledge: the representation of graph nodes according to their structural roles or positions within a graph.

      To address the question more directly, we ran an additional sensor-level RSA analysis using the localizer task data, comparing representational changes from PRE to POST learning. Specifically, we examined whether stimuli in the 6-bridge graph that map onto the same structural roles (e.g., boundary, intermediate, central) within the relevant graph structures show greater neural similarity from before to after learning, and whether this effect depends on the graph structure experienced during prior learning. This new analysis revealed a cluster-based, permutation-corrected, interaction effect between prior learning group and graph factor, consistent with a representational similarity increase selectively for stimuli sharing the same structural role in a graph structure relevant to each group’s prior experience. Importantly, this effect occurs at similar time points as our earlier RSA effects based on overall stimulus-set similarity, suggesting that both analyses capture related aspects of the same underlying representational processes.

      We believe this role-based representational similarity provides more direct evidence for graph-structured representations and their transfer across learning than distance-based or MDS reconstructions in our task context. First, distance within the graph is necessarily correlated with temporal proximity of experience, making it difficult to disentangle distance coding from local transition statistics. Second, multiple distinct graph structures used in our experiment (e.g., cycles, lines, and bridges) share overlapping distance relationships but differ in their higher-order structural roles. Our analysis therefore targets those aspects of structure that are invariant across surface features and that are most relevant for transfer across learning contexts.

      For these reasons, while we do not claim we can reconstruct full graph geometry from neural patterns, our results are consistent with an organization of neural representations according to abstract structural positions within a graph, that is independent of specific stimulus identities. We have added a new panel to Figure 3 illustrating this role-based RSA effect and also expanded the Methods and Results sections to describe this analysis in detail. We believe this addition provides more convincing evidence that participants represent graph structure at an abstract level, even when that structure is not explicitly experienced in the same form during the localiser task. We thank the reviewer for encouraging this more specific analysis, as it significantly strengthens our claims.

      “To test whether localiser representations of abstract graph structure generalised across sets experienced in the main task, we performed RSA separately for PRE and POST localisers. Structural roles were derived from each participant’s learning-phase transition sequences. For 4-state graphs, nodes were assigned to two matched role bins (boundary-like vs central-like) based on first-encounter order within each phase. For 6-state graphs, roles were determined either from node degree (6-line: boundary, intermediate, central). For 6-bridge graphs we used a predefined structural template. Specifically, the first eight valid transitions in the learning phase were mapped onto a fixed sequence of structural roles (central–intermediate–boundary–central–central–intermediate–boundary–central). Each node was assigned a role based on the majority role it occupied across its occurrences in these eight steps (ties resolved in favour of central > intermediate > boundary). For the localiser data, at each time point and sensor we estimated condition-specific activations using a GLM with 20 dummy-coded regressors (10 identities × 2 sets). This yielded sensor-wise beta patterns for each condition. Cross-set representational dissimilarities were computed using an L1 distance metric (mean absolute difference across sensors), resulting in 4×4 and 6×6 cross-set RDMs at each time point. We then summarised each RDM according to structural role: within-role distances (same role across sets), between-role distances (different roles), and their difference (delta = between − within). To control for unequal pair counts, between-role comparisons were subsampled to match the number of within-role pairs (200 repetitions). This produced time-resolved structural generalisation indices for 4-state and 6-state graphs, which were submitted to group-level statistical analyses as described above.”

      (7) In general, the figures are not very clear, and the outcome from statistical tests is not graphically shown. The paper would be easier to digest if, for example, Figures 1-2 were made clearer and statistical significance relative to chance were indicated throughout. To give two examples: (i) Figure 1 should clearly indicate what is meant by observed and held-out transitions and whether it is just the transition or also the compound that is new to the participant. (ii) Figure 2D-E could be shown with relevant comparisons and simpler statistical comparisons. Currently, it is hard to follow without carefully reading the legend.

      We have taken the reviewer’s point on board and have revised the figures to improve clarity. Specifically, we have improved labeling and visual annotation in Figure 1 to clearly distinguish observed versus held-out transitions and to highlight the key experimental manipulations. We have also simplified the presentation of behavioral results in Figure 2D–E and made the most relevant statistical comparisons more explicit, with statistical outcomes now indicated directly in the figures where appropriate.

      We believe these changes improve readability and reduce the burden on the reader, while still relying on the figure captions to convey essential methodological details and interpretation, following standard practice. See Figure 1 and Figure 2.

      Reviewer #1 (Recommendations for the authors):

      (1) For the classifier: what was the overall accuracy of the classifier when tested on held-out examples of the same stimuli? Relative to chance? Relative to entirely different stimuli that have the same transition type (e.g., line 424)?

      (2) In the Results paragraph 2 can you state how many subjects had prior exposure to 4-state vs how many had prior exposure to 6-state?

      This has now been added these data to the results section, reproduced below for convenience:

      In brief, participants “(N = 50, N = 25 subjects per condition)” performed a sequence learning task, observing image sequences produced by walks on product graphs constructed from smaller graph factors (Fig. 1A and B).

      Reviewer #2 (Public review):

      Summary:

      The authors aimed to investigate the temporal dynamics of how prior experiences shape learning in new complex environments by examining whether the brain reuses abstract structural components from those experiences. They employed a sequence learning task based on graph factorization and recorded neural activity using magnetoencephalography (MEG) to investigate how the underlying graph factors are reused to support learning and inference in a new graph. MEG data was derived from passive stimulus presentation trials, and behavior was assessed through a small number of probe trials testing either experienced or inferred successions in the graph. Representational similarity analysis of the MEG data was performed at a quite aggregated level (the principal components explaining 80% of the variance). The authors report (1) enhanced neural similarity among stimuli that belong to the same graph-factor as well as (2) a correlation between abstract role representations, corresponding to particular positions in the graph, and performance in experience-probes but not in inference-probes.

      Overall, the findings are congruent with prior research on neural correlates of structural abstraction. They offer an elegant, well-suited task design to study compositional representations, replicating the authors' earlier finding and providing temporal information on structural generalisation in a sequence learning task.

      We thank the reviewer for this positive evaluation of our work and insightful comments and suggestions.

      (1) The first finding is considered evidence for representational alignment of the graph factors. However, alignment seems to be just one possible arrangement underlying the increased similarity between stimuli of the same vs different graph factors. For instance, a simple categorical grouping of stimuli belonging to the same graph, rather than their structural alignment, could also underlie the reported effect. The wording should be adjusted to avoid over interpretation.

      We agree with the reviewer that increased neural similarity between stimuli associated with the same graph factor does not uniquely imply representational alignment in its strongest sense, and could in principle also reflect a more general categorical grouping of stimuli based solely on belonging to the same graph. We revised the manuscript to tone down the wording and avoid overinterpretation, replacing references to “representational alignment” with more neutral language that refers to increased within-factor representational similarity.

      At the same time, we believe that additional analyses introduced in the revised manuscript constrain alternative accounts. In particular, our new analysis on localiser data, examining representational changes from PRE to POST learning for stimuli that map onto the same structural roles within relevant sub-process graph structures. This analysis showed the presence of a cluster-based, permutation-corrected, interaction effect between group and graph factor, indicating that representational similarity increases selectively for stimuli sharing the same structural role, rather than simply increased similarity for all stimuli associated with the same graph.

      Because these role-based groupings cut across specific stimulus identities and cannot be reduced to a single categorical label for an entire graph, we believe this result provides specific evidence that neural representations are shaped by internal structural properties of the graph, rather than reflecting the emergence of a coarse categorical distinction between graph types. We have added this analysis as a new panel to Figure 3 and expanded the Results and Methods sections accordingly (reproduced below for convenience):

      “The observed increase in neural similarity between stimuli associated with the same graph factor could, in principle, reflect a more general categorical grouping of stimuli belonging to the same graph factor, rather than reflecting an abstract graph representation. To address this alternative account, we examined whether neural similarity in the localizer task is specifically structured according to the graph-theoretic role each stimulus occupies within its graph, using a finer-grained theoretical RDM that distinguishes between boundary, intermediate, and central positions. Structural roles were derived from each participant's learning task sequences and defined by graph topology. For Component 6, roles were assigned using a bridge-graph traversal template (for Condition 6, whose prior learning involved the bridge graph) or degree-based assignment (for Condition 4, whose prior learning involved a line graph): boundary nodes were defined as nodes with degree 1 (graph periphery); intermediate nodes as neighbours of boundary nodes; and central nodes as the remaining, more densely connected nodes. For Component 4, two roles were distinguished, boundary-like nodes (those encountered first and last in the sequence traversal) and central-like nodes (those encountered second and third), reflecting structural position within the graph rather than arbitrary temporal sequence. For further details of role assignment, see Methods. This analysis revealed a cluster-based permutation-corrected interaction (P<sub>FEW</sub> < 0.05, non-parametric permutation test, Figure 3E) between prior learning group and graph factor at overlapping time windows with the previously reported PCA and sensor-level analyses investigating feature-mappings to abstract graph factors. We did not observe significant and multiple comparisons corrected prior learning group and graph factor main effects (all P<sub>FEW</sub> > 0.90, non-parametric permutation test). These results indicate that representational similarity increased selectively for stimuli sharing the same structural role in the graph structure relevant to each group’s prior experience. Critically, this effect was not observed uniformly for all stimuli associated with the same graph, arguing against a purely categorical grouping explanation. Instead, these findings provide evidence that learning induces representations that reflect higher-order relational structure, capturing graph-theoretic roles that are invariant across surface features of the embedding stimuli and support transfer across learning contexts.

      Taken together, our findings indicate a task-induced, learning-related increase in neural similarity for stimuli sharing a structural role in subprocesses common across task phases and is compatible with a structural scaffolding mechanism, though we do not claim these representations are fully context-independent.

      “To test whether localizer representations of abstract graph structure generalised across sets experienced in the main task, we performed RSA separately for PRE and POST localisers. Structural roles were derived from each participant’s learning-phase transition sequences. For 4-state graphs, nodes were assigned to two matched role bins (boundary-like vs central-like) based on first-encounter order within each phase. For 6-state graphs, roles were determined either from node degree (6-line: boundary, intermediate, central). For 6-bridge graphs we used a predefined structural template. Specifically, the first eight valid transitions in the learning phase were mapped onto a fixed sequence of structural roles (central–intermediate–boundary–central–central–intermediate–boundary–central). Each node was assigned a role based on the majority role it occupied across its occurrences in these eight steps (ties resolved in favour of central > intermediate > boundary). For the localiser data, at each time point and sensor we estimated condition-specific activations using a GLM with 20 dummy-coded regressors (10 identities × 2 sets). This yielded sensor-wise beta patterns for each condition. Cross-set representational dissimilarities were computed using an L1 distance metric (mean absolute difference across sensors), resulting in 4×4 and 6×6 cross-set RDMs at each time point. We then summarised each RDM according to structural role: within-role distances (same role across sets), between-role distances (different roles), and their difference (delta = between − within). To control for unequal pair counts, between-role comparisons were subsampled to match the number of within-role pairs (200 repetitions). This produced time-resolved structural generalisation indices for 4-state and 6-state graphs, which were submitted to group-level statistical analyses as described above.”

      (2) The second finding of abstract role representations is indeed expected for structural generalisation. While the data presents an interesting indication, its interpretability is constrained by a lack of testing for generalization of the effect to other graph structures (e.g., to rule out graph-specific strategies) as well as the absence of a link to transfer performance in inference-probes. The authors argue that the experienced transitions the classifier was trained on might be more similar in process to the experience-probes than the inference-probes. However, as inference-probes are the key measure of transfer, one could argue that if abstract role representations truly underlie transfer learning, they should be evident in the common neural signal.

      The reviewer provides a thoughtful comment and we agree that, under an assumption of perfectly learned and context-independent abstract representations, one might expect this would be related equally to performance in experience and inference probes. Below, we clarify the scope of our claims, including presenting additional neural evidence for abstract role representations, and argue that an absence of a strong neural-behavioral correlation for inference probes is not inconsistent with our proposed abstract structural knowledge account of transfer learning.

      First, we acknowledge that our experiment tests generalization only across two graph families, rather than across a broader set of graph structures. While we think it unlikely that our findings are idiosyncratic to cycles or bridge-like graphs, a we now limit our claims and emphasise a future need for testing generalization across additional graph families (see discussion section as reproduced below)

      “We concede that the present experiment examines generalization across two families of graph structures, rather than across a broader space of possible graphs. While we consider it unlikely that our findings are idiosyncratic to cycles, lines and bridge-like graphs, we acknowledge that further work will be needed to support abstraction beyond the limited graph structures studied here.”

      Second, to provide more direct neural evidence that abstract structural roles within the studied graphs are represented per se, we add a new analysis that uses independent localizer task data. In this analysis, we performed a sensor-level RSA contrasting pre- and post-learning representations. Specifically, we test whether stimuli that occupied the same role within learned graph substructures became more neurally similar after learning. This localizer RSA revealed a cluster-corrected interaction effect between prior learning group and graph factor, expressed in an increased representational similarity for stimuli mapping onto equivalent structural roles, independent of specific stimulus identities and outside the task context of the main learning phase. This result supports the proposal that participants form abstract, role-based, representations of graph structure where these representations are not tied to a particular transition sequence or probe type. This finding adds an important insight in that it goes beyond establishing role representations for the 6-bridge graph factor, enabling us to make claims about generalization of structural knowledge of the 4-cycle graph factor in the 4-cycle prior condition (thereby to some extent showing a wider generalization across more structural forms).

      “To test whether localizer representations of abstract graph structure generalised across sets experienced in the main task, we performed RSA separately for PRE and POST localisers. Structural roles were derived from each participant’s learning-phase transition sequences. For 4-state graphs, nodes were assigned to two matched role bins (boundary-like vs central-like) based on first-encounter order within each phase. For 6-state graphs, roles were determined either from node degree (6-line: boundary, intermediate, central). For 6-bridge graphs we used a predefined structural template. Specifically, the first eight valid transitions in the learning phase were mapped onto a fixed sequence of structural roles (central–intermediate–boundary–central–central–intermediate–boundary–central). Each node was assigned a role based on the majority role it occupied across its occurrences in these eight steps (ties resolved in favour of central > intermediate > boundary). For the localiser data, at each time point and sensor we estimated condition-specific activations using a GLM with 20 dummy-coded regressors (10 identities × 2 sets). This yielded sensor-wise beta patterns for each condition. Cross-set representational dissimilarities were computed using an L1 distance metric (mean absolute difference across sensors), resulting in 4×4 and 6×6 cross-set RDMs at each time point. We then summarised each RDM according to structural role: within-role distances (same role across sets), between-role distances (different roles), and their difference (delta = between − within). To control for unequal pair counts, between-role comparisons were subsampled to match the number of within-role pairs (200 repetitions). This produced time-resolved structural generalisation indices for 4-state and 6-state graphs, which were submitted to group-level statistical analyses as described above.”

      Third, in relation to the relationship between neural role representations and transfer performance during inference probes, we believe the reviewer's concern is valid only under an assumption of perfect abstraction. In our task, abstract roles correspond to latent structural variables that are learned gradually, and with uncertainty. Under such conditions, role inference is inherently context-dependent: the role of a given stimulus is not inferred in isolation, but in relation to the compound within which it appears. For example, if one element of a compound is already known with high confidence to belong to a particular subgraph, the role of the second element can be inferred more reliably. In contrast, when both elements are themselves uncertain, role inference becomes less precise. Critically, learning is unlikely to be uniform across compounds, as structural knowledge may be acquired with variable precision for different stimulus pairings depending on their frequency, co-occurrence statistics, and position within a sequence. This variability in learning precision means we would expect corresponding variability in a participant's ability to infer dynamical roles across different compound types, and consequently in their ability to make accurate predictions about those compounds.

      Our MEG signal indexes role-based representational structure specifically for experienced compounds, and most directly reflects the precision of structural knowledge for those items. Therefore a correlation between a MEG signal and accuracy on inference probes is expected to be weaker, since it requires an additional inferential step from experienced to novel compounds, a step that is likely to introduce additional noise proportional to the uncertainty in the learned representations. Ideally we would expect such a correlation to be present for inference probes as well, since better structural knowledge about experienced compounds should in principle support better generalisation to novel ones. However, we consider we are insufficiently powered to detect this weaker relationship and interpret an absence of a significant correlation for inference probes as not inconsistent with a structural scaffolding account.

      Finally, we emphasize that the absence of a strong correlation between aggregate neural decoding measures and aggregate inference-probe performance should not be taken as evidence against abstract learning. Inference performance is likely to be supported by multiple sources of information (including partial structural knowledge and heuristic strategies), whereas neural decoding captures the stability of representational geometry at a population level. The newly added localizer RSA results demonstrate that abstract role representations are present in the neural signal, while at the same time their task-dependent expression may not always be directly mirrored at the level of inference-probe behavior.

      We have an added a paragraph caveating our findings to the discussion section (reproduced below for convenience):

      “Addressing our third research question, whether the strength of identified neural representations relate to behavioral transfer, we found a positive relationship between decoding strength and experience probe performance that was numerically larger for the structurally relevant (6-bridge) graph than for the irrelevant (4-cycle) graph, though this difference did not reach significance; no corresponding relationship was evident for inference probes.” Thus, a behavioral accuracy group difference in predicting successive states for the 6-bridge inference probe performance was of negligible magnitude and did not align with the robust effect observed for experience probes (Fig. 2D), where the latter replicates and extends a previous finding using a 6-state cycle graph and predicted by computational simulations using successor feature models (Luettgau et al., 2024). We speculate that the disparity between probe types is likely due to experience probes and inference probes engaging dissociable cognitive processes – the former relying on predictive representations acquired from experience, the latter relying on an ability to perform mental operations on learned representations of independent feature transitions. This may increase the likelihood of errors due to complexities of the inferred state spaces. However, the observed differences could also relate to previously reported effects of explicit knowledge on performance levels (Luettgau et al., 2024) or be driven by capacity limitations in working memory taxing larger subprocesses more strongly (Collins et al., 2017; Collins & Frank, 2012). “It is also likely that structural knowledge is not acquired uniformly across compounds. Because abstract roles are learned gradually and with uncertainty, role inference is inherently context-dependent: the role of a given stimulus is not inferred in isolation, but in relation to the compound within which it appears. When one element of a compound is already known with high confidence, the role of the second element can be inferred more reliably; when both elements are themselves uncertain, inference becomes less precise. Learning precision may therefore vary across stimulus pairings depending on their frequency, co-occurrence statistics, and position within a sequence, and we would expect corresponding variability in participants' ability to infer dynamical roles, and hence to predict outcomes, across different compound types. This means that an MEG signal, which indexes role-based representational structure specifically for experienced compounds, most directly reflects knowledge precision for those items. A correlation with inference-probe accuracy requires an additional inferential step, from experienced to novel compounds, introducing noise proportional to the uncertainty in the learned representations. In principle, better structural knowledge about experienced compounds should support better generalisation to novel ones, but we might be insufficiently powered to detect this weaker relationship. We therefore interpret an absence of a significant correlation for inference probes not as inconsistent with a structural scaffolding account, and suggest that a null result here should be interpreted with caution rather than as evidence against it. More broadly, an absence of a strong correlation between aggregate neural decoding measures and aggregate inference-probe performance should not itself be taken as evidence against abstract learning. Inference performance is likely supported by multiple sources of information, including partial structural knowledge and heuristic strategies, whereas neural decoding captures the stability of representational geometry at the population level. The localizer RSA results reported above demonstrate that abstract role representations are present in the neural signal, even though their task-dependent expression may not always be directly mirrored in inference-probe behavior.”

      (3) The authors write, "we observed a qualitative pattern indicative of increased neural similarity between stimuli that adhered to the same underlying subprocess across task phases. (...) There was a statistically significant interaction effect of condition x graph factor spanning approximately 300 - 680 ms post-stimulus onset". I conclude there was no significant main effect of graph factor, but the relevant statistics are not reported. The authors should report and discuss the complete statistics.

      Thank you for this comment. The reviewer is correct in their conclusion that the main effects were not significant and we agree the main effect of graph factor and group (as well as their significance) should be reported. We now do so in the figure caption of Figure 3D, as well as in the results section. The section reads as follows:

      We did not observe prior learning group and graph factor main effects (all PFWE > 0.118, non-parametric permutation test).

      (4) The RSA is performed on highly aggregated data (the PCs that explained 80% of the variance). Could the authors include their rationale for this choice (e.g. over-analysis of sensor-level data)? In case sensor-level analyses have been conducted as well, maybe there are comparisons or implications of the chosen approach that are useful to mention in the discussion. The authors should provide the average and distribution of the number of PCs underlying their analyses.

      We thank the reviewer for raising this important methodological concern. We agree that the use of PCA-based dimensionality reduction in RSA requires further justification. Our primary motivation for using PCA, and retaining components that jointly explain 80% of the variance, was based on denoising rather than aggregation per se. Sensor-level MEG data are high-dimensional and highly correlated, and representational analyses that operate directly on the full sensor space may be susceptible to noise amplification and overfitting, particularly when estimating distance measures across time. Retaining components up to a fixed variance threshold is a widely used approach in MEG decoding and RSA to preserve the dominant signal structure while attenuating sensor-specific noise. Importantly, this procedure discards only the lowest-variance 20% of the signal and on this basis does not impose strong constraints on the representational geometry.

      To address the reviewer’s concern more directly, and to ensure our findings are not driven by the PCA procedure itself, we conducted additional robustness checks. Specifically, we performed sensor-level RSA analyses without PCA, using multiple distance metrics (including L1 and L2 distances). These sensor-level analyses yielded highly similar temporal profiles and statistical effects to the PCA-based results, including for the key contrasts reported in the main text. We now include these results in a new supplementary figure and reference them explicitly in the Results section.

      In the revised manuscript, we clarify that PCA was used as a principled denoising step, not as a means of imposing structure on the data, and we explicitly show that our conclusions are robust across analytic choices.

      “Importantly, to verify that the chosen PCA approach did not impose artificial structure within the data, or introduce other potential confounds, we also conducted the above analyses on sensor level MEG data. Highly similar results were obtained, with consistent results for different similarity metrics (absolute distance (L1 norm) and Euclidean distance (L2 norm), Supplementary Figure 3)), demonstrating that our results and conclusions are robust across analytic choices.”

      Methods

      “In addition to the PCA-based feature analysis, we performed a sensor-level RSA. At each time point, we estimated condition-specific activation patterns using a GLM applied separately to each sensor (dummy-coded stimulus identity). RDMs were then computed across stimuli using mean absolute difference (L1 norm) as the primary distance metric. For completeness, we additionally evaluated Euclidean distances (L2 norm), which yielded qualitatively similar results (Supplementary Figure 3).”

      (5) While the paper is well-written overall, it would benefit from more explicitly identifying the concrete research question and advancing through the results. The authors state their aim as understanding the "temporal dynamics of compositional generalisation", revealing "at which moment during neural information processing are they assembled". They conclude with "providing evidence for temporally resolved neural dynamics that support compositional generalization" and "we show the neural dynamics (...) presented across different task phases...". It remains somewhat vague what specific insight about the process is provided through the temporal resolution (e.g., is the time window itself meaningful, if so, it should be contextualized; is the temporal resolution critical to dissociate subprocesses). The different task phases -initial learning and transfer- are the necessary conditions to investigate transfer learning, but do not by themselves offer a particularly resolved depiction of the process.

      We thank the reviewer for these thoughtful and constructive comments. We agree that in the original version of the manuscript our framing did not sufficiently specify the concrete insight that might be gained from neural data, nor did it clearly delimit the scope of our claims. Our primary research question did not relate to characterizing fine-grained temporal mechanisms or sequential subprocesses underlying compositional generalization (e.g., oscillatory dynamics, replay, or temporally ordered stages of computation). Rather, our goal is to determine whether abstract compositional structural representations are detectable neurally during stimulus processing, and how these representations are shaped by prior learning experience.

      We address three specific research questions: whether subprocess-specific representational similarity emerges following learning that is specific to a subprocess experienced during prior learning; whether fine-grained dynamical role representations are acquired during stimulus processing; and whether their strength relates to a behavioral transfer success. Importantly, the time-resolved nature of the analyses is a feature of the method that allows us to track the expression of representational content at a sub-trial timescale, rather than an end in itself. We agree with the reviewer that the temporal resolution does not, in itself, resolve distinct computational subprocesses, nor does it provide a mechanistic decomposition of compositional operations. Accordingly, we have revised the manuscript to more explicitly articulate these three concrete research questions in the Introduction, as well as clarify that the reported time windows should be interpreted as markers of representational availability rather than discrete processing stages. We also tone down any language that might be interpreted as making claims about temporally structured mechanisms. Finally, we agree that the distinction between task phases (prior learning vs. transfer) is not intended to depict a detailed temporal process, but rather to provide the necessary contrast to test whether neural representations reflect abstract structural knowledge that goes beyond direct experience. We have revised the Results and Discussion to make this logic more explicit and to better guide the reader through how each analysis contributes to addressing the three research questions.

      We believe these revisions better align our claims with the level of insight the data support and make the contribution of each analysis more legible to the reader.

      Reviewer #2 (Recommendations for the authors):

      (1) Could the authors explain in the manuscript how the held-out transitions were chosen?

      We agree that the stimulus construction and sequence generation logic were not described with sufficient clarity. In the revised manuscript we add an explicit description of how compound images were constructed from two independently varying visual features, each corresponding to one graph factor, and introduced the distinction between directly experienced, implied-but-unobserved, and never-valid transitions earlier in the text, so that the probe logic is easier to follow from the outset.

      We reproduce parts of the revised methods section describing the held-out stimulus set below:

      “[...] Because sequences were drawn from a subset of the product graph, only a portion of all 24 possible compound images (and their transitions) were encountered directly. Transitions between compound images could thus be: (i) directly experienced in a sequence, (ii) never presented in a sequence but implied by the factorization structure, or (iii) transitions between compound images from different subgraphs, which were never valid. The held-out set of transitions described in (ii) and (iii) between compound stimuli (partially observed during sequence presentations, partially never observed during sequence presentations) provided a context for assessing knowledge of graph factorization.”

      (2) It might be easier to follow the results section (without going back to Figure 1) if the mentioning of specific graph factors (6-bridge, 4 cycle) would occasionally be accompanied by their function/condition in the experiment.

      Thanks for this suggestion, we have implemented this in the manuscript.

      Reviewer #3 (Public review):

      Summary:

      This study investigates how task components can be learned and transferred across different task contexts. The authors designed two consecutive sequence learning tasks, in which complex image sequences were generated from the combination of two graph-based structural "building blocks". One of these components was shared between the prior and transfer task environments, allowing the authors to test compositional transfer. Behavioral analyses using generalized linear models (GLMs) assessed participants' sensitivity to the underlying structure. MEG data were recorded and analyzed using classifications and feature representational similarity analysis (RSA) to examine whether neural similarity increased for stimuli sharing the same relational structure. The paper aims to uncover the neural dynamics that support compositional transfer during learning.

      I found the methods and task design of this paper difficult to follow, particularly the way stimuli were constructed and how the experimental sequences were generated from the graph structures. These aspects would be hard to replicate without some clarification. I appreciate the integration of behavioral and neuroimaging data. The overall approach, especially the use of compositional graph structures in sequence learning, is interesting and could be used and revised in further studies in compositionality and transfer learning. I appreciated the authors' careful interpretation of their findings in the discussion. However, I would have liked a similar level of caution in the abstract, which currently overstates some claims.

      We thank the reviewer for a positive evaluation coupled with helpful suggestions to improve the clarity of our presentation. We are particularly pleased the reviewer found the integration of behavioral and neuroimaging data, the compositional graph structure approach, and our interpretation of findings in the discussion to be particular strengths of the manuscript.

      We address the two specific concerns raised below.

      We agree that the stimulus construction and sequence generation logic were not described with sufficient clarity. In the revised manuscript we have: (i) added an explicit description of how compound images were constructed from two independently varying visual features, each corresponding to a single graph factor; (ii) defined the Cartesian product graph operationally, clarifying also that transitions between compound images are valid when one factor changes state while the other remains fixed; (iii) included a worked example tracing a sample sequence through both factors; and (iv) introduced the distinction between directly experienced, implied-but-unobserved, and never-valid transitions earlier in the text, so that the probe logic is easier to follow from the outset.

      We reproduce parts of the revised methods section describing stimulus construction below:

      “Compound images were constructed by overlaying two independently varying visual features drawn from separate feature sets. Each feature set corresponded to a single graph factor, such that the state of each graph factor independently determines one feature of the compound image. For example, a compound image in state (A, 3) would display feature A from the cyclic factor and feature 3 from the path factor, superimposed or juxtaposed into a single image.

      The set of all compound images and their transitions was defined by the Cartesian product of two graph factors: transitions between compound images were valid if, and only if, one factor alone changed state according to its own transition rules while the other factor remained fixed.

      Observed sequences of image compositions composed from 10 individual features. Each sequence consisted of 8 compound images with 12 compound images in total across sequences.

      [...] For instance, in condition 1, a valid sequence might proceed: (A,1) → (A,2) → (A,3) → (B,3) → (C,3) → (C,4) → (D,4) → (D,5), where each step reflects a transition in either the cyclic (letter) or path (number) factor, but never both simultaneously.

      [...] Because sequences were drawn from a subset of the product graph, only a portion of all 24 possible compound images (and their transitions) were encountered directly. Transitions between compound images could thus be: (i) directly experienced in a sequence, (ii) never presented in a sequence but implied by the factorization structure, or (iii) transitions between compound images from different subgraphs, which were never valid. The held-out set of transitions described in (ii) and (iii) between compound stimuli (partially observed during sequence presentations, partially never observed during sequence presentations) provided a context for assessing knowledge of graph factorization.”

      We thank the reviewer for flagging the mismatch between the strength of interpretations made in the abstract and discussion section. We have revised the abstract to bring the language in line with the level of caution exercised in the discussion, avoiding overstated interpretations of the findings.

      The revised abstract is reproduced below:

      “A human ability to adapt to the dynamics of novel environments relies on abstracting and generalizing from past experiences. Previous research has focused on how humans generalize from isolated sequential processes, yet we know little about mechanisms that enable adaptation to more complex dynamics, including those that govern much everyday experience. Here, using a novel sequence learning task based on graph factorization, coupled with simultaneous magnetoencephalography (MEG) recordings, we ask whether reuse of experiential "building blocks" enable inference and generalization. Behavioral results were consistent with participants decomposing task experience into sub processes, abstracting their dynamical structure away from their sensory specifics and transferring these to a new task environment. Neurally, this transfer was associated with a learning-induced, condition-specific, increase in neural similarity among stimuli conditional on their structural role in abstract sub processes that were shared across task phases. Consistent with this, a complementary dynamical role decoding analysis revealed enhanced neural decodability for stimuli sharing identical structural transition types across experiential contexts, specifically when prior experience included the relevant graph structure. Decoding strength for these role representations was positively related to behavioral success in sub process knowledge transfer, a relationship that will require future independent replication. These findings provide neural evidence consistent with the idea that a structural scaffolding mechanism supports generalization of experience to new contexts.”

      (1) While the introduction mentions brain areas implicated in the low-dimensional representation of task knowledge, the current study uses M/EEG and does not include source reconstruction. As a result, the focus is primarily on the temporal dynamics of the signal rather than its spatial origins. Although I am not suggesting that the authors should perform source reconstruction in this study, it would strengthen the paper to introduce the broader M/EEG literature on task-relevant representations and transfer. The same applies to behavioral studies looking at structural similarities and transfer learning. I encourage the authors to integrate relevant literature to better contextualize their results.

      Duan, Y., Zhan, J., Gross, J., Ince, R. A. & Schyns, P. G. Pre-frontal cortex guides dimension-reducing transformations in the occipito-ventral pathway for categorization behaviors. Current Biology 34, 3392-3404 (2024).

      Luyckx, F., Nili, H., Spitzer, B. & Summerfield, C. Neural structure mapping in human probabilistic reward learning. eLife 8, e42816 (2019). (This is in the references but not in the text).

      Zhang, M. & Yu, Q. The representation of abstract goals in working memory is supported by task-congruent neural geometry. PLoS biology 22, e3002461 (2024).

      L. Teichmann, T. Grootswagers, T. Carlson, A.N. Rich Decoding digits and dice with magnetoencephalography: evidence for a shared representation of magnitude Journal of cognitive neuroscience, 30 (7) (2018), pp. 999-1010

      Garner, K., Lynch, C. R. & Dux, P. E. Transfer of training benefits requires rules we cannot see (or hear). Journal of Experimental Psychology: Human Perception and Performance 42, 1148 (2016).

      Holton, E., Braun, L., Thompson, J., Grohn, J. & Summerfield, C. Humans and neural networks show similar patterns of transfer and interference during continual learning (2025).

      We thank the reviewer for providing these helpful suggestions. We have taken these references on board and now introduce these findings in the introduction of the manuscript (reproduced below for convenience):

      “In parallel, M/EEG studies have shown that abstract, format-independent representations can emerge dynamically over time. For example, multivariate analyses of MEG data demonstrate cross-decoding of numerical magnitude across distinct symbolic formats (e.g., digits and dice), indicating a shared, format-invariant representation that unfolds with distinct temporal dynamics (Teichmann et al., 2018). More broadly, M/EEG evidence suggests that task-relevant information can be dynamically prioritized, compressed, and reformatted, indicative of a rapid temporal evolution of abstract and behaviorally relevant representations even when spatial localization remains coarse. Recent MEG data suggests that high-dimensional sensory inputs are progressively transformed into lower-dimensional, task-relevant, feature manifolds across distinct processing stages, reflecting dynamic gating and reformatting of information in support of flexible categorization (Duan et al., 2024). Complementary EEG–fMRI evidence also indicate abstract task goals are encoded in a low-dimensional neural geometry that emerges in frontal cortex and communicated to posterior regions to guide implementation of stimulus-specific representations, with the fidelity of this geometry predicting behavioral performance (Zhang & Yu, 2024). Likewise, converging behavioral and computational data indicates successful generalization depends on detecting and encoding abstract relational structure rather than stimulus surface features. In effect, training enables transfer when task phases share an underlying rule or abstract relationship, even across modalities, but not when an overlap is purely perceptual (Garner et al., 2016).”

      “At the same time, reuse of shared abstract representations introduces a computational trade-off, such that overlapping codes that facilitate transfer can also induce interference, as observed in both humans and artificial neural networks (Holton et al., 2025). However, while there is now much work elucidating how learned representations are generalized, it remains unclear whether and how abstracted structural representations are expressed neurally during ongoing stimulus processing, and how they are shaped by prior structural experience. Thus there is a need to characterize not only where abstract representations are located in the brain but also how they dynamically unfold and are reused across contexts in support of compositional generalization.”

      (2) I found it interesting that the authors chose to perform PCA for dimensionality reduction prior to conducting RSA; however, I haven't seen such an approach in the literature before. It would be helpful to either cite prior studies that have employed a similar method or to include a comparison with more standard approaches, such as sensor-level RSA or sensor-searchlight analysis.

      (3) Connected to the previous point, the choice to use absolute distance as a dissimilarity measure is not justified. How does it compare to standard metrics such as correlation distance or Mahalanobis distance? The same applies to the use of Kendall's tau.

      We thank the reviewer for raising these methodological concerns and agree methodological choices should be explicitly motivated and justified. Our primary motivation for using PCA, and retaining components that jointly explain 80% of the variance, was denoising. Sensor-level MEG data are high-dimensional and highly correlated, and representational analyses that operate directly on the full sensor space may be susceptible to noise amplification and overfitting, particularly when estimating distance measures across time. Retaining components up to a fixed variance threshold is a widely used approach, both in MEG decoding and RSA, to preserve the dominant signal structure while attenuating sensor-specific noise. Importantly, this procedure discards only the lowest-variance 20% of the signal and therefore does not impose strong constraints on the representational geometry.

      To address the reviewer’s concern regarding methodological choices and what this means for the conclusions drawn more directly, and to ensure our findings are not driven by specific analytic choices, we conducted additional robustness checks, availing of more “standard” approaches. Specifically, we performed the same RSA on localizer tasks but using sensor-level data without PCA, employing multiple distance metrics (including absolute distance/L1 norm and Euclidean distance/L2 norm). These similarity metrics are commonplace in RSA, providing linear, per-dimension differences between neural patterns (L1) or robust small outlier differences along individual dimensions compared to squared differences (Euclidean/L2), providing simple and interpretable similarity metrics.

      These sensor-level analyses yielded highly similar temporal profiles and statistical effects to the PCA-based results, including the key contrasts reported in the main text. We now include these results in a new Supplementary Figure and reference them explicitly in the Results section.

      In the revised manuscript, we clarify that PCA was used as a principled denoising step, not as a means of imposing structure on the data, and explicitly show that our conclusions are robust across analytic choices.

      “Importantly, to verify that the chosen PCA approach did not impose artificial structure within the data, or introduce other potential confounds, we also conducted the above analyses on sensor level MEG data. Highly similar results were obtained, with consistent results for different similarity metrics (absolute distance (L1 norm) and Euclidean distance (L2 norm), Supplementary Figure 3)), demonstrating that our results and conclusions are robust across analytic choices.”

      Methods

      “In addition to the PCA-based feature analysis, we performed a sensor-level RSA. At each time point, we estimated condition-specific activation patterns using a GLM applied separately to each sensor (dummy-coded stimulus identity). RDMs were then computed across stimuli using mean absolute difference (L1 norm) as the primary distance metric. For completeness, we additionally evaluated Euclidean distances (L2 norm), which yielded qualitatively similar results (Supplementary Figure 3).”

      Our choice of Kendall’s tau rank correlation was motivated by its common use for linking neural and theoretical RDMs (e.g., Luyckx et al., 2019 eLife; Nili et al., 2014 PLoS CB). We have now added these citations to the manuscript.

      (5) The analysis described in the "Abstract representation of dynamical roles in subprocesses" does not appear to convincingly test the stated prediction of a structural scaffolding account. The authors hypothesize that if structure and dynamics from prior experiences are repurposed, then stimuli occupying the same "dynamical roles" across different sequences should exhibit enhanced neural similarity. However, the analysis seems to focus on decoding transitions rather than directly assessing representational similarity. Rather, this approach may reflect shared temporal representation in the sequences without necessarily indicating that the neural system generalizes the abstract function or position of a stimulus within the graph. To truly demonstrate that the brain captures the dynamical role across different stimuli, it would be more appropriate to directly assess whether neural patterns evoked by stimuli, in the same temporal part of the sequence, with shared roles (but different visual identities) are more similar to each other than to those from different roles.

      We thank the reviewer for this careful and constructive critique and analytical suggestion. The reviewer is correct that in the bridge graph traversal, structural roles map onto fixed serial positions within a sequence, meaning that same-role stimulus pairs also tend to share the same temporal position in the sequence. This is a potential confound: neural similarity between same-role stimuli could in principle reflect similarity related to time-in-sequence rather than an abstract structural role per se.

      The original role-based RSA does not fully resolve this concern, and we have now conducted, based on the reviewer’s suggestion, an additional analysis that directly addresses it. Rather than comparing stimuli that share a structural role, we examine whether the neural representation of a single central node stimulus is similar across its two distinct serial positions within the prior and transfer learning sequences. Specifically, in the bridge graph traversal, each central node appears twice per sequence: the left central node occurs at steps 1 and 4, the right central node occurs at steps 5 and 8. We estimate neural patterns for each central node separately at its first and second occurrence, using occurrence-specific GLMs, and then compute cross-phase similarity between prior and transfer learning: the neural pattern evoked by a central node at its first occurrence in prior learning is compared to its pattern at the second occurrence in transfer learning, and vice versa.

      For the 6-bridge prior group, whose prior learning also involved a bridge graph, central nodes were identified using the same bridge-template positions (steps 1/4 and 5/8) in both prior and transfer learning phases. For the 4-cycle prior group, whose prior learning involved a line graph rather than a bridge graph, central nodes in the prior phase were identified using degree-based role assignment (the two nodes with the highest degree that are not boundary or intermediate nodes), ordered by first appearance in the prior trial sequence. Transfer learning central nodes were identified from the bridge graph template in both groups, since transfer learning always involved a bridge graph. The group comparison thus tests whether cross-phase similarity between central node representations is specific to participants whose prior experience included a bridge graph relative to participants whose prior experience involved a structurally different graph, for whom "central" nodes in prior and transfer are central in qualitatively different senses. This approach directly controls for the time-in-sequence confound, since the same node is compared across different serial positions rather than comparing different stimuli that share a role and therefore also share a sequence position.

      We compared this cross-phase similarity between the 6-bridge prior and 4-cycle prior groups. We observe a significant group difference at a late stage of the trial (approximately 1.125–1.25 sec post-stimulus onset, P<sup>FEW</sup> = 0.043, two-sample non-parametric permutation test, one-tailed), with additional differences at earlier time points that did not survive correction for multiple comparisons (0.125 sec: t = 2.18, p = .034; 0.79 sec: t = 2.84, p = .007). This indicates increased neural similarity for central node representations across phases in participants who experienced these roles consistently during prior learning.

      We wish to be entirely transparent, however, about two limitations of this additional analysis with respect to the original dynamical role decoding results reported in Figure 4. First, the temporal profile of the cross-phase similarity effect does not perfectly overlap with the time windows identified in the original decoding analysis, which limits the strength of the convergence argument. We therefore cannot fully rule out a possibility that the earlier decoding effects partly reflect temporal position within the sequence rather than abstract structural role coding per se. Second, this analysis is necessarily based on a smaller and less variable set of comparisons than either the original decoding analysis or the role-based RSA, since the bridge graph contains only two central nodes whose repeated occurrences can be directly compared in this way. This limits the statistical power of the analysis and our ability to draw strong conclusions from it in isolation. We acknowledge both limitations explicitly in the revised manuscript. Nonetheless, the observation of a group-specific effect in the cross-phase analysis, which by design controls for serial position, provides some support for the structural scaffolding account, and the late corrected cluster suggests that role-consistent representations do emerge across learning phases.

      In addition to this online analysis, we conducted a parallel role-based RSA on data from the localizer task. This localizer-based analysis examines representational changes from PRE to POST learning for stimuli that share the same structural role within the relevant sub-process graph structures. We find a cluster-based permutation-corrected interaction effect between prior learning group and graph factor, indicating that representational similarity increases selectively for stimuli sharing the same structural role, rather than uniformly for all stimuli associated with a given graph. Together with the localizer-based RSA results, we believe these converging analyses strengthen the overall interpretation, while we acknowledge the temporal confound as a remaining limitation that future work with designs explicitly counterbalancing serial position across roles could address more definitively. We reproduce below the main text results, supplementary methods and Supplementary Figure (Supplementary Figure 4) detailing this complimentary analysis.

      Main manuscript

      “To further test the robustness of the above effect, and to assess whether abstract dynamical roles are reflected in neural representational geometry during task performance, we conducted a complementary cross-phase representational similarity analysis. This analysis addresses directly whether neural representations of central nodes are stable across their distinct serial positions within a sequence, an expected property if representations reflect abstract structural identity rather than time-in-sequence. Specifically, for each participant we estimated neural patterns for each central node separately at its first and second occurrence (phase) within the sequence traversal, using occurrence-specific GLMs, and computed cross-phase similarity between prior and transfer learning phases. This approach controls for a potential time-in-sequence confound inherent in role-based comparisons, since now, the same functional node is compared across different serial positions (rather than comparing different stimuli with a common sequence position, by virtue of sharing role). Consistent with the decoding results, we observed increased cross-phase similarity in participants with prior experience of Component 6 relative to those with prior experience of Component 4 (Supplementary Figure 4). Specifically, a significant group difference was observed at a late stage of the trial (1.125–1.25 sec post-stimulus onset, P<sub>FWE</sub> = 0.043, two-sample non-parametric permutation test, one-tailed), with additional differences at earlier timepoints that did not survive correction for multiple comparisons (0.125 sec: t = 2.18, p = .034; 0.79 sec: t = 2.84, p = .007). These effects indicate increased neural similarity for central node representations across phases in participants who experienced these roles consistently during prior learning. We consider these results complementary to the main analyses and interpret them with caution given that the group difference was only corrected for multiple comparisons at the late cluster. Importantly, the temporal profile of the cross-phase similarity effect does not perfectly overlap with the time windows identified in the original dynamical role decoding analysis, which limits the strength of the convergence argument. We therefore cannot fully rule out the possibility that the earlier decoding effects reported in Figure 4 partly reflect temporal position within the sequence rather than abstract structural role coding per se. We additionally note that this analysis is based on a smaller and less variable set of comparisons than either the original decoding analysis or the role-based RSA, since the bridge graph contains only two central nodes whose repeated occurrences can be directly compared in this way, limiting its statistical power in isolation. Nonetheless, the observation of a group-specific effect in the cross-phase analysis which directly controls for serial position provides support for the structural scaffolding account, and the late corrected cluster suggests that role-consistent representations do emerge across learning phases, albeit potentially at a later stage of processing than the decoding results alone would suggest.”

      Supplementary Information

      “Cross-phase representational similarity analysis

      Complementary to the decoding analysis in Figure 4, we conducted a cross-phase representational similarity analysis (RSA) to test whether neural representations of central nodes were stable across their distinct serial positions within a sequence, a property expected under abstract structural role coding but not under serial position coding. We focused on central nodes of the 6-state graph, as these nodes appear twice within each sequence traversal of the bridge graph: the left central node occurs at steps 1 and 4, the right central node occurs at steps 5 and 8, allowing first and second presentations to be dissociated.

      Structural roles were assigned separately for prior and transfer learning phases. For line graphs (experienced by the Condition 4 during prior learning), central nodes were identified from node degree in the adjacency matrix (boundary: degree 1; intermediate: neighbors of boundary; central: remaining nodes), and the two central nodes were ordered by first appearance in the trial list. For bridge graphs, central nodes were identified from the predefined 8-step traversal template.

      At each time point and sensor, condition-specific activations were estimated using occurrence-specific GLMs: one GLM fitted to trials corresponding to the first occurrence of each number in the trial list, and one fitted to trials corresponding to the second occurrence. Component 6-specific beta estimates were extracted from each GLM separately, yielding four sets of neural patterns per subject: prior-phase first occurrence, prior-phase second occurrence, transfer-phase first occurrence, and transfer-phase second occurrence.

      Cross-phase representational dissimilarity was then computed using an L1 distance metric (mean absolute difference across sensors) across four cross-presentation pairs: Left central (prior first, transfer second), left central (prior second, transfer first), right central (prior first, transfer second), and right central (prior second, transfer first). These pairings compare the same node across different serial positions and different learning phases, directly controlling for time-in-sequence as a potential confound. The mean L1 distance across the four pairs constituted the cross-presentation dissimilarity index at each time point, where lower values indicate greater neural similarity. Timecourses were baseline-corrected by subtracting the pre-stimulus mean (timepoints 1–25, corresponding to −250 to 0 ms) per participant, and analyses were restricted to post-stimulus timepoints. Group differences between Condition 6 and Condition 4 participants were assessed using a two-sample non-parametric cluster permutation test (cluster-forming threshold p = 0.10, cluster-level alpha = 0.05, 1,000 permutations, one-tailed, consistent with the directional prediction that Condition 6 participants would show greater cross-phase neural similarity for central nodes). The results are presented in Supplementary Figure 4.”

      (4) In the following section, the authors correlate decoding accuracy with participants' behavioral performance across different conditions. However, out of the four reported correlations and the additional comparison of differences between conditions, only one correlation and one correlation difference reach significance, and only marginally so. The interpretation of this finding should therefore be more cautious, especially if it is used to support a link between neural representations and behavior. Additionally, it is possible that correlation with a more clearly defined or targeted neural signature, more directly tied to the hypothesized representational content, could yield stronger or more interpretable correlations.

      We agree with the reviewer that the reported brain-behavior correlations should be interpreted cautiously. Only one of the four correlations reached significance, with effect sizes of medium magnitude. However, we emphasize this correlation is significant when corrected for multiple comparisons for two tests, experience and inference probes (ɑ = 0.025). Additionally, it is important to note, we did not expect all four correlations to be significant. The conditions differ in the extent to which behavior is predicted to depend on the specific neural representation indexed by the decoding analysis, and only a subset of conditions are theoretically expected to show a brain–behavior relationship. The absence of significant correlations in the remaining conditions is therefore not inconsistent with our account. For example, we did not expect the two 4-cycle correlations (depicted in green, Fig. 4C) to be significant.

      We agree with the reviewer that the reported brain-behavior correlations should be interpreted cautiously, and have revised the manuscript to reflect a more measured interpretation. We note that the correlation value reported in the revised manuscript (ρ = .48, p = .016) differs slightly from the originally submitted version (ρ = .41, p = .041), due to a correction in the timepoint-averaging window used to derive the decoding strength measure. We consider the revised value the authoritative one and have updated all relevant text accordingly.

      Only one of the four correlations reached significance, with an effect size of medium magnitude. We would not characterise this correlation as marginal: it survives correction for multiple comparisons across the two theoretically motivated tests (experience and inference probes; corrected α = 0.025), and a medium-magnitude Spearman correlation (ρ = .48) in an individual-differences analysis with n = 25 is consistent with a meaningful brain-behavior relationship, even if the sample size limits the precision of the estimate. We agree that independent replication is needed to establish robustness.

      Additionally, it is important to note that we did not expect all four correlations to be significant. The conditions differ in the extent to which behavior is predicted to depend on the specific neural representation indexed by the decoding analysis, and only a subset of conditions are theoretically expected to show a brain–behavior relationship. The absence of significant correlations in the remaining conditions is therefore not inconsistent with our account. For example, we did not expect the two 4-cycle correlations (depicted in green, Fig. 4C) to be significant, since the 4-cycle-prior group did not experience the bridge graph structure during prior learning and therefore would not be expected to show the same alignment between dynamical role representations and transfer learning performance.

      In any event, based on the reviewer’s (and comments from other reviewers about these correlations), we have revised the manuscript to tone down the interpretation of these results (reproduced below):

      “These findings are consistent with, though not conclusive evidence for, dynamical role representations conveying behavioral benefits. Speculatively, such knowledge representation might enable individuals to constrain their predictions of successive states. For example, upon transitioning to a bridge node one can predict that the successor state will involve "the other side of the bridge". While we acknowledge that the correlation results appear inconsistent across experience and inference probes, it is important to consider that our MEG classifiers were trained and tested on experienced transitions alone, such that enhanced classification accuracy is more reflective of a neural representation of experienced transitions. Under this assumption, the MEG classifier would more closely align with behavioral accuracy for the experience probes (testing actually experienced transitions) than for the inference probes (testing never experienced but only implied transitions on the graph). See Discussion for further elaboration of this point, including why this asymmetry is expected under a model of gradual, imperfect structural learning.

      The observed correlation is also consistent with a general learning-ability account, whereby higher-ability participants both better discover the Component 6 structure (that happens to be shared) across sessions and show higher behavioral accuracy overall. For example, higher-ability participants may rediscover this structure during transfer, without necessarily benefitting from having been exposed to it during primary learning. This ability-based account predicts that decoding strength should also relate to Component 4 accuracy, and that Component 4 and Component 6 accuracy should correlate within each prior learning group. Neither prediction was consistently supported (Supplementary Figure 5): The Component 4 decoding strength and Component 4 correlation was not significant (ρ = .38, p = .071), and did not differ significantly from the Component 4 decoding strength and Component 6 correlation (Steiger's test, p = .656); accuracy correlations between Component 4 and Component 6 were significant in only one prior learning group for each probe type, with no significant between-group differences (all p > .29).

      Given this inconsistent pattern, we consider the general-ability account unsupported, though our low per-condition sample size limits power to rule it out. We therefore treat the brain-behavior correlation as selective to Component 6 experience probes in this sample, and treat it as supportive rather than primary evidence for a link between role representations and transfer, pending independent replication.”

      We agree that a more targeted neural signature could in principle yield a more interpretable correlation with behavior. Our interpretation of the reviewer's comment is that this implicitly requires a measure that captures representational content at the level of individual trials or items, for example, a trial-by-trial estimate of how strongly a given stimulus is represented in its abstract structural role, which could then be correlated with individual participants' behavioral performance. Our current decoding measure does not provide this: it indexes classification accuracy averaged across all trials of a given transition type, yielding a single scalar value per participant per timepoint rather than a trial- or item-level representational estimate.

      Computing such a trial-level measure from our data would require a fundamentally different analysis approach, for example, single-trial decoding confidence scores or RSA-based measures of individual stimulus representational fidelity, which goes beyond what our current classifier-based pipeline and data structure can deliver. We have instead conducted additional analyses that more directly index neural representational content (role-based representational similarity analyses, reported in the revised manuscript), which provide converging support for the proposed computational account.

      Minor Comments:

      “During preprocessing, sensors were excluded based on an identified noise level. However, the authors do not specify the threshold used to define this noise level, nor do they report how many sensors were excluded per participant. It would be helpful to have these details. Additionally, it is unclear why the authors opted to exclude sensors rather than removing noise with MaxFiltering or interpolating bad sensors. Finally, the authors should report how many trials were discarded on average (and standard deviation) per participant.”

      We thank the reviewer for these comments. We have updated the methods section to address the points raised.

      Regarding the noise threshold and number of excluded sensors/trials: sensors were excluded using the default osl_detect_artefacts settings, which apply a Generalised Extreme Studentised Deviate (GESD) test at a significance level of 0.05. On average across all MEG runs and participants, 8.67 sensors (SD = 7.36) and 9.13 trials (SD = 11.46) were excluded. These details have been added to the methods section.

      Regarding the choice to exclude sensors rather than applying MaxFilter or interpolation: MaxFilter was not applicable here as our data were acquired on a CTF system, for which MaxFiltering is not designed. Sensor interpolation was not performed as bad channels are excluded prior to ICA decomposition following standard OSL pipeline practice. Given that excluded sensors represented on average ~3% of the total 273 sensors, we do not expect this to have meaningfully affected our results.

      The updated methods section now reads as follows:

      “On average across all MEG runs and participants, 8.67 sensors (SD = 7.36) and 9.13 trials (SD = 11.46) were excluded (using default osl_detect_artefacts settings; channel significance level for Generalised Extreme Studentised Deviate = 0.05). We did not apply MaxFilter as our data were acquired on a CTF system, for which MaxFiltering is not designed. Sensor interpolation was not performed as bad channels are excluded prior to ICA decomposition following standard OSL pipeline practice; given that excluded sensors represented on average ~3% of the total 273 sensors, we do not expect this to have meaningfully affected the results.”

      Reviewer #3 (Recommendations for the authors):

      (1) The manuscript seems to use the terms generalization, transfer, compositionality, and compositional generalization somewhat interchangeably. While I appreciate that both compositionality and transfer learning are central to the task design, I believe it's important to distinguish these concepts more clearly. Specifically, generalization typically refers to the ability to apply learned structure within a task to novel but similar instances, whereas transfer involves applying learned components or representations across different tasks or contexts. Clarifying these distinctions - ideally with explicit definitions early in the introduction - would help avoid confusion and better situate the contribution of this work within the broader literature.

      (2) The manuscript frequently refers to abstract knowledge or abstract representations. However, I would argue that abstract knowledge is typically characterized by its ability to generalize or transfer across different tasks or domains. In the current paradigm, while the structural relationships between stimuli change, the task demands and sensory modalities remain constant. It would strengthen the conceptual clarity of the paper if the authors could more carefully define what they mean by "abstract".

      We thank the reviewer for these suggestions. We agree that “abstract” can carry different meanings across the literature. We have now added an explicit definition to the introduction clarifying our usage. We use 'abstract' to refer to representations that are invariant to surface sensory features while capturing relational structure, consistent with findings in a representation learning literature (e.g., Bernardi et al., 2020; Behrens et al., 2018). While the reviewer raises the valid point that task demands and sensory modality remain constant across learning phases, we highlight that the stimuli themselves are entirely novel in the transfer phase, such that any representational similarity must reflect relational rather than perceptual overlap.

      We have added explicit definitions of abstract, generalization, transfer, and compositional generalization to the introduction, clarifying how each term applies to our task design and how they relate to one another. We have also aimed for more consistent usage throughout the manuscript.

      This added paragraph in the Introduction reads as follows:

      “Throughout this work, we use "generalization" to refer to the ability to apply learned relational structure to novel stimulus compositions within the same task context, and "transfer" to refer to the reuse of (abstracted) representations across distinct task contexts or learning phases. Note we use “abstract” to refer to representations that are invariant to the sensory specifics of individual stimuli, capturing relational structure (e.g., the role a stimulus occupies within a graph) rather than surface features. Our task is structured compositionally in that every experienced compound stimulus is the joint product of two simultaneously evolving subprocesses, while the specific compound encountered during transfer learning is never observed during prior learning. We use 'decomposition' and 'transfer' to refer to the abstraction and reuse of a single such subprocess across learning phases, and reserve “compositional generalization” for the broader phenomenon whereby task performance depends on appropriately decomposing and recombining structural knowledge, a capacity our design requires of participants. Here we acknowledge that our study speaks most directly to decomposition and transfer of individual structural components rather than to the act of recombination itself.”

      (3) The supplementary materials include a section on replay analyses, but it is unclear how these analyses relate to the main text. I could not find a corresponding discussion or reference to replay in the results or discussion sections.

      We thank the reviewer for flagging this. The replay analysis was referenced in the Discussion of the previous version of the manuscript. To make this analysis more visible, we have also added a brief summary of the null replay result to the Results section, with a pointer to the Supplementary Results where the full analysis and discussion of limiting factors are reported.

    1. Author response:

      The following is the authors’ response to the previous reviews.

      eLife Assessment:

      This valuable study addresses a critical question regarding the role of a subpopulation of cortical interneurons (Chrna2-expressing Martinotti cells) in motor learning and cortical dynamics. However, despite the inclusion of interesting behavioral and imaging data, significant limitations remain, even after revision, in the design of the motor learning task and the associated data analyses. As a result, the presented data are incomplete to support the central conclusions.

      We appreciate the valuable feedback. To address these concerns, we have rephrased all conclusions to explicitly focus on motor execution consolidation rather than learning, as our task design inherently emphasizes performance refinement over acquisition. This reframing is now fully supported by compelling evidence from our data and analysis, demonstrating that Mα2 cell activation reduces pyramidal cell population plasticity and improves motor execution.

      Public Reviews:

      Reviewer #1 (Public review):

      In line 331, the authors refer to session 5 as “training,” describing it as the final spoon session, and session 6 as “re-training,” because it is the first session in which the pellet is presented on the plate rather than on the spoon. However, in Fig. 1F-H, even in the Ctrl group, it is clear that the performance drops significantly in session 5, which is supposed to be the easiest session before switching to the more difficult plate condition.

      As described in the methods, the task is made progressively harder (as evidenced by the success ratio curve), therefore a lower performance in session 5 (the hardest spoon session) is expected, as now explicitly stated in the results (lines 816-825).

      In the classic pellet-reaching task, the spoon sessions would typically be considered “shaping”, while the plate sessions would represent the actual training phase. However, in this manuscript, the authors still insist on referring to session 2 as “learning” and session 5 as “training.” I don’t understand the difference between session 2 and session 5, especially when session 5’s performance is lower than session 2 (even in Fig 1H when you compare succ ratio).

      The experiments were designed to investigate the effect of Ma2 cell activation on learning and training outcomes. As we wanted to compare completely naive mice with mice that had been trained and that had learned the task, we included the first sessions with the spoon in our analysis. In many other studies or experimental set-ups those sessions would have been considered shaping. The reason for this design is that we did not want to miss early changes related to training and learning that could have a great impact on the final outcome, as most dendritic spines that correlate with learning are formed after the initial training session and are maintained in the second training session (10.1016/j.neuron.2021.07.030). During pilot studies, several different strategies were tested and it was discovered that the mice needed to succeed several times in the initial sessions in order to keep trying. Hence, the pellet presentation needed to be less challenging in the beginning than in the final sessions in which the pellet was presented on the plate. Therefore, as explained above, the task was made progressively harder throughout the session and from session to session, thus mice expectedly had more difficulty in session 5. We agree that the session names could be misleading, particularly in the context of our task design, and therefore changed all session labels to session numbers.

      Since session 6 (on the plate) is considered as “retraining,” why don’t the authors present the behavioral results beyond session 6? As a result, it remains unclear whether the animals improved their performance during the retraining phase.

      We agree, and now show behavior performance from sessions 1 to 10 for the behavioural group. Mice displayed a clear improvement after session 6, reaching a plateau after session 7 (Figure 1F-H). Unfortunately, due to technical challenges with reattaching the miniscope multiple times and following the same neurons over time, we do not have miniscope data from beyond session 6, which is why we initially only presented behavioural data up to session 6.

      Lastly, in Fig. 4B the authors present only the success ratio and claim that performance improves with CLZ application. However, when comparing sessions 8-10 between the Ctrl and Cre+ groups, there already appears to be a baseline difference. CLZ treatment in Cre+ mice seem to bring performance only to the WT level rather than producing a clear improvement beyond baseline.

      In the previous version (first submitted), we showed the success rate (number of success per minute), to the same conclusion. Note that our conclusion is supported by the effect of treatment found in Cre+, meaning that Cre+ improved upon CLZ (Ma2 cells increase in excitability) compared to NaCl (No change in Ma2 cell excitability). The control group is a control for the Ma2 cell activation specificity, and as expected it shows no treatment effect (since there is no hM3Dq expression, as already reported, Supplemental Table 1L). Further, the reviewer’s suggestion of a baseline difference between groups is not supported by our data, since no statistical differences were found on these comparisons (t-test eff. size < -1.587; p > 0.293; as already stated in the methods, the absence of significance bars “for any comparison means no significant difference was found”).

      Regarding the alignment between imaging and behavior, the authors report ~100 prehensions per minute. However, the calcium imaging traces show fewer than 20-30 spikes over 150 seconds (~2.5 min; Fig. 1E). This discrepancy raises concerns about whether the authors can truly isolate calcium signals corresponding to individual prehension events (either successful ones or multiple combined events for unsuccessful attempts). The manuscript still does not present behavioral data that directly aligns prehension events with calcium imaging activity. Although the authors performed analyses suggesting that prehension-related activity does not systematically alter nonprehension epochs, this claim is difficult to evaluate without seeing the underlying traces. It is therefore unclear how the authors selected the example calcium traces aligned to prehension onset, given that there are more than 100 prehension events per minute.

      If we understand this comment correctly, the reviewer presumes that there should be a direct relationship between upper motor neuron activity and prehension activity (i.e. muscle activity). Such one-to-one correspondence between prehension events and calcium transients in individual pyramidal neurons should not be expected.

      Upper motor neurons do not fire in a direct, event-by-event relationship with movements. Instead, motor actions emerge from distributed population activity, where individual neurons contribute sparsely and variably. Classical work described in the book Corticospinal function and voluntary movement by Porter and Lemon (1993) show that the relationship between single-neuron firing and muscle contraction is indirect and probabilistic. This circumstance required spike-triggered averaging based on several thousands of recordings to reveal consistent relationships between neuronal firing and motor output, precisely because individual spikes are neither necessary nor sufficient for a movement instance.

      Calcium imaging accentuates this dissociation. Calcium signals are a temporally filtered and nonlinear proxy of spiking activity, with limited sensitivity to single spikes and a bias toward burst-like or temporally clustered firing. As a result, many individual action potentials, especially those occurring in isolation, may not generate detectable calcium transients. Therefore, observing fewer calcium events than behavioral actions is expected and does not imply a failure to capture relevant neural dynamics.

      Thus, motor cortex representations during skilled behaviors such as prehension are distributed across neuronal ensembles rather than encoded at the level of single neurons. Each prehension recruits a subset of neurons, and each neuron contributes only intermittently across trials. Consequently, the appropriate level of analysis is not event-by-event alignment for individual cells, but rather population-level dynamics (e.g., ensemble activity patterns, dimensionality reduction, or trial-averaged responses aligned to behavior).

      We have not selected “example calcium traces aligned to prehension onset”. We performed all quantifications on the average of all trials, and we thus show one example of such traces in Figure I and all average traces in Supplemental Figure 3I. All trials were included, therefore there is no “selection”, as already explained in the methods section (lines 607-611).

      Taken together, the apparent discrepancy between behavioral event rate and calcium event frequency reflects known principles of motor cortex coding and calcium imaging limitations, rather than a methodological inconsistency. This explanation is now added to the discussion section (lines 1186-1211).

      Regarding the baseline effect analysis (Supplemental Figure 3I), we do not understand the claim that the underlying traces for the quantification shown cannot be seen, when they are explicitly shown in the same figure (Supplemental Figure 3A-E). We agree that the figure legends for Supplemental Figures 2 and 3 were missing the description of the traces shown as average traces of all trials for all neurons, with the shade showing the standard error of the mean. We now added this information to the Supplemental Figures 2 and 3 legends.

      In Fig. 1I, the authors also did not address why neural activity during successful trials is already lower one second before movement onset. The longer traces provided do not help to explain this observation or clarify the origin of this pre-movement reduction in activity. It actually further suggests that there may be some artifacts in the imaging that could affect the analysis.

      We understand that the example shown in Figure 1I can cause confusion, therefore we chose a clearer example neuron. As explained in the previous comment, no quantifications were made at the trial level, therefore Figure 1I shows the average +SEM of all trials.

      Overall, because it remains difficult to understand exactly what the authors are analyzing (and because the definitions of the motor learning stages appear arbitrary) it is difficult to agree with the authors’ conclusion that Ma2s cells reduce PyrN cell assembly plasticity during learning, thereby possibly facilitating already acquired motor skills.

      We rewrote our conclusions to better fit our results and thoroughly explained the calcium imaging analysis concerns above. No quantifications (nor claims) were done at single-level trial, and we clearly show the exact traces from where the quantifications were derived (Figure 1E, 1I; Supplemental Figure 2A-H and 3A-H.

      Reviewer #2 (Public review):

      While the authors addressed some of the concerns raised by the reviewers, several major limitations still exist in the revised manuscript.

      (1) I appreciate the authors now showing more measures of the prehension task (total reaches, success reaches/min, and success ratio) and providing more details on the task design. However, it is unclear why the authors chose a task design that is somewhat different from the commonly used approach. Here they increase the distance of the food pellet each session and are thus making the task increasingly harder, whereas commonly the target distance is kept stable (See 10.1038/nature08389 for example). The result is that important readouts of learning (e. g. success rate) thus remain stable, making it impossible to judge if learning has occurred, without a control group of non-trained mice. This makes it impossible to judge if the task is affected by increased Ma2 cell excitability, since there is no reference of how these measurements are supposed to change in a mouse that learns or doesn’t learn the task.

      The experiments were designed to investigate the effect of Ma2 cell activation on learning and training outcomes. As we wanted to compare completely naive mice with mice that had been trained and that had learned the task, we included the first sessions with the spoon in our analysis. In many other studies or experimental set-ups, those sessions would have been considered shaping. The reason for this design is that we did not want to miss early changes related to training and learning, that could have a great impact on the final outcome, as most dendritic spines that correlate with learning are formed after the initial training session and are maintained in the second training session (10.1016/j.neuron.2021.07.030). During pilot studies, several different strategies were tested and it was discovered that the mice needed to succeed several times in the initial sessions in order to keep trying. Hence, the pellet presentation needed to be less challenging in the beginning than in the final sessions in which the pellet was presented on the plate. On previous pilot experiments, when the spoon distance was kept stable across sessions, most animals did not perform the task upon switching to the plate position (a large and abrupt increase in difficulty), whereas progressively increasing the difficulty led to more mice reaching for the plate target. We agree that this task design better reflects motor execution than learning, and have stated throughout the manuscript that learning is unaffected. We also reframed conclusions about learned motor execution to better fit our task design.

      (2) Regarding the analysis of the calcium imaging data, it is still unclear why the authors cannot report a commonly used dF/F0 or z-score value, as recommended by both reviewers. The authors state the 1 sec time window prior to the prehension cannot be used as a baseline (F0), as there might be preparatory motor activity. In that case an even earlier window (such as -2 to -1sec) or z-scores should be used. The current version relabeling the background subtracted fluorescence signal as dF/F0 is misleading. Relatedly, it is unclear why the authors don’t think the 1 sec window before prehension cannot be used as baseline, but at the same time use the difference in calcium activity before and after prehension onset as a cut-off criterion for defining cells as modulated during prehension and including in the analysis.

      As explained in the previous review round, we performed baseline subtraction as described in the methods section: "The baseline components were estimated using a running 8th percentile derived from kernel density estimation over a 250-frame window, and subtracted from each respective trace. Although true F0 estimation is not possible on 1-photon data, the baseline-subtracted trace is here referred to as ΔF/F. The fact that the label ΔF/F is commonly used in 1-photon data is misleading, since studies analyzing miniscope data using the label ΔF/F define F0 as the raw video frame minimum (e.g., 10.1371/journal.pbio.3000584, 10.1111/ejn.70190), mean of “non-spiking” periods for all neurons (e.g., 10.1016/j.crmeth.2025.101221), or providing no F0 definition (e.g., 10.1002/adfm.202511627, 10.3389/fnagi.2025.1550673, 10.1016/j.bpsgos.2025.100531, 10.1038/s41586-025-10096-w), none of which are true F0. We reiterate, as in the previous review round, that any use of the label ΔF/F is technically incorrect, not only here but in any study using 1-photon data.

      After the previous review round we defined F0 as the baseline components estimated as described above, which is a much more reliable and standardized measure of baseline components estimation compared to the measures cited above, using an extensively validated algorithm (10.7554/eLife.38173), and labeled our data as ΔF/F since they are already properly scaled, as previously done (10.3389/fnagi.2025.1550673). However, after this discussion, we suggest reverting back to the more correct technical term “ΔF detr.”. This also aligns with previous other similar work (e.g., 10.1073/pnas.2503139122, 10.3389/fnsys.2026.1765204), and that is what our traces (and any traces from any study derived from 1-photon data) actually are.

      We searched and found some studies analysing miniscope data that have z-scored fluorescence traces, but none of those provided a clear justification for doing so (e.g., 10.1016/j.isci.2026.115514, 10.1016/j.neuron.2025.07.020). We do not think that z-scoring appropriately scales fluorescence traces, particularly when baseline components are already subtracted. Fluorescence traces exhibit strong positive skewness, characteristic of calcium imaging data where the baseline is stable (after removing baseline components as described above) but transient events create a heavy tail, and z-scoring relies on the mean and standard deviation. In highly skewed distributions, both the mean and standard deviation are strongly influenced by the magnitude and frequency of these transients. Consequently, z-scoring the traces artificially compresses the baseline and distorts the relative amplitude of events, leading to biased comparisons between different cells by penalizing cells according to their own activity (more active cells will have more transients, therefore larger mean, and lower z-scored traces), instead of normalizing to a biologically meaningful scale. This can be easily demonstrated, take for example the signal fragment in Author response image 1.

      Author response image 1.

      The A panel shows a fluorescence trace from one neuron. If we slice this trace in half (B), the background component is the same, since they are derived from the same cell. If we z-score those halves, the half with higher activity is penalized (C, blue), while the less active half is artificially increased (C, orange). Since both signals are from the same cell, if z-scoring the traces was an appropriate normalization procedure, the differences between them should remain, which is not the case. Therefore, it is clear that z-scoring does not properly scale fluorescence traces for the purpose of comparisons between cells.

      Regarding the inclusion criterion, we used the difference between before and after activity precisely to include only neurons related to the task, which does not mean that the "before" epoch is baseline, only that it is not the same as the "after" epoch, as shown by data already included in the manuscript. Further, we already ran the suggested analysis (after/before ratio) and presented the full results set: “We found a three-way interaction effect of genotype, session, and prehension accuracy (Supplemental Table 2K; Supplemental Figure 4), with genotype effects for both accuracies on the naive session and successful prehensions during the learning session (Supplemental Table 2L-N), and accuracy effects in control mice across the learning and training sessions (Supplemental Table 2O-P). This indicates that Mα2 cell activity might selectively refine the neural signal balance during planning/execution phases of motor execution particularly on initial training sessions.”

      (3) While the authors have improved their statistical reporting, key information is still missing in several places. For example, no N-numbers are listed in legends for figure 3, and there is no mention of the number of mice for analysis in figures 2 and 3. For clarity, the authors should also include the statistical test performed in the figure legends for any p-values shown in the figure.

      We thank the reviewer for the attention to details, and clarified that Figure 2 shows latency analysis for the same dataset as Figure 1, we now explicitly state the number of mice and assemblies in Figure 3 results section, and added the statistical tests performed in each panel’s legend.

    1. Author response:

      The following is the authors’ response to the previous reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      In this revision the authors address some of the points, but they also make some technical errors. My overall view of the manuscript hasn't changed since the original evaluation.

      Previously I noted that SC sparsity presents an issue when comparing to full FC matrices. They author misinterpreted the Honey et al paper. They resampled ALL entries of the SC matrix (including zeros) from a Gaussian distribution. In effect, this assigns zeros small (but uniform) weights. In Honey et al., the authors resampled only existing edge weights from a gaussian distribution (the rationale at the time was that there might be pushback against the extremely heavy-tailed edge weight distribution). In other words, the zeros are still zeros following this resampling procedure.

      That said, I agree that the log transform is likely useful or necessary given edge weight distributions.

      In short, I still think that the approach is interesting and meritorious, I just don't think the execution is correct.

      Thank you very much for pointing this out. Regarding Gaussian resampling, we recalculated the results to avoid including zeros of the SC matrix in the resampling. As before, we confirmed that when the ROI count is small (200 or less), Gaussian resampling tended to produce a higher SC-FC correlation (Extended Data Figure 2-2a), as the ROI count increased so too did the Sparsity Rate (Extended Data Figure 2-2b), and the log transform tended to produce a higher SC-FC correlation (Extended Data Figure 2-2a). However, for both methods we still observed a tendency for the FC-SC correlation to decrease as the ROI count increased. Therefore, we will continue to use the log transform, but we will update Ext.Data.Fig.2-2 and now explicitly state in the text (lines 132-137) that there is a tendency for FC-SC correlation to be higher as the Sparsity Rate increases.

      Reviewer #3 (Public review):

      Summary:

      In this manuscript, Okuno et al. re-analyze whole-brain imaging data collected in another paper (Brezovec et al., 2024) in the context of the two currently available Drosophila connectome datasets: the partial "FlyEM" (hemibrain) dataset (Scheffer et al., 2020) and the whole-brain "FlyWire" dataset (Dorkenwald et al., 2024). They apply existing fMRI signal processing algorithms to the fly imaging data and compute function-structure correlations across a variety of post-processing parameters (noise reduction methods, ROI size), demonstrating an inverse relationship between ROI size and FC-SC correlation. The authors go on to look at structural connectivity amongst more polarized or less polarized neurons, and suggest that stronger FC-SC correlations are driven by more polarized neurons.

      Strengths:

      (1) The result that larger mesoscale ROIs have higher correlation with structural data is interesting. This has been previously discussed in Drosophila in Turner et al., 2021, but here it is quantified more extensively.

      (2) The quantification of neuron polarization (PPSSI) as applied to these structural data is a promising approach for quantifying differences in spatial synapse distribution. The revision now uses morphological cable length for some analyses rather than straight-line distance, which improves the realism and interpretability of these results.

      Weaknesses:

      One should not score noise/nuisance removal methods solely by their impact on FC-SC correlation values, because we do not know a priori that direct structural connections correspond with strong functional correlations. In fact, work in C. elegans, where we have access to both a connectome and neuron-resolution functional data, suggests that this relationship is weak (Yemini et al., 2021; Randi et al., 2023). Similarly, I don't think it's appropriate to tune the confidence scores on the EM datasets using FC-SC correlations as an output metric. While it is likely that some FC-SC relationship does exist at large scales, it does not in my view justify use of this metric for evaluating noise removal methods, since such methods may inadvertently remove real neural correlates. This concern remains unaddressed in the revision.

      Thank you for pointing this out. Firstly, regarding C. elegans, and mentioned in our Discussion section, the FC of calcium dynamics in the soma was compared with the SC of the whole cell in C. elegans studies (Yemini et al., 2021; Randi et al., 2023). Neurons in C. elegans are non-spiking, and calcium dynamics have been shown to differ between compartments (soma and other parts) in a neuron (Hendricks, et al., 2012). While fly and human studies compared the SC and FC of synaptic population dynamics in brain regions, C. elegans studies compared the SC of cells (not regions) with the FC of dynamics in the cell body. This discrepancy is thought to explain the differing results.

      In support of our approach, numerous studies (cited in our manuscript Introduction) have demonstrated statistically significant FC-SC relationships across species and modalities, including human rs-fMRI and diffusion MRI, marmoset retrograde tracing and rs-fMRI, and Drosophila calcium imaging and connectomics. These findings suggest that still SC provides an important anatomical constraint on FC.

      We also used FC-SC detection in addition to FC-SC correlation. Correlation measures similarity by normalizing the covariance between FC and SC values by the product of their standard deviations. On the other hand, FC-SC detection measures the detection accuracy (AUC) of FC. Since FC and log-transformed SC are fundamentally different, both correlation and detection are considered useful indicators. In both indicators, high correlation and high AUC were observed using the same nuisance removal method. Our results suggested that head movement and the attenuation of fluorescent molecules due to long-duration imaging are the sources of noise, and this provides supporting evidence that the procedure may be improving signal quality. Therefore, we consider FC-SC correspondence to be a biologically motivated validation metric for nuisance removal and a way to validate nuisance removal factors.

      However, we agree that FC-SC correspondence may not be regarded as a ground truth objective, and that biologically meaningful functional relationships may also arise through indirect pathways, network effects, neuromodulation, and other mechanisms not captured by direct SC. As examples, neuropeptides diffuse to transmit signals, while gap junctions tightly and directly connect neurons, and there is also a pathway mediated by glia. Although SC cannot be equated with FC, we believe that the relationship between the two remains strong. To investigate this matter further, we consider it necessary to conduct additional research involving the simultaneous measurement of whole-brain FC (calcium) and ‘non-synaptic’ signals.

      We have rewritten the manuscript to say that SC is not a ground truth but a biologically motivated evaluation metric (line 102) for nuisance removal, and we have added content to the discussion around the points discussed here (lines 296-306).

      Any discussion of FC-SC comparisons should include an analysis of excitatory/inhibitory neurotransmitters, which are available in the fly connectome dataset. The authors examine the ratios of input and output neurotransmitters in different defined regions. However, I think it would be more useful to integrate the neurotransmitter information more fully into the assessment of SC, for instance: examining the signed weight (excitatory - inhibitory), or by examining the excitatory and inhibitory networks separately.

      Thank you for suggesting the idea. This matter has not been thoroughly investigated in this study. Figure 3g shows the correlation between neurotransmitters (rate of neurons) and FC-SC correlation, but we have not been able to analyze the effects on FC-SC in detail. Due to this, we think that this topic requires further analysis as part of future work.

      Comparisons between fly and human MRI data are also premature here. Firstly, the fly connectomes, which are derived from neuron-scale EM reconstructions, are a qualitatively different kind of data from human connectomes, which are derived from DSI imaging of large-scale tracts. Likewise, calcium data and fMRI data are very different functional data acquisition methods-the fact that similar processing steps can be used on time-series data does not make them surprisingly similar, and does not in my view constitute evidence of "similar design concepts."

      We are not saying we have presented evidence; we are merely saying that it is possible that it is a similar design concept. That is, the fundamental calculation is performed analog through local addition, subtraction, and multiplication by multiple synapses, and when it is necessary to transmit the data over a distance, it is converted to digital by convolution. This is the idea of an analogue-digital-hybrid circuit (Shirahata et al., Euro. J. Neurosci., 2025). Although C. elegans lacks sodium channels and most of neurons are non-spiking, AWA cell has been shown to exhibit action potential mediated by calcium spikes (Liu et al., Cell, 2018). This suggests that even C. elegans utilize an analog-digital-hybrid circuit. ‘FC’ is correlation between local activity of synapses, and FC-SC showed a high correlation between regions. This result was similar in both flies and mammals. In other words, functions are implemented locally (analog) and connected over a wide area (digitally). We believe this design is common across multiple species, even at different brain size scales. To address your concern, we modified the text on line 320 to give a more conservative tone.

      The comparison of FlyEM/FlyWire connectomes concludes that differences are more likely a result of data processing than of inter-individual variability. If this is the case, the title should not claim that the manuscript covers individual variability.

      The analysis of the wedge-AVLP neuron strikes me as highly speculative, given that the alignment precision between the connectome and the functional data is around 5 microns (Brezovec* et al, PNAS 2024).

      Thank you for pointing that out. We have changed the title because the original title was considered too broad and general.

      Recommendations for the authors:

      Reviewer #3 (Recommendations for the authors):

      (1) I still feel that the title and introduction overstate the results, despite the small changes to the introduction.

      Thank you for pointing that out. We have changed the title because the original title was considered too broad and general.

      (2) Re: the use of a custom FC-SC score in this manuscript, I agree with the authors that the overall approach is common. However, I would like to see some evidence that the qualitative conclusions in the paper are robust to the way this score has been designed, particularly because it deviates from metrics used in prior work.

      In relation to this, we also performed an additional analysis of the FC-SC correlation using the Gaussian resampling method (Honey et al., 2009) [6]. Compared to the log transform of the SC matrix, Gaussian resampling showed a higher correlation when the ROI count was 200 or less, and as the ROI count increased and the Sparsity Rate rose, the log transform showed a higher correlation (Ext.Data.Fig.2-2a and b). However, in both methods we still observed a tendency for the FC-SC correlation to decrease as the ROI count increased. This content has been added to the main text (lines 132-137).

    1. Author response:

      The following is the authors’ response to the previous reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      The authors have substantially strengthened the manuscript in response to my comments. In particular, they have improved the treatment of non-canonical calls, added further illustrative examples at the level of individual RNA variants, repeated pathway enrichment using an appropriate expression-matched background, assessed treatment-associated cell viability, and moderated several biological claims. The revised manuscript is now most compelling as a technical benchmarking and best-practice resource for high-confidence prediction of a common RNA chemical modification from nanopore direct RNA sequencing.

      The matched-input comparison of two methods, use of unmodified RNA controls, and inhibitor treatment are important strengths. Together, these experiments provide solid support for the central conclusion that careful filtering and appropriate controls can substantially reduce likely false-positive calls and yield a reproducible set of high-confidence predictions. The added analyses also provide useful illustrations of the capacity of long-read sequencing to assign predictions to individual RNA variants, although they do not establish broad superiority over the short-read comparison method.

      A few claims remain insufficiently supported. First, the discussion of non-DRACH sites should cite Cancer mutations rewire the RNA methylation specificity of METTL3-METTL14 (Science Advances, DOI: 10.1126/sciadv.ads4750). In particular, Figure 3C of that study shows that the normal METTL3-METTL14 enzyme retains measurable activity on non-DRACH substrates; this provides a useful precedent for describing the inhibitor-sensitive GGAUU calls as plausible candidates rather than treating non-DRACH calls, especially those detected only by GLORI, as presumptively artefactual. The revised manuscript appropriately notes technical and biological explanations for non-canonical calls and identifies the GGAUU sites as candidates requiring further validation, but this additional context would improve interpretation.

      We thank the reviewer for reminding us of this interesting publication. We have included the citation and adjusted our discussion accordingly (lines 576-579).

      Second, the comparison between Dorado and GLORI remains overinterpreted. The matched-input design and inhibitor perturbation are important strengths, but the current analysis does not establish that sites detected only by GLORI are false positives or that Dorado is a reference standard. This would require, for example, direct comparison of inhibitor responsiveness among GLORI-only and shared sites, while accounting for coverage, conversion efficiency, and other method-specific biases; therefore, phrases such as "GLORI exhibits reduced specificity," "largely spurious," and "validated by an orthogonal approach" are not fully supported by the data presented.

      Thank you for this comment. We agree that our original language potentially overinterpreted the GLORI-Dorado comparison. In our GLORI dataset, the relatively high gene-level non-conversion rate (>5%) particularly limits interpretation of low-proportion sites. Although this background has little effect at high m<sup>6</sup>A/A proportions, it can substantially affect calls in the 10-20% range. Consistent with this limitation, GLORI-only sites were predominantly low-stoichiometry and more often occurred outside DRACH motifs, whereas shared sites were enriched at higher predicted m<sup>6</sup> A/A proportions. GLORI coverage was similar between categories, and all sites analyzed were STM2457-responsive. However, residual non-conversion may disproportionately affect low-fraction calls. Thus, our findings do not establish that GLORI-only sites are false positives but instead indicate unresolved method-specific differences. We have adjusted the section accordingly (lines 327-382) and added two additional subplots in Fig. S21 (lines 1193-1202 contain the new figure legends).

      Similarly, the thresholding approach should not be described as "unbiased." The analysis is useful and empirically informed, but it relies on selected parameters, a manually specified penalty, and predetermined decision criteria. Describing the procedure as "data-driven" or "empirically calibrated against matched unmodified RNA controls" would more accurately convey both its value and its limitations.

      Thank you for this comment. We agree that this language should be used carefully. To our knowledge, we have already refined the relevant wording in the current revised version.

      The additional RNA-variant examples are helpful, but they demonstrate an advantage of long-read data rather than broadly proving that Dorado "outperforms" GLORI for RNA-variant-level quantification. A more accurate formulation would be: "Direct RNA sequencing provides RNA-variant-resolved predictions that are not readily assignable using short-read GLORI data, as illustrated at several loci."

      We have revised the wording to emphasize that DRS enables RNA-variant-resolved predictions that are not readily assignable using short-read GLORI data (lines 384-385 and 404-406).

      Finally, the authors now acknowledge that the functional significance of cell-type differences remains unresolved, but the abstract still presents the results as evidence of "finely tuned" regulation, and the discussion links them to neuronal function. The data provide solid evidence for differences in predicted modification proportions between cell types, but the evidence is incomplete for claims about functional consequences; these statements should therefore be framed as context or hypotheses for future study rather than as inferences from the present experiments.

      Thank you for this comment. In the revised manuscript, we do not describe the observed cell-type differences as evidence of “finely tuned” regulation or infer functional consequences for neuronal function. Any potential relevance is framed only as context for future investigation. We refer to lines 43-46 and 602-606, where we describe our observations about increased m<sup>6</sup>A/A site ratios in HD10.6 cells compared to NHDFs.

      Reviewer #2 (Public review):

      The revised manuscript has improved substantially. The authors have addressed the main concerns raised during the previous round by introducing an IVT-based calibration framework, evaluating background calls across probability thresholds, examining base calling mismatches, and replacing "stoichiometry" with the more appropriate term "predicted modification proportion." The expanded discussion of non-DRACH predictions is also useful and appropriately balanced. Overall, the study now provides a valuable practical framework for Dorado-based RNA modification analysis.

      I have only a few remaining comments, all of which should be addressable through clarification and minor textual revisions.

      (1) The comparison between NHDF and HD10.6 cells does not appear to include independent biological replicates. The observed differences in predicted m6A/A proportions should therefore be presented as differences between the two datasets rather than as general cell-type-specific effects. The interpretation is already cautious in the Discussion, but similar wording should be used in the Abstract, Results heading, and title if applicable.

      We thank the reviewer for this suggestion and agree that the wording should avoid overinterpretation. We consider the title appropriate, as the manuscript reports differences in predicted m<sup>6</sup> A proportions between fibroblast and neuronal datasets. However, to ensure greater precision, we revised the relevant sentence in the Abstract (lines 43-46) and two Results section headings (lines 130-131 and 408-409).

      (2) The direction of the comparison in Figure 3D should be clarified. The percentages represent the fraction of GLORI sites that is also detected by Dorado. Thus, the analysis shows that Dorado increasingly recovers high-proportion GLORI sites. It does not directly demonstrate that high-proportion Dorado predictions are increasingly validated by GLORI. The text should reflect this distinction, and the figure should clearly identify which circle represents each method.

      We thank the reviewer for this clarification. We revised the text in lines 367-369 to clarify that Dorado increasingly recovers high-proportion GLORI sites, and we adjusted Fig. 3D to improve clarity.

      (3) The ratio of calls detected in IVT relative to biological samples is a useful empirical measure of background, but it is not formally a false-positive rate because the true status and testability of every site are not known. A term such as "IVT-to-sample call ratio" or "empirical background-call ratio" would be more precise and would not alter the main conclusion regarding the value of stringent filtering.

      The reviewer’s point is well taken, and we have replaced the use of false-positive with ‘background signal’ throughout the manuscript when dealing with our approach and results. We have however retained the use of false-positive as a term when directly quoting from other published studies (regardless of whether they used this term correctly).

      (4) The description of the change-point framework still contains the placeholder "at least X-fold more signal." The actual enrichment threshold should be provided. The authors should also ensure that a log2 ratio threshold of 1.5 is not described as 1.5-fold enrichment, since these values are not equivalent.

      We thank the reviewer for catching this. We have corrected the sentence on lines 739-740 to note that the fold enrichment is 1.5-fold which equates to a log2 ratio threshold of ~0.585.

      These are relatively minor issues. The authors have responded constructively to the previous reviews, and I do not consider further experimental work necessary.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      (1) Add the Science Advances reference, DOI: 10.1126/sciadv. ads4750, to the discussion of non-DRACH sites and use it to contextualize inhibitor-sensitive GGAUU sites as plausible candidates requiring independent validation.

      (2) Revise language implying that GLORI-only sites are false positives, that GLORI has reduced specificity, or that Dorado serves as the validating reference method; instead, describe the observed agreement and acknowledge unresolved method-specific differences.

      (3) If feasible, compare inhibitor responsiveness directly among shared and GLORI-only sites, reporting coverage and conversion-related quality measures for those categories.

      (4) Replace "unbiased" thresholding language with "data-driven" or "empirically calibrated against matched unmodified RNA controls."

      (5) Revise broad "outperforms" language about RNA-variant-level quantification to specify that long-read sequencing enables predictions at individual RNA variants in the illustrated examples.

      (6) Remove or further qualify statements that infer finely tuned regulation or neuronal functional effects from differences in predicted modification proportions alone.

      We have addressed these recommendations as described above.

    1. Author response:

      The following is the authors’ response to the original reviews.

      eLife Assessment:

      This study reports the relative importance of Tie1 and Tie2 signaling for atrial versus ventricular trabeculation. It is an important study and is one of the few works to date that have carefully and simultaneously analyzed these two processes. In line with a previous study in zebrafish, the authors demonstrate key differences between atrial and ventricular trabeculation. While the imaging and quantitative data were conducted with solid and validated methodology throughout the manuscript, the work would benefit from more rigourous approaches where Tie1/2 signaling is disrupted prior to the onset of atrial/ventricular trabeculation, to allow for a more direct comparison.

      We thank the editors for the eLife assessment. We would like to request that the following statement be modified: “…the work would benefit from more rigourous approaches where Tie1/2 signaling is disrupted prior to the onset of atrial/ventricular trabeculation, to allow for a more direct comparison”. We request this change for the following reasons:

      We utilized two distinct genetic mouse models in this study (as summarized in Fig. 7I), comprising conventional knockouts (Tie1<sup>tm1a/tm1a</sup>, Tie1<sup>ΔICD/ΔICD</sup> and Tie1<sup>ΔICD/ΔICD</sup>;Tek<sup>+/-</sup>) and inducible gene deletion models (Tek<sup>iECKO</sup>, Tie1ICD<sup>iECKO</sup>, and Tie1ICD<sup>iECKO</sup>;Tek<sup>+/-</sup>) [1-3].

      The Tie1<sup>tm1a/tm1a</sup> line is equivalent to the previously published Tie1<sup>-/-</sup> mouse line as demonstrated in our prior work and by others [1, 4-6]. For the Tie1<sup>ΔICD/ΔICD</sup> line, as described in the previous report [2], the expression level of Tie1<sup>ΔICD</sup> decreased dramatically compared with that of wild-type mice, which may result from the nonsense-mediated mRNA decay. Based on the lymphatic and venous phenotypes [1, 2], we conclude that the Tie1<sup>ΔICD/ΔICD</sup> line is almost equivalent to Tie1 null mice.

      Therefore, the Tie1 or Tek alleles were inactivated prior to the onset of atrial and ventricular trabeculations, as shown in Fig. 1, Fig. 2, Fig. 3, Fig. 5A-D, and Supplemental Fig. 3. Based on these findings, we propose that TIE1 is differentially required for atria versus ventricle morphogenesis, and acts synergistically with TIE2 during cardiac trabeculation.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      In this manuscript, Ding et al. use genetic mouse models to demonstrate that atrial trabeculation is more dependent on Tie1/Tie2 signaling than ventricular trabeculation. With additional experimentation that would support the current claims, the results may hold significant value, as atrial trabeculation remains an understudied phenomenon in cardiac biology with potential implications for atrial cardiomyopathy and atrial fibrillation.

      Strengths:

      Detailed characterization of atrial versus ventricular trabeculation across different developmental time-points, and the use of appropriate animal models to address the scientific question at hand.

      Weaknesses:

      The authors have consistently treated mice with tamoxifen after ventricular, but not atrial, trabeculation has already started. As such, the observed cardiac phenotypes - where predominantly atrial trabeculation is affected - might be a mere consequence of the precise time window in which Tie1/2 signaling was impaired, rather than a direct measurement of its relative importance for atrial versus ventricular trabeculation. The conclusions of the paper may thus be significantly strengthened by depleting Tie1/2 signaling prior to the onset of ventricular trabeculation, as is done for atrial trabeculation.

      We thank the reviewer for the comments.

      Regarding the timeline of gene deletion and tamoxifen treatment, we would like to provide the following clarification.

      Fig. 1-3: As described in the Methods and Materials, Tie1<sup>tm1a/tm1a</sup> is a knockout first mouse model established from EUCOMM embryonic stem cells (EPD0735-3B07) targeting Tie1 gene. Therefore, the Tie1<sup>tm1a/tm1a</sup> line is equivalent to the previously published Tie1 null mice (Tie1<sup>-/-</sup>). The Tie1<sup>Flox/Flox</sup> mouse line (with exon 8 floxed) was generated when the lacZ reporter and neo-cassette were excised using the FLPeR mice.

      Fig. 5A-D: To investigate the synergy of TIE1 and TIE2 in cardiac trabeculation, we utilized the Tek<sup>+/-</sup> and Tie1<sup>ΔICD/+</sup> mouse lines and they were crossbred to generate double mutant mice harboring a homozygous Tie1 mutation and a single null Tek allele (Tie1<sup>ΔICD/ΔICD</sup>;Tek<sup>+/-</sup>). Although no obvious defects were observed in atrial or ventricular structures following Tie1 deficiency alone at E10.5, both atrial and ventricular development were disrupted in Tie1<sup>ΔICD/ΔICD</sup>;Tek<sup>+/-</sup> mutants at the same stage (Fig. 5A-D).

      Supplemental Fig. 3: To verify the role of TIE1 in atrial development, we employed alternative knockout mouse line targeting the Tie1 intracellular domain by floxing exons 15 and exon 16 (Tie1ICD<sup>Flox/Flox</sup>). Mutants harboring these null alleles are designated as Tie1<sup>ΔICD/ ΔICD</sup>. As detailed in the previous publication, the line is also equivalent to the previously published Tie1 null mice (Tie1<sup>-/-</sup>). The cardiac phenotypes shown in Supplemental Fig. 3 are indeed similar to those of Tie1<sup>tm1a/tm1a</sup> mutant mice.

      For the inducible knockouts targeting Tie1, Tek and both, the results are shown in Fig. 4, Fig. 5E-H, Fig. 6, and Fig. 7.

      Fig. 4: As mice homozygous for Tek mutation (Tek<sup>-/-</sup>) die before E10.5 [3, 7], we performed studies using the inducible knockout line targeting Tek (Tek<sup>Flox/-</sup>;Cdh5-Cre<sup>ERT2</sup> named as Tek<sup>iECKO</sup>), as shown in Fig. 4.

      Fig. 5-7: To investigate the synergy of TIE1 and TIE2 in the cardiac trabeculation at the later stages of embryogenesis (Fig. 5E-H, Fig. 6) and the postnatal stage (Fig. 7), we used the inducible knockout models targeting Tie1/Tek, including Tie1ICD<sup>iECKO</sup> (Tie1ICD<sup>Flox/-</sup>;Cdh5-Cre<sup>ERT2</sup>) and Tie1ICD<sup>iECKO</sup>;Tek<sup>+/-</sup> (Tie1ICD<sup>Flox/-</sup>;Cdh5-Cre<sup>ERT2</sup>;Tek<sup>+/-</sup>).

      Reviewer #2 (Public review):

      Summary:

      Ding et al. examine the role of TIE1 in cardiac chamber morphogenesis using genetic mouse models targeting Tie1, Tek, or both, and analyzing endocardial cell-mediated chamber formation across multiple embryonic developmental and postnatal stages, supported by analysis of published single-cell datasets and new bulk RNA seq analyses of murine cardiac tissue. The authors find that Tie1 and Tek expression is higher in atrial than ventricular endocardial cells. Notably, endothelial Tie1 is required for atrial trabeculation at E12.5, but is less critical in ventricular trabeculation. TIE1 also acts synergistically with TIE2 during atrial trabeculation. While Tie1 deficiency alone does not cause defects at E10.5, combined heterozygous deletion of Tek disrupts both atrial and ventricular development at E10.5. This synergy is further supported by analyses at later embryonic stages and in postnatal hearts.

      Strengths:

      The study is well-designed, clearly written, and supported by high-quality figures. The performed experiments demonstrate a previously unrecognized role for Tie1 in cardiac development and identify synergistic control of cardiac morphogenesis by Tie1 and Tie2. This synergy is consistent with the previously identified roles of Tie1 and Tek in venous development and with Tie1 involvement in angiopoietin-dependent postnatal vascular and lymphatic remodeling. Together, these findings support a role for Tie1 as a contributor to Ang1-Tie2 signaling during heart development.

      Weaknesses:

      The manuscript does not include direct mechanistic studies; however, RNA seq analysis of atria and ventricles showed reduced expression of Tek, Dll1, and Notch1 upon Tie1 deficiency in developing hearts. Although previously reported mechanisms, such as TIE1-TIE2 heterodimer formation and effects on endothelial junctions, migration, or survival are discussed, no direct mechanistic experiments are performed. Addressing some of these mechanisms would have clarified the basis of Tie1-Tie2 synergy. As two distinct Tie1 models are used, including one targeting the kinase domain, the authors should state whether phenotypes differed or were similar between models.

      We thank the reviewer for this comment. In this study, we provide genetic evidence that TIE1 is differentially required for atrial versus ventricular trabeculation. Although the precise molecular mechanisms underlying TIE1 function warrant further investigation, we have provided compelling genetic evidence of its synergistic role with TIE2 during this process. Crucially, the two genetic models targeting Tie1 (Tie1<sup>tm1a/tm1a</sup>, Tie1<sup>ΔICD/ΔICD</sup>) produced consistent cardiac and vascular phenotypes, as shown in both this study and our previous work [1, 2].

      Regarding endocardial TIE1 in atrial morphogenesis, fully elucidating its downstream mechanism may require the isolation of primary endocardial cells for further study. However, our previous work using HUVECs have demonstrated that TIE1 acts synergistically with its homologue TIE2 to regulate AKT-mediated COUP-TFII protein stability [1, 3]. The essential roles of COUP-TFII in venous and atrial development have been well-documented in the literature [8, 9]. We have expanded our Discussion section to reflect these mechanistic insights.

      Reviewer #3 (Public review):

      Summary:

      Ding et al. investigate the roles of TIE1 and TEK (Tie2) in mouse cardiac development, with a particular focus on atrial trabeculation. The authors employ multiple genetic models, including Tie1ICDflox/flox (with Cdh5-CreERT2), a knockout-first allele (EUCOMM, Tie1 tm1a/tm1a), and a Tek deletion model.

      Based on the dataset from Feng et al. 2022 Nat Commun, the authors report increased expression of Tie1 and Tek transcripts in atrial endocardial cells compared to ventricular cells at embryonic day (E) 14.5. Loss of Tie1 leads to early atrial trabeculation defects detectable at E12.5, whereas ventricular defects appear later and are less pronounced at E14.5. Chamber-specific RNA sequencing reveals stronger transcriptional changes in atrial tissue.

      Conditional deletion of Tek results in a similar phenotype, with more pronounced atrial defects. Combined deletion of Tie1 and Tek (Tie1 ΔICD/ΔICD; Tek+/-) leads to earlier and more severe defects in both atrial and ventricular trabeculation and results in embryonic lethality around E12.5, suggesting a synergistic interaction between the two genes.

      Conditional endothelial deletion of Tie1 combined with heterozygous global Tek at later embryonic stages allows analysis at later time points and again shows more severe defects in atrial trabeculation. Postnatal analysis of this model reveals reduced heart-to-body weight ratios and potential mild atrial abnormalities.

      Strengths:

      (1) The authors address chamber-specific signaling mechanisms underlying atrial versus ventricular trabeculation, an area of high developmental and clinical relevance.

      (2) The study provides a comprehensive temporal analysis across multiple embryonic stages.

      (3) The use of multiple genetic models strengthens the overall conclusions and allows comparative interpretation.

      (4) While focusing on trabeculation, the authors also include observations on coronary vessel development, increasing the broader relevance of the work. The findings are therefore of interest to the wider cardiovascular research community.

      Weaknesses:

      (1) Timing of recombination vs. trabeculation onset

      Ventricular trabeculation begins earlier than atrial trabeculation. Since tamoxifen (in contrast to 4-hydroxytamoxifen) requires metabolic activation, Cre-mediated recombination will occur with a delay. This suggests that atrial trabeculation may be targeted before its onset, whereas ventricular trabeculation may already be underway for 2-3 days at the time of effective gene deletion.

      How do the authors account for this discrepancy in their interpretation?

      Have earlier induction time points been tested to better capture the onset of ventricular trabeculation? This limitation should be explicitly discussed.

      (2) Clarity of genetic models and experimental design

      The study employs several genetic constructs. It would improve clarity if, for each experiment, the specific genetic model and tamoxifen regimen were clearly described before presenting the results.

      We thank the reviewer for the detailed and constructive comments. As detailed above, for studies employing the inducible gene deletion mouse models (models (Tek<sup>iECKO</sup>, Tie1ICD<sup>iECKO</sup>, and Tie1ICD<sup>iECKO</sup>;Tek<sup>+/-</sup>), the genetic models and tamoxifen treatment schemes have been provided in the related figures.

      For the investigation of TIE1 or TIE2 in atria versus ventricle morphogenesis at earlier embryonic stages, we utilized the conventional knockouts targeting Tie1 (Tie1<sup>tm1a/tm1a</sup>, Tie1<sup>ΔICD/ΔICD</sup>) or the combined deletion of Tie1 and Tek (Tie1<sup>ΔICD/ΔICD</sup>;Tek<sup>+/-</sup>), as detailed above.

      (3) Tie1 tm1a/tm1a phenotype vs. known global knockout

      Previous studies (PMID: 8846781, 7596437) show that complete Tie1 loss leads to severe edema, vascular rupture, and embryonic lethality around E13.5-E14.5.

      How does the Tie1 tm1a/tm1a allele differ, given that animals appear to survive longer? Is this allele hypomorphic rather than a full knockout?

      This point requires clarification.

      Tie1<sup>tm1a/tm1a</sup> is equivalent to the full Tie1 knockout (Tie1<sup>-/-</sup>). As demonstrated in our prior work, the Tie1<sup>ΔICD/ΔICD</sup> model produced lymphatic and blood vascular phenotypes similar to those of Tie1<sup>-/-</sup> mutants [1, 2, 5, 6].

      (4) Limited mechanistic insight

      While the authors aim to investigate underlying mechanisms, the current study is largely descriptive and based on mRNA expression and genetic interaction analyses (Tie1/Tek co-deletion). Direct mechanistic insights into signaling pathways remain limited. However, the dataset provides a valuable foundation for future mechanistic studies, which should be more clearly acknowledged in the discussion.

      We thank the reviewer for the comment. We have incorporated this discussion into the revised manuscript

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      The conclusions of the paper may be significantly strengthened by addressing several of the following comments:

      Major critiques:

      The authors state that Angpt1 is more prominently expressed in atrial versus ventricular myocardium and that this might explain the larger impact of Tie1 deletion on atrial versus ventricular trabeculation. However, other ligands for Tie1/Tie2 have been described, such as Svep1, Angpt2, and Lect2. It would be great if the authors could show the relative expression of these ligands in atrial versus ventricular cardiomyocytes over time.

      We appreciate the reviewer's valuable suggestion. To address this, we analyzed the scRNA-seq dataset to compare the expression profiles of key ligands (Angpt1, Angpt2, Svep1, and Lect2) between atrial and ventricular cardiac cells during embryonic development. These new data have been integrated into Supplemental Fig. 1F. Our analysis reveals that Angpt1 is differentially enriched in atrial cells relative to ventricular cells. However, no distinct inter-chamber differences were detected for Svep1 or Angpt2. Notably, Lect2 transcripts were virtually absent in both chambers; this is fully congruent with our bulk RNA-seq data, which showed no detectable Lect2 expression in whole-heart lysates.

      Likewise, the authors indicate that ANGPT1-TIE2 signaling is stronger in atria than ventricles at E14.5. Could this reflect a temporal rather than spatial difference? How does ANGPT1-TIE2 signaling compare between atria and ventricles during different steps of the trabeculation process?

      We thank the reviewer for this insightful question regarding spatial versus temporal dynamics. To address whether the observed differences reflect a temporal shift or a sustained spatial pattern, we evaluated Angpt1 expression across a developmental timeline spanning the major stages of trabeculation, from initiation through remodeling (E10.5 to E18.5).

      As shown in the newly added Supplemental Fig. 1F, Angpt1 is consistently and differentially enriched in atrial cells relative to ventricular cells throughout all examined embryonic stages. This sustained divergence confirms that elevated ANGPT1-TIE2 signaling in the atria is a distinct spatial feature rather than a transient temporal shift. This finding aligns with our ligand-receptor interactome analysis between cardiomyocytes and endocardial cells (Supplemental Fig. 1E). Furthermore, a specialized role for ANGPT1-mediated signaling in atrial morphogenesis has been independently demonstrated by Kim et al. (Cell Rep, 2018), supporting our model that this pathway is uniquely critical for the assembly of the atrial muscular network [10].

      Ding and colleagues demonstrate that loss of endothelial/endocardial Tie1 results in absent atrial trabeculae, while ventricular trabeculae are only moderately impacted. As ventricular trabeculation is initiated much earlier than atrial trabeculation, this discrepancy might, however, be secondary to the precise time point within trabecular network formation at which Tie1 was deleted. The make sure that Tie1 does not prevent ventricular trabeculation to an equal extent as atrial trabeculation, the authors should conduct additional experiments in which Tie1 is deleted before the onset of ventricular trabeculation (i.e., E8.5). Consistent with this, Tie1 knockout mice display substantial ventricular trabeculation defects (Figure 5). This comment extends to the analysis of the Tie2 knockout mice, where knocking out Tie2 starting from E12.5 does not affect ventricular trabeculation at E14.5 but impairs ventricular trabeculation when hearts are analyzed later (at E17.5). Additionally, Figure 5 clearly demonstrates that ventricular trabeculation is impacted in the combined absence of Tie1 and Tie2. Overall, a more detailed analysis of the relative importance of Tie1/Tie2 signaling for atrial versus ventricular trabeculation with more appropriate tamoxifen regimens needs to be performed to support the claims made by the authors.

      While one can deduce from the Methods section that tamoxifen was administered at E10-5-E11.5 for the results depicted in Figure 1, no information is provided regarding the tamoxifen regimens for the following figures, obscuring proper interpretation of the results. The authors should clearly state the precise time window in which they depleted endothelial Tie1 for each Figure in both text and legends, as this essential information is missing in Figures 2 and 3.

      We thank the reviewer for pointing this out. To rigorously investigate the differential requirement of TIE1, as well as its synergy with TIE2, during the distinct stages of atria versus ventricle trabeculation, we utilized both conventional (constitutive) and inducible gene knockout models. For the inducible genetic models, the exact timelines of gene deletion and tamoxifen treatments are detailed within their respective figure panels and legends. Below is a brief overview of the constitutive null models used in this study.

      Fig. 1-3 (constitutive null models): As described in the Materials and Methods, the Tie1<sup>tm1a/tm1a</sup> line is a “knockout-first” mouse model generated from EUCOMM embryonic stem cells (EPD0735-3B07) targeting Tie1 gene. Consequently, the Tie1<sup>tm1a/tm1a</sup> line is functionally equivalent to previously published Tie1 null mice (Tie1<sup>-/-</sup>). The Tie1<sup>Flox/Flox</sup> mouse line (harboring a floxed exon 8) was generated by excising the lacZ reporter and neo-cassette using FLPeR delete mice. As described above, the Tie1<sup>ΔICD/ΔICD</sup> line is also equivalent to Tie1 null mice.

      Fig. 5A-D: To investigate the genetic synergy between TIE1 and TIE2 during the initiation phase of cardiac trabeculation, we crossbred Tek<sup>+/-</sup> and Tie1<sup>ΔICD/+</sup> lines to generate compound mutants harboring a homozygous Tie1 mutation paired with a single null Tek allele (Tie1<sup>ΔICD/ΔICD</sup>;Tek<sup>+/-</sup>). While Tie1 deficiency alone yielded no obvious defects in atrial or ventricular structures at E10.5, compound Tie1<sup>ΔICD/ΔICD</sup>;Tek<sup>+/-</sup> mutants exhibited severe disruption in both atrial and ventricular development at the same developmental stage (Fig. 5A-D).

      In the last paragraph, Ding et al. propose a model in which Tie1/Tie2 signaling drives atrial versus ventricular endothelial/endocardial specification. To substantiate this claim, the authors should identify several genes that differentiate between these two and demonstrate that their asymmetric expression pattern is perturbed in Tie1/2 mutant embryos. Alternatively, single-cell RNA-seq in control and Tie1/2 mutant embryos could provide a more holistic view of endothelial specification processes and their impact on myocardial shape and function.

      We thank the reviewer for these constructive suggestions. We agree that a comprehensive single-cell RNA-seq analysis of Tie1/Tek mutant embryos would provide a holistic view of endocardial specification. While performing this extensive sequencing is beyond the scope of our current study, we believe our present combination of chamber-specific bulk RNA-seq and functional genetic models provides a strong foundation for these mechanisms. Further studies are certainly warranted to provide deeper single-cell insights in this direction, and we have added this point to our revised Discussion section.

      A recent publication (Albu et al., Nature Communications) found no evidence for Nrg/Erbb and Notch signaling in atrial trabeculation, but reported that YAP signaling was implicated in the latter. This raises important questions: Did the authors observe Yap-mediated signaling in their RNAseq datasets? Could Yap/Taz be investigated in control and Tie1/2 mutant mice? Is there a link between Tie1/2 and Yap/Taz signaling in other systems, such as venous versus arterial endothelial specification?

      We thank the reviewer for this insightful comment. Based on our bulk RNA-seq data, we did not observe an obvious change in Yap1 and Wwtr1 (Taz) transcript expression in the hearts of Tie1 null mice compared to their littermate controls. However, this transcriptomic data does not exclude the possibility of post-translational regulation occurring at the protein level, such as alterations in protein phosphorylation, nuclear translocation, or the activation of downstream YAP/TAZ target genes. We agree that investigating potential alterations in YAP signaling following the induced endothelial deletion of Tek or compound Tie1/2 represents an important direction for future study.

      In contrast to the study by Albu and colleagues, the manuscript presented here observes Notch1 downregulation in the atria but not ventricles (Figures 3F, G). What could be the reason for these discrepancies? Does loss of Tie1 and/or Tie2 impair Nrg1, VEGF, or is Notch signaling more impactful in atria versus ventricles at the protein levels?

      We thank the reviewer for the insightful comment. Using a Zebrofish model, Albu et al., (Nat Comm 2024) [11] reported no evidence for Nrg/ErbB or Notch signaling in atrial muscle network formation. Based on our bulk RNA-seq analysis of heart tissues from Tie1 deficient mice compared to littermate controls, we demonstrated a decrease in Erg1 and Notch1 transcripts in Tie1 mutants. In contrast, we detected an increase in Vegfa transcript levels, which may result from compensatory changes in cardiac angiogenesis induced by hypoxic stress upon TIE1 deficiency. The biological significance of these transcriptomic changes requires further investigation. We have modified the text to include this discussion in the revised manuscript.

      In Figures 5 and 6, it is not clear which genotype was used as a control. Are these controls Tek+/-, Tie1ICDECKO, or WT mice? If there were any differences between these genotypes, these should be reported with the appropriate statistical tests.

      We thank the reviewer for pointing this out. We have added the information in the revised manuscript. Related to Fig. 5 and Fig. 6, the genotype for the control mice used are described in the Methods and Materials section. The genotypes of the Tie1/Tek knockout and control mice are as follows: Tie1ICD<sup>Flox/-</sup>;Cdh5-Cre<sup>ERT2</sup> named as Tie1ICD<sup>iECKO</sup>, littermates Tie1ICD<sup>Flox/+</sup> or Tie1ICD<sup>Flox/+</sup>;Cdh5-Cre<sup>ERT2</sup> mice named as Control. Tek<sup>Flox/-</sup>;Cdh5-Cre<sup>ERT2</sup> named as Tek<sup>iECKO</sup>, littermates Tek<sup>Flox/+</sup> or Tek<sup>Flox/+</sup>;Cdh5-Cre<sup>ERT2</sup> mice named as Control. Tie1ICD<sup>Flox/</sup>-;Cdh5-Cre<sup>ERT2</sup>;Tek<sup>+/-</sup> named as Tie1ICD<sup>iECKO</sup>;Tek<sup>+/-</sup>, littermates Tie1ICD<sup>Flox/+</sup>;Cdh5-Cre<sup>ERT2</sup>;Tek<sup>+/-</sup>, Tie1ICD<sup>Flox/+</sup>;Tek<sup>+/-</sup>, Tie1ICD<sup>Flox/+</sup>;Cdh5-Cre<sup>ERT2</sup>;Tek<sup>+/+</sup> or Tie1ICD<sup>Flox/+</sup>;Tek<sup>+/+</sup> named as Control.

      Minor points:

      The resolution of the retinal stainings should be improved.

      We thank the reviewer for pointing this out. We performed the analysis of retinal vascular phenotype in this study, which is for the verification of gene deletion efficiency.

      Sarcomeric defects have been observed in tie1-/- zebrafish. Can the authors check if such sarcomeric defects are also present in their mouse models and if they are more pronounced in atrial versus ventricular cardiomyocytes?

      We thank the reviewer for the interesting comment. We have not studied whether there is any sarcomeric defect in Tie1 null mice, which requires further investigation.

      If Tie1/2 signaling is more critical for atrial than ventricular development and function, is there any evidence for an association between atrial cardiomyopathy and/or atrial fibrillation in humans carrying pathogenic Tie1/Tie2 mutations?

      We thank the reviewer for this insightful comment. Whether human patients carrying pathogenic Tie1/Tie2 mutations have atrial cardiomyopathy and/or atrial fibrillation warrants further investigation.

      Bulk RNAseq reveals that Tie1tm1a/tm1a mice have reduced Nrg1 mRNA levels in the heart (Figure 2I), but this is not reflected in the atrial or ventricular transcriptomics (Figure 3). Could the authors explain this discrepancy in more detail?

      We thank the reviewer for pointing this out. As described above, there was a decrease of Nrg1 transcript level in hearts of Tie1 mutant compared to that of the littermate controls. The biological significance of this change requires further investigation. We have included this discussion in the revised manuscript.

      Reviewer #3 (Recommendations for the authors):

      Unfortunately, line numbers are not provided, which makes it difficult to refer to specific passages.

      We thank the reviewer for pointing this out. We have added line numbers to the revised manuscript t.

      While it is appropriate to mention in the Discussion that Tie1 variants have been associated with lymphatic defects, this information should be removed from the abstract, as the manuscript does not address lymphatic biology, and this statement distracts from the main focus of the study.

      We thank the reviewer for the comment. In the abstract background, we stated: “…TIE1 variants or loss of function mutations were reported in a subset of lymphedema patients, and it is unknown whether the patients have also cardiac defects in addition to the lymphatic abnormality.” By framing the introduction this way, we aimed to establish the central question of our study: whether Tie1 variants or loss-of-function mutations lead to cardiac abnormalities, which could ultimately contribute to or exacerbate systemic lymphedema alongside primary lymphatic defects.

      Figure 5F should include single-channel images for Tie1 staining to allow proper assessment of signal specificity and localization.

      We thank the reviewer for this comment. The co-staining of TIE1 and PECAM1 is intended primarily to demonstrate gene deletion efficiency. As shown In Fig. 5F, TIE1 is efficiently deleted in Tie1ICD<sup>iECKO</sup>;Tek<sup>+/-</sup> mice compared to control mice. Furthermore, as previously reported by Cao et al. [1] and Shen et al. [2], the mutant mice (Tie1ICD<sup>iECKO</sup>;Tek<sup>+/-</sup>) exhibit disrupted venous development alongside defective lymphatic formation.

      Parts of the manuscript use non-scientific language, for example, "doubly knockout mice" or "atria appear to have some wavy edges." These should be revised for a more formal scientific tone.

      We thank the reviewer to point this out. We have modified the text in the revised manuscript.

      Typo error in Figure 1D: "ventricle"

      We thank the reviewer to point this out. We have made the correction with Fig. 1D.

      Reference

      (1) Cao, X., et al., Endothelial TIE1 Restricts Angiogenic Sprouting to Coordinate Vein Assembly in Synergy With Its Homologue TIE2. Arterioscler Thromb Vasc Biol, 2023. 43(8): p. e323-e338.

      (2) Shen, B., et al., Genetic dissection of tie pathway in mouse lymphatic maturation and valve development. Arterioscler Thromb Vasc Biol, 2014. 34(6): p. 1221-30.

      (3) Chu, M. et al., Angiopoietin receptor Tie2 is required for vein specification and maintenance via regulating COUP-TFII. Elife, 2016. 5:e21032.

      (4) Rodewald, H.R. and T.N. Sato, Tie1, a receptor tyrosine kinase essential for vascular endothelial cell integrity, is not critical for the development of hematopoietic cells. Oncogene, 1996. 12(2): p. 397-404.

      (5) D'Amico, G. et al., Loss of endothelial Tie1 receptor impairs lymphatic vessel development-brief report. Arterioscler Thromb Vasc Biol, 2010. 30(2): p. 207-9.

      (6) Qu, X., et al., Abnormal embryonic lymphatic vessel development in Tie1 hypomorphic mice. Development, 2010. 137(8): p. 1285-95.

      (7) Dumont, D.J., et al., Dominant-negative and targeted null mutations in the endothelial receptor tyrosine kinase, tek, reveal a critical role in vasculogenesis of the embryo. Genes Dev, 1994. 8(16): p. 1897-909.

      (8) You, L.R., et al., Suppression of Notch signalling by the COUP-TFII transcription factor regulates vein identity. Nature, 2005. 435(7038): p. 98-104.

      (9) Wu, S.P., et al., Atrial identity is determined by a COUP-TFII regulatory network. Dev Cell, 2013. 25(4): p. 417-26.

      (10) Kim, K.H., et al., Myocardial Angiopoietin-1 Controls Atrial Chamber Morphogenesis by Spatiotemporal Degradation of Cardiac Jelly. Cell Rep, 2018. 23(8): p. 2455-2466.

      (11) Albu, M., et al., Distinct mechanisms regulate ventricular and atrial chamber wall formation. Nat Commun, 2024. 15(1): p. 8159.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      There is prior literature showing a robust relationship between sulcal interruptions in the posterior occipital temporal sulcus (pOTS) and reading ability. The goals of this study were to extend these findings to children examined longitudinally as they become better readers, and to examine the underlying white matter properties in individuals with and without pOTS sulcal interruptions. To do this, the authors collected longitudinal structural, diffusion, and behavioral data in 51 children (TP1 age 5.5, TP3 age 8.2 years).

      First, the authors found that the gyral gap was consistent across time within the subject. This is expected, as they state in the introduction that sulcal patterns are typically established in utero. Next, they found that children with an interrupted pOTS have higher reading scores (across a variety of measures) at timepoint (TP) 3 than children with continuous pOTS, and this was specific to the pOTS, as no associations emerged for the anterior OTS or MFS; this is again expected from prior literature. They then found that the binary presence of this gap, but not anterior OTS or MFS predicted T3 reading performance. Further, they found that a subsample of the lowest readers at TP1 did not have differences in reading score by gyral gap, but that this difference emerged at TP3. Additionally, the gyral gap at TP1 is similar to variance TOWRE 3 reading skills as some behavioral measures at TP1. Examining underlying white matter in a smaller subset of children, the authors found higher MD in children with an interrupted pOTS vs. those with a continuous pOTS, which was contrary to their hypothesis, and higher local connectivity for interrupted, aligning with their hypothesis, but this difference was no longer present when accounting for TP3 reading scores. The authors conclude that structural properties, in this case, the gyral gap, may guide neural plasticity for reading.

      Strengths:

      This paper has an interesting set of longitudinal data to examine the perhaps changing relationship between sulcal interruptions in the pOTS with reading scores. I commend the authors on data collection and attention to detail in the anatomical analyses.

      Weaknesses:

      However, my enthusiasm was somewhat dampened after finding numerous prior publications on this very topic and I'm unclear as to how much more this paper adds to the current literature. Would we expect the existence of sulcal interruptions to be aligned with reading skills in older kids but not younger kids? Is the point to see if the interruptions exist prior to reading (but these children are not really prereaders)? What is the alternative- why would these interruptions not exist? After all, this anatomy is determined prenatally. Children who have pOTS interruptions at T1 should also have these interruptions at T3 (and indeed that is what the authors find). So how can this be the mechanism that drives plasticity? The authors also talk about the neuronal recycling hypothesis but their data cannot speak to this because they do not have fMRI data nor does their sample include only prereaders with no reading experience. The conclusions are overall overstated and not supported by the results. I think this paper could add interesting knowledge for the specific subfield of reading and the brain. However, the current state of the results, especially with the inclusion of so many trending results and the comparison of so many different processing pipelines and models, in addition to a conclusion that is not motivated by the work makes it difficult to appreciate the paper.

      We thank Reviewer 1 for their detailed feedback. The reviewer raises several related concerns regarding the novelty and framing of the study, the interpretation of stable sulcal anatomy, early reading abilities, statistical robustness, and the proposed link between pOTS morphology, white matter, and reading development. In response, we have revised the manuscript to make clearer that the main contribution is not the stability of pOTS morphology itself, nor simply the replication of previously reported cross-sectional associations with reading, but rather how this stable anatomical feature relates prospectively to reading acquisition from the onset of literacy instruction. In particular, we now make more explicit that left pOTS interruption contributes to later reading beyond associations already present at age 5, including through an updated serial mediation analysis, and we better highlight how this relationship develops over time.

      The reviewer’s comments also prompted us to explain more clearly how the complementary analyses in the full sample and in the subgroup with very limited initial reading skills converge to support our conclusion that left pOTS interruption is a particularly strong longitudinal predictor of later reading relative to the benchmark behavioral and familial predictors considered, despite the collinearity between pOTS interruption and emerging literacy skills at T1. We have renamed this subgroup more accurately from “pre-readers” to “initial minimal readers” and clarified its characteristics and range of reading abilities.

      We also moved key analyses from the Supplement to Figure 3 to make the distinction between separate and unique longitudinal contributions easier to follow. The initial-minimal-reader analyses provide a complementary assessment in which confounding with early reading is substantially reduced. At the same time, as the reviewer accurately pointed out, some of our previous wording implied a more categorical superiority than the analyses warrant; we have therefore softened these claims throughout the manuscript while preserving the conclusion that pOTS interruption is among the strongest longitudinal contributors considered. We also added, in response to Reviewer 2, a new systematic analysis supporting the relative cognitive specificity of the pOTS effect.

      Finally, we made several interpretations more precise, notably by presenting the white-matter findings as a candidate pathway rather than a definitive mechanism and by removing implications that our data directly test the neuronal recycling hypothesis. We believe these revisions make the longitudinal contribution, scope, and significance of the findings considerably clearer, and we are grateful to the reviewer for prompting these improvements.

      Reviewer #2 (Public review):

      Summary:

      This manuscript examined the impact of sulcal morphology on reading development. A very specific feature on the ventral surface of the brain was identified, namely the presence of an interruption in the posterior portion of the left occipitotemporal sulcus (pOTS). Compared to children with a continuous pOTS, children with an interruption at age 5 years had better reading ability at age 8. This was a large effect measured in 43 children. Surprisingly, this morphological feature was a better predictor of reading ability than measures of pre-literacy cognitive skills, such as phonological awareness. The effect was tested and reproduced across several different measures of reading ability. The authors hypothesised that the mechanism underlying this benefit related to greater local connectivity, which confers a computational advantage. This was demonstrated using analysis of diffusion-weighted imaging data in 29 of the children obtained at age 8.

      Strengths:

      The novelty of the manuscript is threefold: (i) the measure was made in children who were pre-literate (previous work was in older children and adults); (ii) longitudinal brain imaging and behavioural data were analysed; and (iii) diffusion data were analysed to test a hypothesis about the underlying mechanism.

      The manuscript is exceptionally well written. The methods are detailed and easily reproduced. The approach is thoughtful and meticulous. All possible alternatives appear to have been considered. Where possible, further analyses have been done to address these alternatives. For example, the testing of the specificity of the sulcal interruption to left pOTS was an important addition. None predicted reading skills.

      Weaknesses:

      The correlation of the interruption with all kinds of literacy measures and in particular reading comprehension and then PIQ suggest this interruption might confer a more general cognitive advantage rather than specifically a reading one.

      It would be interesting to know if the anatomical difference predicts any other cognitive ability or if there might be any cognitive cost (a negative correlation) of this sulcal interruption.

      The location of the interruption in the sulcus is quite variable and in some cases, there is more than one interruption. The sample size is probably not big enough to compare these different patterns or to evaluate the influence of the location of the sulcal interruption.

      The sample is quite high-functioning and the generalisability of the findings outside of this specific population is inevitably limited.

      We would like to thank Reviewer 2 for their positive feedback and for their insightful suggestions.

      Cognitive specificity: We agree with the reviewer that the association between left pOTS interruption and performance IQ, as measured in the concept formation learning task, on top of its association with multiple measures of literacy, raises the possibility that this sulcal feature relates to general cognition more broadly. The fact that reading and general cognitive abilities are highly correlated and mutually influence one another over development complicates any attempt to interpret the effect of left pOTS interruption as purely reading-specific. Our results however support a relative specificity of this sulcal feature to reading: left pOTS interruption remains a strong longitudinal predictor of later reading, even when controlling for the moderate association with performance IQ, and its impact on reading skills is larger than on pIQ. Importantly, a new systematic analysis of associations with all the cognitive and academic skills obtained at T3 further supports a relative cognitive specificity to reading: We show that while left pOTS interruption is also significantly associated with several assessments of math, language and general cognition at age 8 (possibly due to the inherent correlations across these domains), hierarchical clustering indicates that pOTS interruption aligns most closely with literacy-related outcomes (cf. See rev 2 recommendation comment (1)). We observe no cognitive costs of left pOTS interruption across the many linguistic, pre-literacy and cognitive domains tested.

      Neuroanatomical precision: We also fully agree that our sulcal marker of interest, i.e., whether the posterior portion of the left pOTS is interrupted or not, is relatively coarse and may lack in neuroanatomical precision (though this robustness may alternatively be seen as a strength). Beyond this first approximation, several questions remain unanswered, including whether additional interruptions confer an additional reading advantage, or whether interruptions in more specific locations of the left posterior OTS would be optimal. Unfortunately, multiple interruptions were too rare and gap locations too unevenly distributed in our cohort to support adequately powered comparisons. These questions can only be answered on larger sample sizes, which we now mention in our revised Discussion. Please refer to See rev 2 recommendation comment (3) for more details and for the results of tentative explorations which did not support clear trends.

      Sample limitations: The characteristics of our sample (being both from a high socio-economic background, as often seen in pediatric research, and high-functioning) indeed limit the generalizability of our results, as we now acknowledge in the Discussion. However, we replicate results by Cachia and colleagues (2018) which were obtained in a sample where half of the participants were from a rural and (very) low socio-economic background, in order to match a sample of illiterate adults, and this association has been now found in multiple samples with various SES and cognitive characteristics. This suggests that overall such associations may be generalizable across extremely varied socio-economic backgrounds and also possibly along the spectrum of general cognitive skills (cf. R2 comment-toaddress #5).

      Additional correction made during revision:

      During the revision process, we identified one subject for whom an anterior OTS gap had been incorrectly included in the diffusion analyses (participant 6007 on previous Supplementary Figure S6). We removed this gap, reran all diffusion analyses, and updated the relevant results and figures. The results and conclusions remained essentially unchanged.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      Comment (1) The results are currently framed in a manner that makes it difficult to figure out what the main findings of the paper are, and to see if those findings support their conclusions.

      The beginning of the results is focused on showing that the longitudinal pipeline has a better consistency across time points, yet the authors still report follow-up analyses with the cross-sectional pipeline, even though those results are only trending. I think it would make more sense to only focus on the longitudinal pipeline because that is the novelty of this manuscript.

      We fully agree with Reviewer 1 that the longitudinal pipeline shows better consistency and likely constitutes a more accurate, less noisy measure of sulcal interruptions, as we report. For this reason, all the results reported in the main figures concern the longitudinally processed data only.

      Yet, we choose to also include and report supplementary cross-sectional analyses since these analyses, while less reliable, are important for several conceptual reasons:

      (1) Since we wanted to demonstrate that T1 brain anatomy predicted T3 behavior longitudinally, it seemed important as a proof of principle to show that this prediction held with T3 brain data completely unseen, i.e., with T1 cross-sectional processing only. We have now clarified the text referring to this analysis (lines 192-196):

      “This importantly implies that left pOTS morphology at T1 was still a significant longitudinal predictor of T3 reading behavior when T3 brain images were not used to improve T1 anatomical segmentations, i.e., with T1 cross-sectional processing alone, despite noisier tissue segmentations with cross-sectional processing (see also Reuter et al., 2012).”

      (2) Since most studies are cross-sectional, reporting cross-sectional effects may constitute a more relevant reference for other studies, and for the generalizability of our results.

      (3) Larger samples were available for the cross-sectional processing, allowing to test a maximum number of children, despite the higher noise in the sulcal measurements.

      Please also note that across the 4 types of processing (2 timepoints x cross-sectional & longitudinal pipelines), only pOTS interruptions measured cross-sectionally at T3 showed a marginal association with reading scores, while the other 3 processings showed a large significant effect. Having established that cross-sectional measures are less reliable, and since our main goal was to demonstrate that T1 morphology predicted T3 reading, such trending results are found in the least reliable and least relevant condition, with otherwise large and significant effects, which seems quite acceptable. If anything, we believe that transparently reporting these consistent results altogether support, rather than challenge, the robustness of the association.

      Our main findings are summarized in the last paragraph of the Introduction as well as in the first paragraph of our Discussion.

      Comment (2) Also, as the authors note, it is known that sulcal patterns develop in utero; therefore, we would expect a perfect alignment between TP1 and TP3- there should be a more in-depth analysis of the lack of alignment in the main results. And further, this is more reason that the results should focus on the longitudinal pipeline which is closer to that expectation. However, it is unclear whether T1 data processed through the longitudinal pipeline preserves anatomical nuances of that time point (since the images are averaged across the timepoints). Maybe the cross-sectional pipeline is a better depiction of how anatomy changes as a child develops.

      We thank Reviewer 1 for raising these relevant questions.

      First, we would like to clarify that T1 longitudinal processing does preserve anatomical nuances of this time point. In fact, the averaging of T1 and T3 MRIs into a subject base is only an intermediate step of the longitudinal pipeline, which then crucially allows to re-initialize T1 MRI and T3 MRI tissue segmentations separately from their respective scans, but using this time the common tissue priors provided by the subject base (hence the reference to distinct “T1 longitudinal” and “T3 longitudinal” processing). We describe this in the Methods (lines 764-769):

      “When images were available at both Time 1 and Time 3 for a child (N=43), the longitudinal Freesurfer pipeline was used, which first creates an unbiased subject average across time points (“base”) and then restarts multiple processing steps at each time point separately from the base template in order to refine tissue segmentations on each image (respectively T1 and T3 longitudinally processed images, Reuter et al., 2012; see Figure 1A).”

      Therefore, a perfect match between T1 and T3 anatomy is not expected, even if we could expect (and indeed find) pOTS morphology, and interruption patterns in particular, to be extremely stable. Actually, our left pOTS interruption classification only changes between the T1 and T3 longitudinal processing for one child, with two left pOTS sulcal components separated by a distance estimated as 1.34mm at T1 and 0.99mm at T3, leading to a different classification given our 1 mm minimum-distance interruption criterion. We added the following sentence accordingly (lines 146-149):

      “Only one child changed left pOTS interruption classification between T1 and T3 under longitudinal processing, due to the measured inter-component distance crossing the predefined 1-mm threshold, consistent with high stability of this macro-anatomical feature.”

      Our results are therefore consistent with the view that sulcal interruption patterns are set in utero and stable after birth. Given that there actually is limited direct evidence to this effect, we chose to confirm this stability as a first step, which we refer to in the Discussion (lines 606-610):

      “In our study, we observed high reliability of the pOTS interruption from age 5 (T1) to age 8 (T3), which is consistent with the longitudinal stability of interruptions of (i) the intraparietal sulcus and postcentral sulcus (Schwizer Ashkenazi et al., 2024), (ii) sulci in inferior frontal cortex (Tissier et al., 2018), and (iii) patterns of the anterior cingulate sulcus (Cachia et al., 2016) observed in late childhood (approximately 8 years onwards) to early adulthood.”

      As discussed above, the longitudinal processing pipeline leads to better precision in assessing neuroanatomy, as well as its change across time (see the seminal paper by Reuter et al., 2012), which is why we mostly use measures derived from the longitudinal processing.

      Comment (3) The analyses starting on p.4 ("Left pOTS interruption is prospectively associated with better reading skills") seem overly fixated on cross-sectional vs. longitudinal processing pipelines. The key comparisons should be on anatomical specificity (posterior or anterior OTS, etc) as well as including T1 reading skills as a regressor to see if the interruptions at T1 explain additional variance in T3 skills.

      We thank Reviewer 1 for highlighting that we had started our result paragraph by a verification that was less essential. We have now reordered our results to highlight those concerning the anatomical specificity to the left pOTS, in the analyses reported under “The association between left pOTS interruption and reading skills was robust to different measurements of reading skills and sulcal interruption in four ways” (line 175 onward).

      Testing whether the interruptions at T1 explain additional variance in T3 skills over and above T1 reading skills is so essential that it is actually the object of the entire next subsection “The effect of left pOTS interruption on reading accumulates over time” (lines 235-274). This claim is supported by the following findings:

      (1) In the subsample of minimal readers with little to no reading experience at T1, we see that despite the absence of associations between left pOTS interruptions and reading at T1, the association is present and significant at T2 and T3 and appears to grow (lines 243-253 and Supplementary Figure 4);

      (2) In the serial mediation analysis across the whole sample that follows, we observe important and significant additional contributions of left pOTS on later reading skills beyond the contributions at T1. We have now clarified this essential point and rephrased these results, notably adding this particular sentence:

      “Importantly, there were also significant contributions of left pOTS interruption onto T3 reading on top of those mediated through T1, with large cumulative effects through T2 and directly onto T3 (d*c+f: ꞵ = 4.580, SE = 1.757, p = .009), while indirect effect through T1 TOWRE scores alone were non-significant (a*b*c+a*e: ꞵ = 0.971, SE = 0.839, p = .25).” '

      We thank the reviewer for bringing to our attention that this was lacking in the previous version and needed to be made explicit. (Please note that p-values for the serial mediation analysis slightly changed, as the bootstrap was rerun to estimate this additional path.)

      The analyses in the following section “Left pOTS interruption makes a strong longitudinal contribution relative to established predictors of reading” also support the same conclusion that left pOTS interruptions explain variance in T3 reading over and above T1 reading, despite the concern of collinearity with early literacy skills in our entire sample, as we explain below in details.

      Comment (4) The authors do a version of this on p. 6 lines 269-273 and show that indeed, pOTS binary classification contributes a very similar proportion of the variance in T3 reading scores as the next best predictor (letter knowledge). They do not seem to be significantly different- are they?

      When longitudinal contributions are tested separately, left pOTS interruption accounts for 20.5% of T3 reading variance while T1 letter knowledge accounts for 19.6% of this variance. While these values appear numerically close, one should first bear in mind that, as an emerging literacy measure rather than a pre-literacy predictor from a different domain, letter knowledge is expected to be a strong predictor of future literacy skills. The fact that left pOTS interruption, a much less proximal neuroanatomical marker, explains slightly more variance in reading stands out as a more interesting observation.

      More importantly, while proportions of explained variance cannot be compared statistically in a straightforward fashion, the collinearity between these two predictors across the full sample anyway completely biases this comparison: because left pOTS interruption already accounts for significant variance in letter knowledge (cf. Figure 3B and analyses reported in lines 320-326), the estimation of the longitudinal contributions of letter knowledge to reading skills is inflated by this collinearity, picking up in addition some of the true effects of sulcal interruption on T3 reading (and vice versa).

      For that reason, our claim that left pOTS interruption is a strong longitudinal predictor of reading relative to pre-literacy skills actually rests on the integration of all of the results reported in the corresponding section (lines 275-367), including: the contributions of each predictor separately under discussion, in addition also their unique contributions above all other predictors, and the analysis of the underlying collinearity and how it reduces the power in testing the true effects of pOTS interruption, as well as the same analyses repeated in the subsample of minimal initial readers where the collinearity between pOTS and emerging literacy is removed. (Please note that in this subsample, letter knowledge has minimal nonsignificant contributions to T3 reading, contrarily to sulcal interruptions - cf. Figure 3D and F and Comment-to-address #6).

      To clarify this entire section and how all these results converge to support our conclusion, we have now moved several supplementary figure panels from Supplementary Figure 5 to Figure 3 (also addressing See rev 2 recommendation comment (9)) and largely edited the text, including:

      “These significant associations between left pOTS interruption, performance IQ and pre-literacy skills (Figure 3B and D), as well as potential associations between pre-literacy skills themselves (cf. correlation matrices in Supplementary Figure 5D and H), make it challenging to fairly assess the separate unique contributions of each of these variables to the longitudinal prediction of reading skills. For instance, because left pOTS interruption explains a significant amount of variance at T1 in letter knowledge, early TOWRE scores and performance IQ, some of its true direct effect on future T3 reading skills is already captured in a baseline model including these cognitive predictors only, even before left pOTS interruption is explicitly entered as a predictor. Yet, even when controlling in a such a stringent way for all pre-literacy skills, early reading abilities, family history of dyslexia and their shared variance with left pOTS interruption in such nested model comparison, left pOTS interruption still had a marginal additional contribution to predicting T3 TOWRE reading scores (ΔR<sup>2</sup> = 5.0%, F(1, 31) = 3.74, p = .062) inspite of this important collinearity. Rapid naming and family history were the only two other predictors that outperformed left pOTS interruption in terms of unique contributions to T3 reading (ΔR<sup>2</sup> = 7.7% and 6.6% for RAN and mother ARHQ respectively, see Figure 3C), possibly because these predictors were among the least confounded with others (see Figure S5D for correlations among predictors) and thus among the least affected by collinearity. Letter knowledge, in contrast, had the smallest, non-significant unique contributions to T3 reading (ΔR<sup>2</sup> = 0.61%, p = .50).”

      Thus, while the separate contributions of letter knowledge to T3 reading was almost as large as that of left pOTS interruption, their unique contributions above each other and other predictors strikingly differed: ΔR<sup>2</sup> = 5.0% for left pOTS interruption vs. 0.61% for letter knowledge.

      Please also note that our statistical approach is particularly stringent: our nested model comparisons evaluated the unique contributions of each variable above all other predictors, i.e. after accounting for the variance in the outcome jointly explained by the covariance between predictors. In such cases of highly collinear variables, statistical power is importantly reduced.

      Comment (5) And again even if the T1 presence of pOTS interruption explains this additional variance, what does that tell us? The brain (as measured by this pOTS measure) does not change from T1 to T3, as evidenced by this result: Lines 178-180: "left pOTS morphology at T1 remained a significant longitudinal predictor of T3 reading without taking into account brain information at T3, i.e., with T1 cross-sectional processing alone." T3 anatomical data is therefore redundant to this fit. This is further confirmed by the results in lines 220-226, showing differences in T1 TOWRE scores between children with continuous vs. interrupted pOTS. Additilly, the finding that "the effect of pOTS interruption accumulates over time" may instead suggest that TOWRE skills are more accurately measured at T3, especially for the lowest scores. It had alreaonady been shown that pOTS interruptions correlate with reading skills in readers- paired with assessment issues/lack of norms at T1 of these reading measures and the lack of change in pOTS over time, these results are not surprising.

      We fully agree with the reviewer that given the previously observed associations between left OTS interruptions and reading skills in 10-year-olds and adults (Borst et al., 2016; Cachia et al., 2018) and the general understanding that sulcal patterns are stable after birth, it was natural to expect that left OTS patterns observed before or at the onset of literacy acquisition would predict future reading skills. Yet, validating hypotheses -however natural they may seem- is essential for moving science forward.

      Beyond this expected longitudinal association, the fact that left pOTS interruption at T1 predicts additional variance in T3 reading above early literacy skills and all other cognitive, linguistic and familial predictors of literacy also tells us new and important things. Notably:

      (1) It shows that this sulcal marker is a large and important predictor of future reading skills, with a predictive performance comparable to or exceeding the conservative benchmark of pre-literacy skills and familial predictors used for the identification of children at risk of dyslexia. This highlights the relevance of this neuroanatomical marker at a theoretical level for reading acquisition, with possible practical implications for early identification and intervention further down the line.

      (2) We learn that the association between left pOTS morphology and reading is not merely a byproduct of pre-existing associations between sulcal morphology and cognitive or familial factors before literacy learning. Instead, our results clarify the neurocognitive origins of the relationship between reading and OTS morphology by showing a prospective and sustained association with reading acquisition between sulcal morphology and reading acquisition during literacy learning.

      Concerning the relevance of T1 vs. T3 brain data, please refer to our response to Comment-to-address #2, in which we clarify that the longitudinal pipeline serves to improve the reliability of the assessment of sulcal interruptions at T1, but that our results are indeed also confirmed using only T1 brain data.

      Concerning the matter of measurement accuracy of the TOWRE at T1, we agree that reading is harder to measure at the very beginning of literacy acquisition, and that the TOWRE is not normed below age 6. For this reason, our analyses controlled for early literacy skills at T1 using both scores of letter knowledge, as measured by the age-appropriate and normed WMRT letter identification subtest, and the principal component of the two TOWRE raw scores (scaled). This ensured a strict control procedure for all measurable emerging literacy skills: letter knowledge, but also word reading and phonological decoding (if already acquired in precocious/early readers, or to confirm this was not acquired yet).

      In the absence of TOWRE norms for all children at T1, we used this TOWRE principal component to derive a T1 TOWRE population-scaled index. This scaling mostly served to ensure that this early reading score would be of a similar nature and scale as the T2 and T3 TOWRE standard scores, notably for statistical and plotting purposes (Supplementary Figure 4A and D).

      Interestingly, we observed in the full longitudinal sample that left pOTS interruption was already associated around age 5 with this T1 TOWRE score, in addition to the letter identification scores. In the context of stronger associations observed at T2 and T3, this suggests that the T1 TOWRE score, even if not normed nor very accurate, does still capture relevant variance in early literacy skills.

      Comment (6) Further, while one main conclusion is that the gyral gap predicts T3 reading ability better than typical behavioral TP1 measures (but it really does not appear to), this result is mixed in with a series of nonsignificant results (labeled as marginal or trending, but p>0.05) and difficult to parse sections. Some, but not all, analyses are performed in a set of 'pre-readers' (defined as scoring <95th percentile on a reading test which is not particularly stringent), and at some points, the authors get a significant result in the whole sample, but not the prereaders and interpret these results as only trending because of a smaller sample size (line 287), but at other times they get a trending result in the main group, and a significant result in the pre-reader group (line 303), and choose to focus on the result of the prereaders. This inconsistency makes me skeptical of why some analyses were done with different samples. The definition of a pre-reader is not really a pre-reader but rather just below an average reader. This also leads back to my question above on the underlying hypotheses, which critically needs to focus on prereaders. Can you further explain the decision to run some analysis in pre-readers (example line 285/286) and further explain what it means to be a pre-reader in this sample? Perhaps try to think of a more direct way to examine the impact of the gyral gap at TP1 predicting behavioral performance at TP3, as a trending result in the whole sample followed by significance in just a subset is not convincing (line 298, 303).

      We thank Reviewer 1 for this opportunity to clarify our results and some misunderstandings.

      We acknowledge, and are sorry for, the lack of clarity of our previous explanations, especially as some analyses are complex and some conclusions require integrating results across multiple analyses to understand the overall implications. We believe that our statistical approach was justified, though perhaps not well explained in the original version. We have now clarified and addressed these issues in the revision by renaming pre-readers to ‘minimal initial readers’ - which is indeed more accurate (thank you for raising this concern) -, better explaining the composition of this subsample and what analyses restricted to this subsample bring (notably lines 243-253, and in the descriptive demographic Table 1), rewriting the entire section “Left pOTS interruption Left pOTS interruption makes a strong longitudinal contribution relative to established predictors of reading” (lines 275-367), and adding a number of figure panels to Figure 3 (previously in supplementary figure 5), to aid the comparison and integration of results across both samples to support our conclusion. To answer directly the reviewer’s questions and remarks:

      Why two groups? We carry out analyses both in our entire available sample and in a subsample with little to no early literacy skills, since these samples are both relevant for our hypotheses and offer different advantages:

      The entire sample allows to maximize sample size, and is more representative of the general population. This naturally implies that some kindergarteners have emerging literacy skills, including letter knowledge, knowledge of a few sight words and minimal decoding. Interestingly, we found these early literacy measures to already be significantly associated with our sulcal marker, but two problems also derive from this: (1) These emerging reading skills preclude from directly testing in this sample our strong hypothesis that pOTS interruption before literary learning predicts future reading scores. (2) The collinearity between the T1 behavioral predictors and left pOTS interruption is a statistical obstacle to testing reliably how each predictor truly contributes to predicting future reading skills separately (as explained in our answer to Reviewer 1’s Comment-to-address #4 above, taking the comparison with letter knowledge as a key example).

      To remove the association between pOTS and T1 reading and bypass both these problems, we perform additional analyses in a decently-sized subsample of children with little to no reading abilities at T1 - that we have now renamed more accurately as ‘initial minimal readers’.

      Definition and composition of our subsample of “initial minimal readers”:

      Kindergarteners are expected to know letters and how to write their names, they may have understood the basics of the alphabetic principle and phonological decoding, and may have learned to recognize a few highly frequent sight words through repeated exposure in their books and environments (e.g., “the”, “and”). From our entire sample, including a number of children accordingly able to read some sight words and decode some syllables and pseudowords (cf. Table 1), we defined a subsample of lowest readers by using a cut-off of a TOWRE population-scaled index at T1 under 95 (due to the lack of norms, cf. see rev 1 recommendation comment (5)). For reference, the equivalent standard score of 95 would correspond to a 37th percentile in a normal distribution.

      This cut-off was chosen as it translated to very little actual reading abilities overall and crucially removed the statistical association between pOTS and T1 reading needed to address our two problems, while being still decently sized to allow for our statistics (n = 24, i.e. 56% of the sample, cf. distributions on Supplementary Figure 4A). We now specify more clearly notably in the results lines 244-253:

      “We conducted a supplementary analysis in the subset of 24 children with the lowest reading scores at T1 (defined as those with a TOWRE T1 population-derived composite score equivalent below 95). Hereafter, we refer to these children as initial minimal readers: 79% could not decode a single syllable or pseudoword in 45 s, with a maximum of four pseudowords decoded, and 63% could not recognize a single frequent sight word, with a maximum of seven words recognized. Although these children showed no difference in T1 reading scores as a function of whether their left pOTS was interrupted or continuous (F(1, 19) = 0.21, p =.66, ΔR<sup>2</sup> = 0.82%, Cohen’s d = 0.034), [...] “

      and methods - lines 988-991:

      “We therefore selected a subsample of children whose TOWRE standard score equivalent at Time 1 was below 95, resulting in a subset of 24 initial pre-readers (median of 0 words read in 45s in SWE, range: 0-7; median of 0 syllables in 45s in PDE, range: 0-4; see Table 1).” as well as Table 1.”

      Expecting a larger proportion of children of this age with no word reading or decoding at all would be both unnecessary for our analyses and developmentally unrealistic, especially in this high-SES sample, selecting an atypical population at especially high risk of dyslexia.

      Discrepancies between statistics in the full sample and the subsample:

      Because this subsample was chosen to remove the associations at T1 between pOTS and early literacy which affected some analyses (cf. Comment #4), some discrepancies in the results across the two samples are actually expected. Conducting statistics on 56% of the full sample may also affect the statistical power for other analyses in the subsample.

      First, concerning issue #1 of the simple longitudinal prediction of T2 and T3 reading, we find that left pOTS interruption also reliably predicts future reading in the subsample of initial minimal readers, even if the association is absent at age 5, confirming analyses in the main sample.

      Concerning the issue #2 of the comparison with other benchmark predictors of literacy, our results in the entire sample show that despite a large amount of collinearity between our T1 predictors (documented, explained and quantified in lines 320-334, Figure 3B and Supplementary Figure 5D, including strong significant associations of left pOTS morphology with T1 reading, T1 letter knowledge and T1 performance IQ) and despite using the most stringent statistical approach to control for it (nested model comparison), left pOTS interruption still has a marginal contribution to predicting T3 reading on top of all other early literacy, pre-literacy, cognitive and familial predictors of reading (Figure 3C), in line with its large separate contributions (Figure 3A). In the subsample of initial minimal readers, where there is only partial collinearity with performance IQ but not early literacy, we find the specific longitudinal contributions of left pOTS morphology to be strong and significant over and above all of the other T1 behavioral and familial predictors (see Figure 3F and corresponding text). In other words, the collinearity present in the full sample weakens statistical power when controlling for other collinear predictors, with only marginal unique longitudinal pOTS contributions in our stringent analyses, while removing this collinearity in the subsample reveals a large and highly significant unique contribution, in line with the large contributions of pOTS observed overall (Figure 3A, D, and F).We believe that detailing these analyses and finding coherent results on both samples, with potential differences in statistical strength explained by specific factors, overall brings reliability to our results and conclusions, rather than challenges them.

      The reviewer refers also to one interesting incidental finding when examining the T1 cognitive associations of the pOTS interruption in the full sample, consisting in a significant association with the concept formation subtest, measuring a form of performance IQ (though a weaker association than with reading skills, see Figure 3B). When restricting to the subsample of initial minimal readers, this association was then indeed found marginal, though of a similar amplitude as in the full sample. We therefore speculated that the combination of a significant effect in the full sample, and of a marginal finding in the subsample, revealed a possibly true underlying effect, while likely affected by a decrease of statistical power associated with using only 56% of the sample. This effect and speculation are in no way fundamental to our study and claims. The new additional analysis revealing a significant association with performance IQ at T3 again in the full sample (Supplementary Figure 6) would however further support this idea.

      Comment (7) Given that there are these potentially major differences in the pOTS, how are the results of structural connectivity mapped to a common template for Figure 4? There is likely an error in registration at the exact location of the observed differences.

      Individual structural connectivity results were mapped to an MNI template space using standard procedures (lines 919-922 of our Methods:):

      “The obtained individual probabilistic fiber density maps were then transformed into template MNI space for statistical analysis using non-linear registration in ANTs, from individual diffusion space (individual FA map) to the HCP1065 MNI FA template, and smoothed with a 4-mm-FWHM Gaussian kernel.”

      As the reviewer points out, group analyses performed in atlas space are inherently affected by variations in neuroanatomy across individuals and by the quality of registrations. Mapping individual connectivity results to template space was however the only approach that made sense to us to evaluate which connectivity benefits would be associated with the presence of such gaps, given the variability in the number and location of gyral gaps in children with interrupted sulci, and the need to find a common comparison ground with children who had a continuous sulcus. High neuroanatomical variability around the pOTS in particular likely plays against us in investigating such connectivity differences. In spite of these difficulties, we do find differences that seem to explain the reading advantage associated with the presence of gyral gaps.

      Comment (8) While I appreciate the control analyses for the white matter connectivity, I think more robust analyses are more appropriate. Are there MD differences between white matter underneath sulci and gyri of neighboring or even distant regions? I'm not sure what the white matter analyses are really adding to the story. The white matter differences do not explain the differences in T3 reading ability.

      Our rationale for choosing and conducting the reported white matter analyses was the following: Having provided strong evidence that left pOTS sulcal interruptions facilitate reading acquisition, a naturally following question was that of its underlying mechanisms. It had been hypothesized - though never tested directly - that white-matter differences associated with the presence of gyral gaps may improve the connectivity around sulcal interruptions and constitute a potential mechanism linking interruptions to behavioral advantages (cf. lines 399-424). We therefore set out to investigate the underlying white matter, how it differed between children with and without interruptions, and its associations with reading skills.

      Since long-distance projection connections tend to terminate more in gyri than sulci, one potential hypothesis was that gyral gaps in pOTS could be a hot-spot for such connections, facilitating the information flow between regions of the OTS and other functional hubs of the reading network. Because a higher density of such projection fiber endings is expected to result increased intra-cortical myelination, we test whether MD values in the gaps vs. sulcus are consistent with a higher myelination in the gaps than in sulcus, but we instead find the opposite pattern of lower myelination (cf. lines 435-457). This invalidated our first hypothesis.

      In this context, it is thus unclear which questions would warrant additional analyses on MD values in other anatomical regions, or what these would bring in our specific search for mechanisms underlying the reading advantage of pOTS interruptions.

      A second potential mechanism was that left pOTS gaps could be associated with increased local connectivity surrounding the left pOTS, through the packing of more U-shaped fibers traveling superficially, resulting somehow in a computational advantage for reading. This time, we found evidence in favor of this hypothesis: children with an interrupted left pOTS had more local white-matter connectivity around the pOTS travelling superficially under the left pOTS and it gaps (cf. lines 477-493). Moreover, when accounting in the same model for T3 reading on top of the presence of interruptions, this increase in local U-shape fibers was instead captured by T3 reading scores rather than the presence of a pOTS interruption. As such, these white matter differences did indeed explain differences in T3 reading, suggesting a candidate local-connectivity pathway underlying the reading advantage.

      Comment (9) Were any of the analyses performed on the right pOTS? What are the differences in the laterality of gaps? Connectivity?

      The right pOTS had an interruption rate of 58.3%, which was similar to that of the left pOTS (56.5%, Fisher test: p = .75, cf. Supplementary Figure 1 and lines 134-139).

      The right pOTS does not show associations with reading skills, which we report in Figure 2C and lines 184-186:

      “[A]ssociations between sulcal interruption and reading skills were specific to the left pOTS within VTC. No significant associations were observed for anterior OTS (aOTS) or MFS in either hemispheres, or for the right pOTS (see Figure 2c, all p-values > 0.58, all ΔR<sup>2</sup> < 0.7%).”

      Due to the absence of an association between the right pOTS and reading abilities, additional connectivity analyses in the right hemisphere did not seem warranted.

      Comment (10) Finally, the authors' conclusion, and particularly the last section of their discussion on the neuronal recycling hypothesis, does not seem related to their data, analyses, or questions. The authors do not motivate the link between a hypothesis focused on changes in functional activation during skill acquisition, to their current work which only has structural and diffusion connectivity data. Either remove or further motivate this discussion.

      While there has been a heated debate on the specific nature and underlying mechanisms of “neuronal recycling”, our intention was merely to frame our results within the general well-established and widely accepted premises that (i) cultural skills such as reading and symbolic number processing are too evolutionarily recent to rely on dedicated neural circuits and therefore must recruit pre-existing cortical territories, and (ii) reading acquisition is accompanied by the development of functional responses to written words in left posterior vOT, around the pOTS, free from dedicated evolutionary constraints.

      Keeping in mind that the left pOTS and surrounding cortex see a major functional development of functional responses to words literacy acquisition is indeed fundamental in order to understand the relevance and implications of our structural results in this particular patch of cortex that hosts the VWFA, and their relative cognitive specificity to reading. Specifically, we claim that strong structure-function associations around the left pOTS for reading may mediate the behavioral benefits of left pOTS gyral gaps.

      We therefore refer to these questions and hypotheses throughout our text. We first mention the existence and importance of structure-function relationships in the case of the VWFA early on in our introduction (lines 57-66). Throughout the paper, we state our hypotheses on how sulcal morphology and the associated structure of white-matter fiber tracts may result in functional and behavioral reading benefits, motivating our white-matter connectivity analyses. The discussion paragraph “Local connectivity differences at gyral gaps: a computational advantage?” (lines 629-648) then explicits in depth our final interpretation linking our sulcal marker and the computational efficiency of the functional reading network, as supported by an extensive literature.

      To avoid any implication that our findings speak directly to the neuronal recycling framework, we have revised the relevant sentence (lines 651-659) and conclusion to focus solely on its broad, non-specific premises and have removed explicit mention of neuronal recycling.

      “Interestingly, associations between sulcal interruptions and behavior have also been reported for symbolic, but not non-symbolic, number processing (Roell et al., 2021; Schwizer Ashkenazi et al., 2024), highlighting common processes by which cultural acquisitions, too recent on the scale of human evolution to rely on dedicated neural circuits (Dehaene & Cohen, 2007), may be boosted by the presence pre-existing gyral gaps. In the case of the left pOTS, various other aspects of early brain structure have been proposed to constrain the development of reading skills and of functional activations for reading in the VWFA and broader neural network involved in reading such as anatomical connectivity (Bouhali et al., 2014; Grotheer et al., 2021; Li et al., 2020; Moulton et al., 2019; Saygin et al., 2016) and cortical morphology. In terms of the latter, longitudinal studies following pre-reading children at familial risk of dyslexia showed for instance that the surface area of the left fusiform gyrus (Beelen et al., 2019) and patterns of grey-matter volume around the VWFA (Skeide et al., 2016) could be predictive of future dyslexia diagnosis.”

      We have also updated the subsection header to “Common cortical constraints on cultural learning” to reflect this more neutral framing, and adjusted the first discussion paragraph and the conclusion to avoid confusion with the neuronal recycling hypothesis. These changes clarify that our discussion situates the findings within a general conceptual background, rather than interpreting them as evidence for a specific theoretical model.

      Comment (11) I think this paper could add interesting knowledge for the specific subfield of reading and the brain. However, the current state of the results, especially with the inclusion of so many trending results and the comparison of so many different processing pipelines and models, in addition to a conclusion that is not motivated by the work makes it difficult to appreciate the paper.

      We thank Reviewer 1 for their suggestions to improve the manuscript. We have revised the text to focus more clearly on the main longitudinal and anatomically specific findings, and have clarified the role of the initial minimal-reader subgroup, the significant longitudinal contribution of pOTS interruption beyond associations with emerging literacy at age 5, and its unique contribution relative to other established predictors of reading. We hope these changes make the central contributions of the study clearer.

      Although the revision adds some content to an already detailed article, we believe that, taken together, these analyses provide a thorough and integrated account of the association between OTS morphology and reading. In particular, they help clarify how macro-anatomical differences in sulcal morphology may relate to cognition, how these associations unfold across development, and how a candidate white matter pathway may contribute to this relationship.

      Minor points:

      Comment (12) Figure 1 needs more explanation for those who have not hand-labeled these regions. Can you clarify what differentiates the continuous left pOTS in the top row and then interrupted pOTS in the bottom row? The top row all has a gap between dark green and light green. Also, what does the color scale mean? Is it a posterior to anterior gradient?

      We thank Reviewer 1 for highlighting the need for clarification. Our legend now stipulates:

      “Left hemispheric views from exemplar children are shown, either with a continuous left posterior OTS on the top row (i.e., no more than one connex OTS component in the space posterior to the white dotted line) or an interrupted left pOTS on the bottom row (two or more sulcal components present in posterior space, with a total Euclidean distance between components ≥1mm). Green and orange gradient colors are respectively used to highlight the different sulcal components of the OTS and MFS.”

      Comment (13) The discussion on sulcal interruption associations with symbolic but not non-symbolic number processing is interesting! Are these sulcal interruptions present in non-human primates?

      To our knowledge, pOTS interruptions directly analogous to the human left pOTS gyral gaps studied here have not been systematically characterized in non-human primates. Macaques do have an occipitotemporal sulcus, and comparative work shows that sulcal landmarks in macaque and human VTC can relate to functional organization. However, the human OTS is laterally displaced relative to the macaque OTS, and the specific left pOTS interruptions examined here are defined in relation to human VTC and literacy. We therefore view the comparative anatomy of these interruptions as an open question.

      Comment (14) Your T1 voxel size (line 629 0.859 x 0.859 x 1.2mm) does not match the recommendation for the FreeSurfer pipeline you stated, being both anisotropic and having a dimension with > 1mm. "The method works well for voxel sizes 0.75 mm3. It should work with voxel between 1mm3 and 0.75mm3 ... We haven't tested the stream for inputs with anisotropic voxels." (https://surfer.nmr.mgh.harvard.edu/fswiki/SubmillimeterRecon). Further, you note in the methods section that small interruptions can be a result of bad segmentation (line 718/719). Given that segmentation is affected by voxel size, and potential partial volume effects. How do the voxel parameters impact the results and reliability of the analyses?

      Our T1 voxel volume was 0.885 mm³, within the voxel volume range for which the FreeSurfer submillimeter stream is expected to work, although we acknowledge the caveat that the stream was not specifically validated for anisotropic voxels. Yet, Freesurfer pipelines resample anisotropic voxels to isotropic ones by default, resulting here in a final voxel size of 0.859mm isotropic on which the submillimeter pipeline was run. To address possible segmentation concerns, we visually inspected all segmentations in bilateral ventral occipitotemporal cortex thoroughly, excluded scans with excessive motion, imposed a conservative> 1 mm criterion for classifying interruptions, and verified high T1–T3 reliability. Thus, while voxel anisotropy may affect very fine morphometric estimates, our macroanatomical feature of interest - the binary pOTS interruption classification - appears robust.

      Comment (15) On line 417, you should refer to the panel of the figure (I think 4c bottom panel), like you did for many other results. It was helpful when you linked a particular result to its matching figure.

      We thank Reviewer 1 for pointing out this omission, which has now been corrected.

      Comment (16) The percentage values on the bars should be larger for Figure 2, they are hard to read.

      We had chosen to represent the p-value significance on the bars, rather than the percentages themselves, which are indicated by the x-axis and reported numerically in the main text (except from the least relevant ones). We have now increased the font size of these significance stars. Thank you.

      Reviewer #2 (Recommendations for the authors):

      The authors may want to consider the points below.

      Comment (1) The relationship with Performance IQ is interesting. It does not predict much variance in reading scores at T3 but it is strongly predicted by the pOTS interruption at T3. There is quite a significant correlation among all the measures. The authors acknowledge the difficulty in assessing the unique contribution of each measure. I was unclear how they "over" controlled for pre-literacy skills etc. (line 296) and would like more elaboration on that in the main text.

      It would be interesting to know whether there were any cognitive measures where better performance was not predicted by the presence of the interruption? Were there any measures where worse performance was predicted? (i.e. a potential cost of this feature).

      A relative specificity of left pOTS interruption on reading:

      We agree that the association between left pOTS interruption and performance IQ at T1 raised the question of the cognitive specificity of a reading advantage associated with left pOTS interruption, as opposed to a possibly more general cognitive advantage as suggested by Reviewer #2 in their public review above.

      This question is of course complicated by the fact that reading skills are by nature highly correlated with general cognitive abilities, as they are also with math abilities (see e.g., the meta-analyses by Ünal et al., 2023) and language. General cognitive skills and reading are in fact so intertwined that they positively and symbiotically influence each other over development (Ferrer et al., 2007; Peng and Kievit, 2020). Yet, bearing these strong associations in mind, our results suggested a certain degree of cognitive specificity of left pOTS interruption benefits on reading. Indeed, while left pOTS interruption predicted about 14.3% of variance in T1 concept formation (measuring performance IQ), it predicts about 20.5% of T3 TOWRE reading scores. In addition, left pOTS interruption significantly and strongly predicts T3 reading scores, while T1 performance IQ did not (cf. Figure 3A, D and C, except in the subsample of initial minimal readers where pIQ has a significant contribution but about twice smaller than that of pOTS interruption - Figure 3F). Therefore, the prospective association between left pOTS interruption and reading skills could not merely be driven by an association with general cognitive abilities at age 5. Finally, left pOTS interruption showed no other significant association with the pre-literacy skills considered (other than early literacy itself), or family history of dyslexia. This points towards a strong and relatively specific contribution of left pOTS on reading acquisition beyond its moderate association with T1 general cognitive skills.

      We also conducted a new analysis to directly address this question, by systematically testing the associations between left pOTS interruption and all the cognitive and linguistic scores that were obtained at T3. Our new results also support the conclusion of a relatively specific cognitive advantage on reading, and are shown in Supplementary Figure 6 (with Supplementary Table 2 providing a description of the different subtests). The results are exposed in the main text as follows, in a new result subsection “Left pOTS interruption has a relatively specific cognitive impact on reading abilities” (lines 369-397):

      “The incidental observation of a significant association between left pOTS interruption and performance IQ at T1, although smaller in magnitude and not sufficient to account for the association with literacy skills, raises the possibility that left pOTS interruption may confer a broader cognitive advantage rather than a specific benefit for reading acquisition. We therefore conducted a supplementary analysis to examine the relative domain-generality versus cognitive specificity of this association. This question is inherently difficult to address because reading and general cognitive skills are strongly correlated and mutually influence each other across development (Ferrer et al., 2007; Peng & Kievit, 2020; Ünal et al., 2023).

      “We gathered all cognitive and linguistic scores obtained at T3, including measures of mathematics, general cognition, executive functioning, language, and reading (see Table S2 for a full list and description of the included subtests), and tested how each measure was associated with left pOTS interruption, residualized for demographic variables and total brain volume. Left pOTS interruption showed strong and significant associations with several measures of language, reading, mathematics, and general cognitive ability (see Supplementary Figure 6). As expected, we also observed strong and significant correlations among the behavioral measures themselves.

      “However, the strongest correlations with left pOTS interruption residuals were observed for reading scores. Moreover, hierarchical clustering grouped left pOTS interruption with a subcluster that included most reading assessments - spanning phonological decoding, word reading, and sentence reading fluency -, as well as spelling and more surprisingly an expressive language index. This reading-related cluster was most closely related to another cluster comprising measures of written and oral language comprehension (i.e., receptive language), followed by a cluster of phonological awareness. In contrast, measures of mathematics, general cognitive ability, backward working memory and rapid naming formed a separate cluster. Thus, although left pOTS interruption is associated with several cognitive, linguistic, and academic measures, its pattern of associations is most closely aligned with children’s reading outcomes, supporting a relatively specific cognitive advantage for reading.”

      We have therefore modified the Discussion paragraph that refers to the question of cognitive specificity vs. domain-generality as follows (lines 564-580):

      “Interestingly, left pOTS interruption also showed associations with other cognitive skills: it was associated with performance IQ at age 5 (see Figure 3B and E), and with performance IQ, math and language skills more broadly at age 8 (Supplementary Figure 6). However, left pOTS interruption was most strongly associated and clustered with assessments of reading at age 8 (as well as spelling and expressive language). In addition, the prospective association between left pOTS interruption and reading skills was not merely driven by an association with general cognitive abilities at age 5 (Figure 3C and F) and no association with any other pre-literacy skill was found (Figure 3B and E). Math, reading, language and cognitive skills are intrinsically highly intercorrelated, as we also observed at age 8, and are known to mutually and positively influence each other over time (Ünal et al., 2023; Peng & Kievit, 2020; Ferrer et al., 2007; Huettig & Hulstijn, 2025; Dehaene et al., 2015). The weaker pOTS cognitive associations may therefore result from the mere combination of a specific pOTS influence reading and of associations between reading and other cognitive domains, although more research is needed to better understand these associations and how they unfold during development. Together, these findings highlight a relative degree of specificity of left pOTS influences to reading abilities, in line with the welldocumented functional specificity of the left pOTS for orthographic processing and reading (e.g., Dehaene & Cohen, 2011; Gaillard et al., 2006; Pillet et al., 2024; Wilson et al., 2013; Woolnough & Tandon, 2024; Zemmoura et al., 2015; Zhan et al., 2023).”

      No observed cognitive cost to left pOTS interruption:

      These different analyses show that there is no negative cost to the presence of left pOTS interruption, or at least not across the wide variety of cognitive skills we considered. While left pOTS interruption was significantly and positively associated with many assessments of general cognition, math and language (perhaps due to inherent associations and interactions between these domains), several domains were not significantly associated with the morphology of the left pOTS: rapid naming, backward working memory, as well as receptive vocabulary and phonological awareness (at least at T1). Except for a nonsignificant correlation of -0.01 with CTOPP Blending Words at T3, no subtest showed negative associations with left pOTS interruption.

      “Over-controlling” and assessing unique contributions:

      We had used the term “over-controlling” to refer to the fact that testing the longitudinal effects of left pOTS interruption on T3 reading over and above a number of strongly collinear covariates (such as letter knowledge, T1 reading scores and performance IQ) by nested model comparison necessarily decreased the estimation of the true effect of left pOTS interruption on reading. Indeed, the baseline model with collinear variables then already accounts for a part of the variability in pOTS morphology and of its effect reading, through its joint effects with other co-variates, even before the sulcal variable is explicitly added in the model. The statistical power to test the true sulcal longitudinal effect by nested model comparison over such a strong baseline is therefore decreased, and the effect is underestimated.

      Since this non-canonical term and our previous explanations appeared confusing, we clarified the corresponding paragraph as follows (lines 336-361):

      “These significant associations between left pOTS interruption, performance IQ and pre-literacy skills (Figure 3B and D), as well as potential associations between pre-literacy skills themselves (cf. correlation matrices in Supplementary Figure 5D and H), make it challenging to fairly assess the separate unique contributions of each of these variables to the longitudinal prediction of reading skills. For instance, because left pOTS interruption explains a significant amount of variance at T1 in letter knowledge, early TOWRE scores and performance IQ, some of its true direct effect on future T3 reading skills is already captured in a baseline model including these cognitive predictors only, even before left pOTS interruption is explicitly entered as a predictor. Yet, even when controlling in a such a stringent way for all pre-literacy skills, early reading abilities, family history of dyslexia and their shared variance with left pOTS interruption in such nested model comparison, left pOTS interruption still had a marginal additional contribution to predicting T3 TOWRE reading scores (ΔR<sup>2</sup> = 5.0%, F(1, 31) = 3.74, p = .062) in spite of this important collinearity. Rapid naming and family history were the only two other predictors that outperformed left pOTS interruption in terms of unique contributions to T3 reading (ΔR<sup>2</sup> = 7.7% and 6.6% for RAN and mother ARHQ respectively, see Figure 3C), possibly because these predictors were among the least confounded with others (see Figure S5D for correlations among predictors) and thus among the least affected by collinearity. Letter knowledge, in contrast, had the smallest, non-significant unique contributions to T3 reading (ΔR<sup>2</sup> = 0.61%, p = .50). In order to reduce the collinearity confounds resulting from the associations between pOTS interruption and T1 early reading skills, we also reran the same analysis in the subsample of initial minimal readers. Left pOTS interruption in this subsample significantly contributed to predicting future T3 reading over and above all pre-literacy skills and family history (ΔR<sup>2</sup> = 27.8%, F(1, 12) = 13.80, p = .003), making it the first independent longitudinal contributor of reading (see Figure 3F). The second largest longitudinal predictor in terms of unique contributions was performance IQ (ΔR<sup>2</sup> = 12.8%, F(1, 12) = 6.34, p = .027). No other predictor had a significant unique contribution to the longitudinal prediction of T3 reading in the subset initial minimal readers, including rapid naming even though its separate contribution was larger than that of pOTS.”

      We also moved several figure panels from Supplementary Figure 5 to Figure 3 so that readers would have the necessary material in the main text to document this collinearity and see how it impacted the separate vs. unique contributions of each predictor to T3 reading.

      Comment (2) It was surprising that no other anatomical feature of the pOTS (like sulcal depth) predicted reading skills. I would have expected these to be quite closely correlated with interruption distance that did predict reading. Do the authors have any thoughts as to why this might be?

      We thank Reviewer 2 for this question. While it seems intuitive that gyral gaps would affect sulcal depth, this mostly depends on whether we consider these gaps to be part of the sulcus -which here we do not- and on how the depth measure is actually calculated. With a definition of the sulcus as exclusive of gyral gaps, sulcal interruptions affect sulcal depth profiles only locally around the interruptions, where the fundus has to emerge to the convex hull surface. Because we measure sulcal depth based on the depth of the 8% deepest vertices (using an approach adjusted from that of Madan, 2019, see Methods lines 845-852), our measure of sulcal depth is essentially unaffected by interruptions.

      As a confirmation and for more details, we provide Author response image 1 for the correlation matrix between the various morphological measures under consideration. (Using the same conventions as other correlation matrices displayed in the article and supplements: only significant correlations are displayed, according to FDR-corrected p-values above the diagonal.)

      Author response image 1.

      Comment (3) I hadn't quite appreciated on first reading the quite large variability in the location of the interruption (see Figure 4a, where three clusters seem to emerge). Nor did I appreciate that more than one interruption was often present (perhaps Figure 1 could be updated to show examples with more than one interruption). Some measures of distance along the OTS could be helpful and a possible comparison of the "types" based on location. I would have thought that proximity to the location of the VWFA might have meant a stronger effect. I presume this could be tested or discussed.

      We entirely agree with Reviewer 2 that these are important questions. Unfortunately, it also appears that these cannot be reliably tested in our sample.

      Specifically, while 25 children out of 43 had at least one interruption in the left pOTS, only 3 of those had two or more interruptions larger than 1mm each (or 6 children with two interruptions of any size). These incidence rates, combined with the fact that the locations of pOTS gaps do not distribute uniformly along the postero-anterior axis (Figure 4A), do not allow us to reliably assess in this sample either whether having more interruptions may confer an additional reading behavioral advantage, or whether interruptions in particular locations of the pOTS could be more beneficial than others.

      We explored - for speculative purposes - whether a relationship may exist between reading scores and the location of left pOTS interruptions, taking the center of mass of the cortical gyral gap volumes as a coarse reference. We found no evidence for any relationship between reading and the locations of the left pOTS gap along the antero-posterior axis, nor between reading and the distance of the gap centroids to the VWFA (taking the Neurosynth reading meta-analysis peak coordinates, MNI -44 -58 -12), or between reading and the distance to the VWFA standard coordinates along the Y axis only (please see Author response image 2).

      We choose not to report these analyses in the main text as they seem largely underpowered.

      However, we added an example participant with two left pOTS interruptions in Figure 1 as suggested, and now added reference to these important questions in the Discussion, for future studies to address (lines 596-600):

      “Such large-N approaches are needed to answer a number of outstanding questions, such as, in our case, whether there is an additional behavioral reading benefit to having two or more left pOTS interruptions - since these were too infrequent in our sample -, or whether gyral gaps placed in specific locations along the left pOTS may be optimal to for facilitating reading acquisition.”

      Author response image 2.

      Comment (4) It wasn't clear to me how the analysis of the diffusion data proceeded in the case of more than one interruption - it appears that each one was measured but this could be clarified. Is the location of relevance to the findings?

      Regarding diffusion analyses, the diffusion tensor analysis averaged values across all pOTS interruptions together in the few children who had several. The tractography analysis used the full pOTS and all its interruptions, if present, together as a seed volume.

      The precise location of the gyral gaps would indeed be very relevant to the tractography findings as one expects the gyral gaps to relate in a local fashion to the neuroanatomy of the underlying white matter. However, using the whole pOTS with its gaps as a seed seemed to us the only reasonable way to investigate the white-matter correlates of the effect of gyral gaps on reading at a group level, given (i) the large variability in gap location among the 15 of children with interruptions and diffusion data, (ii) the fact some children had multiple gaps, and most crucially (iii) the need to find a common ground for comparison with the group with no left pOTS interruption (continuous sulcus). The fact that our analyses average along the whole pOTS and across children with different pOTS gap locations likely washes away some of this neuroanatomical specificity, thus reducing the strength of any expected effect.

      Comment (5) The authors could include a discussion of the sample's characteristics. They are not necessarily representative given the high SES and the average PIQ being more than 1SD above the mean.

      We thank Reviewer 2 for pointing out this limitation we had overseen.

      High-SES and high-functioning population samples indeed constitute a common bias in pediatric research samples, since study participation requires parents to have the time, interest and access to necessary information. This bias was likely increased here by the fact the data was acquired at Stanford University, in a very privileged area (Palo Alto, CA). The median performance IQ was indeed about one standard deviation above the population mean. Moreover, our sample is enriched for family history of dyslexia. We agree with the reviewer that this limits the generalizability of our results.

      Yet, we replicate the association between left pOTS interruption and reading skills observed by Cachia and colleagues (2018) in a sample where half of the participants were from a rural and (very) low socioeconomic background (so that they would match a sample of illiterate adults), and with limited higher education. This suggests that, overall, such associations may generalize across extremely varied socioeconomic backgrounds and also possibly along the spectrum of general cognitive skills.

      Since our reviewed preprint came out, two other studies further replicated associations between the left pOTS and reading skills (Cachia et al., 2025; Yao et al., 2026), in populations of different ages, countries and across the reading spectrum, including many children with dyslexia (Yao et al., 2026). While SES and cognitive skills are not systematically reported in those studies, one could assume that these studies and ours pooled together would be more representative.

      Accordingly, we added this paragraph to the discussion (lines 548-562):

      “Our study further extends previous results by Borst, Cachia and colleagues (2016; 2018) to a population of children with above-average cognitive and reading scores, from relatively high-SES families, and enriched for family history of dyslexia (cf. Table 1) - although no child met criteria for dyslexia by T3. While our sample is not representative of the general population, thereby limiting the direct generalizability of our results, half of the adult sample from Cachia et al. (2018) came from low socio-economic and rural backgrounds (matched to a sample of illiterate adults), suggesting that the association between left pOTS interruption and reading skills is robust across socio-economic contexts. Since our reviewed preprint came out, the association between left pOTS interruption and reading was further replicated (Cachia et al., 2025; Yao et al., 2026), notably in a larger child sample along the full reading continuum and oversampling children with dyslexia (Yao et al., 2026). (Of note, the finding that pOTS morphology correlated in adults with reading fluency rather than accuracy (Cachia et al., 2025) may also explain one of two prior negative findings concerning the association between pOTS and reading (Del Mauro et al., 2022)). Thus, our results together with the extant literature overall underline a common effect of left pOTS interruption observed across the continuum of reading abilities, and possibly of cognitive abilities.”

      Minor

      Comment (6) Line 342-44: A visualisation of what is meant by superficial vs deep plis de passage would help.

      While an illustration of deep vs. superficial plis de passage would greatly help in clarifying this distinction for the readers, we feel that providing such a visualization in our figures would be equally confusing, if not more, as it may prime readers to wrongfully assume that we differentiate between superficial and deep plis de passage in our own analyses. Instead, we have tried to further clarify the distinction between deep and superficial plis de passage in the text as follows (lines 418-424):

      “Indeed, Bodin and colleagues (2021) showed that, in the superior temporal sulcus (STS), the presence of plis de passage was associated with a higher density of U-shaped fibers connecting adjacent gyri. Superficial plis de passage, i.e., complete sulcal interruptions with a gyral gap visible on the cortical surface, showed an even higher local connectivity advantage than deep plis de passage, the complete gyral gaps or partial interruptions with sulcal pinching which are buried within the depth of the sulcus. (Please note that in our study, we focus on superficial gyral gaps visible on the cortical surface only, and do not classify deep plis de passage.)”

      Comment (7) Line 96 - replace "blindly from" with "without awareness of" or "while .... were concealed".

      The text was edited accordingly (lines 102-103 and 781) - thank you.

      “[...] the OTS and MFS were delineated manually in each hemisphere, without awareness of the reading scores [...] Sulcal labeling was conducted without awareness of the children’s reading scores [...]”

      (8) Line 547 - it is my impression that the findings of morphological differences in dyslexia are quite mixed. This gives the impression that the studies reported are representative of quite a vast number of studies and I don't think that is the case. Perhaps a sentence here with some more scepticism or alluding to the diverse findings in dyslexia?

      It was indeed not our intention here to simplify or summarize a broad literature on morphological differences in dyslexia, but rather to cite a few example results in support of the preceding assertion “various other aspects of early brain structure have been proposed to constrain the development of reading skills”.

      We clarified this sentence as follows (lines 659-662):

      “[L]ongitudinal studies following pre-reading children at familial risk of dyslexia showed for instance that the surface area of the left fusiform gyrus (Beelen et al., 2019) and patterns of grey matter volume around the VWFA (Skeide et al., 2016) could be predictive of future dyslexia diagnosis.”

      Comment (9) Finally, there is quite a lot of supplemental information, some of which is very interesting. I would recommend that the authors check what could be usefully transferred to the main body of the article. eLife uses figures and figure supplements followed by Appendices and the authors might want to check this before deciding on the final version of record.

      We thank Reviewer 2 again for this suggestion to improve our manuscript. We have chosen to move several figure panels for Supplementary Figure 5 to Figure 3, following this suggestion, and given that our previous explanations in the paragraph concerning reading predictors appeared confusing to both reviewers (cf. see Rev 2 recommendation comment (1) and rev 1 recommendation comment (4)).

      While figure supplements seem handy for reading the article directly on the eLife website, we chose to stick with the more standard practice of one appendix or supplementary file gathering all the additional information, which seems more accommodating of different reading practices overall.

      References for Response to Reviews:

      Borst G, Cachia A, Tissier C, Ahr E, Simon G, Houdé O (2016) Early Cerebral Constraints on Reading Skills in School-Age Children: An MRI Study. Mind, Brain, and Education 10:47–54.

      Cachia A, Dupont C, Palmis S, Menu I, Auzias G, Sein J, Coulon O, Longcamp M (2025) The sulcal patterns of the occipito-temporal and anterior cingulate cortices influence reading and writing in children and adults. Cereb Cortex 35:bhaf145.

      Cachia A, Roell M, Mangin J-F, Sun ZY, Jobert A, Braga L, Houde O, Dehaene S, Borst G (2018) How interindividual differences in brain anatomy shape reading accuracy. Brain Structure and Function 223:701–712.

      Del Mauro G, Del Maschio N, Abutalebi J (2022) The relationship between reading abilities and the left occipitotemporal sulcus: A dual perspective study. Brain and Language 235:105189.

      Ferrer E, McArdle JJ, Shaywitz BA, Holahan JM, Marchione K, Shaywitz SE (2007) Longitudinal Models of Developmental Dynamics Between Reading and Cognition From Childhood to Adolescence. Developmental Psychology 43:1460–1473.

      Peng P, Kievit RA (2020) The Development of Academic Achievement and Cognitive Abilities: A Bidirectional Perspective. Child Development Perspectives 14:15–20.

      Reuter M, Schmansky NJ, Rosas HD, Fischl B (2012) Within-subject template estimation for unbiased longitudinal image analysis. NeuroImage 61:1402–1418.

      Roell M, Bellon E, Polspoel B, Declercq M, De Smedt B (2022) Investigating the association between variability in sulcal pattern and academic achievement. Sci Rep 12:12323.

      Ünal ZE, Greene NR, Lin X, Geary DC (2023) What Is the Source of the Correlation Between Reading and Mathematics Achievement? Two Meta-analytic Studies. Educ Psychol Rev 35:4.

      Yao JK, Mitchell JL, Davison A, Yeatman JD (2026) Sulcal anatomy of ventral temporal cortex and reading development. :2026.04.06.716640 Available at: https://www.biorxiv.org/content/10.64898/2026.04.06.716640v1.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      In this work, T. Wijerathne et al. investigated and reported the agonistic effect of Yoda1 and Yoda2 over PIEZO2 function using patch clamp electrophysiology, Ca2+ imaging, and molecular dynamics. They find that Yoda1 sensitizes PIEZO2 to membrane tension, can induce Ca2+ influx, and decreases its inactivation to a lesser degree than it does to PIEZO1 channels. Additionally, their data shows that Yoda2 sensitizes PIEZO2 channels to membrane indentation to a greater extent, but it has a weaker effect on channel inactivation than Yoda1. Interestingly, they report that a mutation in a conserved arginine between PIEZO channels can be used to abolish PIEZO1mediated Ca2+ flux in response to Yoda molecules. As a whole, the results presented here should be put into perspective against previous and future works involving systems where both PIEZO1 and PIEZO2 might be expressed. This is especially true for works where Yoda1 has been used as a basis for determining the absence of PIEZO2.

      Strengths:

      The authors use multiple techniques to investigate how Yoda molecules affect the three most important biophysical aspects of PIEZO channels that, when changed, result in pathophysiological responses: a) sensitivity to mechanical stimuli, b) Ca2+ entry, and c) channel inactivation. Lastly, they find a specific amino acid/region that could be exploited for drug design and/or development.

      Weaknesses:

      The methods and discussion sections are lacking enough detail to fully evaluate the findings and put them into perspective, respectively.

      We have included new results, expanded our discussion, and added additional details in our Methods section.

      Reviewer #2 (Public review):

      Summary:

      This manuscript challenges the long-standing assumption that Yoda1 and Yoda2 are PIEZO1selective activators. Using patch-clamp electrophysiology and calcium imaging in HEK293TΔPZ1 cells overexpressing PIEZO2, the authors demonstrate that Yoda1 potentiates PIEZO2 stretch activated currents to a similar extent as PIEZO1 and slows PIEZO2 poking-current inactivation (albeit with lower efficacy). They further show that the more potent analog Yoda2 affects PIEZO2 at nanomolar concentrations and use mutagenesis and molecular dynamics simulations to propose that Yoda2's benzoic acid group forms a transient salt bridge with R1724 in the putative Yoda binding pocket, explaining its enhanced potency.

      Strengths:

      The authors are established Piezo/biophysics experts; the study is highly important, technically competent, and carries significant implications for the reinterpretation of prior work that used Yoda compounds as PIEZO1-selective probes.

      The core finding that Yoda1 modulates PIEZO2 stretch currents is convincing and important. However, several conceptual, methodological, and presentational issues need to be addressed before acceptance, as detailed below.

      Weaknesses:

      (1) The abstract states that Yoda1 potentiates PIEZO2 "as efficaciously as PIEZO1." This claim is accurate only for stretch currents and single-channel open probability, but the paper itself demonstrates important asymmetries: i) Yoda molecules slow PIEZO2 poking-current inactivation ~2-fold, versus ~5-10 fold for PIEZO1 (Figure 3b and ref #60). ii) Spontaneous Ca<sup>2+</sup> entry via PIEZO2 requires non-physiological conditions (high extracellular Ca<sup>2+</sup>, hypertonic solutions) that are unlikely to occur in native cells. The abstract should be revised to clearly qualify where equivalence holds and where efficacy differences exist. IMO, the current wording risks overcorrecting the historical bias (PIEZO1-only) by going too far in the other direction.

      We have changed our language throughout the manuscript to convey more accurately differences of Yoda agonism between the two Piezo homologs.

      (2) Related concern: the PIEZO2 Ca<sup>2+</sup> signal in Figure 2 is only detectable using a Ca<sup>2+</sup>-boosted solution (CBS ie 30 mM Ca<sup>2+</sup>). Physiological extracellular Ca<sup>2+</sup> and cells normally do not experience sustained hypertonicity at these magnitudes. The authors should explicitly clarify that the practical implication of their findings is primarily for electrophysiological (patch-clamp) experiments and that the Ca<sup>2+</sup> imaging caveat applies only under amplified conditions. Specifically, the authors should state that in standard Ca<sup>2+</sup> imaging assays with physiological buffers, PIEZO2 is unlikely to confound Yoda1 results.

      Agreed. As mentioned above, we have modified our wording to convey this point more clearly.

      Related point: Can cytochalasin D (CytoD) restore a Yoda1-dependent Ca<sup>2+</sup> signal in physiological saline? This would help determine whether the weak PIEZO2 response is primarily a membrane tension issue (cytoskeletal tethering) versus intrinsically lower channel expression or permeability. The authors already have tagged PIEZO1/2 constructs and could, in principle, normalize by surface expression.

      We have repeated our acute pharmacological treatment in cells pre-treated with CytoD (or 0.5% DMSO vehicle control). These experiments were done in normal saline solution. We found that Yoda1 produces a very small (but significant) calcium influx in cells treated with CytoD. This result strengthens our conclusion that Yoda1 is capable of producing an activatory effect on Piezo2 in absence of external mechanical stimulation - albeit this effect is very small and only detectable in non-physiological (calcium-rich or destabilized cytoskeleton) conditions. It remains difficult to definitely conclude about why Yoda molecules exert different agonistic effects. We can only discuss possibilities. Differences in Ca2+ permeability is unlikely to contribute to this difference, as pore properties and selectivity for monovalent ions are similar between the two channels (see PMID: 39543876). Slight differences in how Yoda bind the Yoda binding region could explain why Yoda1 robustly modulates Piezo2 stretch currents but fails to produce robust calcium influx, as recent work suggests that these two agonist effects may originate from two distinct Yoda binding poses in this region (PMID: 38060566; PMID: 41402296). Piezo2’s intrinsically high threshold for stretch-activation could also represent a contributing factor, as figures 1e-f show that Piezo2’s midpoint activation pressure in the presence of Yoda1 (about -30 mmHg vs. -60 mmHg) might still be too high to enable robust Yoda-induced activation at the resting membrane tension of the cell. Since Piezo1 has been consistently shown (by us and others) to be expressed at a higher level than Piezo2 in transfected HEK293 cells (e.g., PMID: 20813920; PMID: 32227462, PMID: 37102984; PMCID: PMC13423835), we have not replicated these experiments with Piezo1. We have modified our manuscript to include these new results and discussion.

      (3) The mean inactivation tau values for wild-type PIEZO2 poking currents in both DMSO and Yoda1 conditions (Figure 3b, approximately 15-40 ms range) appear substantially higher than values reported in published literature (typically 5-10 ms; eg, PMID: 20813920). This discrepancy needs to be addressed.

      This discrepancy likely arises because inactivation kinetics of Piezo1 and/or 2 poking currents can be modulated by many biological and experimental variables that are difficult to control. Biological variables include membrane potential (PMID: 20813920), extracellular pH (PMID: 25561736), temperature (PMID: 35858335; PMID: 31413193), the presence of modulatory proteins (PMID: 37590348) and extracellular matrix (PMID: 28164706). Experimental variables include the mechanics of probe displacement (velocity and impact angle) and the precise positioning of the time-cursor near the peak current for exponential fitting. In addition, the decaying portion of Piezo poking currents is likely contributed by both inactivation and deactivation, as a recent study demonstrates relaxation of the poke stimulus during mechanical indentation in N2a cell (PMID: 42649207). Cellular viscoelastic properties and cytoskeletal organization are thus anticipated to dictate how fast this relaxation occurs, influencing the proportion of inactivating and deactivating currents in poking recordings. Since this point deviates from our main goal - to test an effect of Yoda on channel kinetics measured side-by-side – we prefer not to discuss it.

      (4) The authors perform all MD simulations on a truncated PIEZO1 model and justify this choice by noting that the Yoda binding region is highly conserved between homologs. This is a reasonable and defensible starting point given the availability of well-validated PIEZO1 simulation set ups in their lab. A few points are nonetheless worth addressing: While PIEZO2 simulations are not strictly required, the authors are encouraged to briefly discuss whether any long-range structural differences between PIEZO1 and PIEZO2 (outside the binding site itself) could influence Yoda2 binding dynamics, particularly in light of the chimera data showing that PIEZO2 sequence in repeat A abolishes Yoda1 sensitivity. This reviewer still doesn't understand the reason behind this discrepancy despite it being acknowledged in the text.

      We have now conducted three replicas of all-atom MD simulations of the Yoda2-bound PIEZO2 system. The new results show that the equivalent Arg residue in PIEZO2 (R2029) also forms a salt bridge with Yoda2, consistent with our observations from the Yoda2-bound PIEZO1 simulations. Taken together, these simulation results seem to point to the fact that Yoda molecules bind to a similar region in both PIEZO1 and PIEZO2. The lack of Yoda1-sensitivity in the chimera is quite puzzling, and we can only speculate about why. The swapped chimeric region includes 103 residues, 21 of which are non-conserved between PIEZO1 and PIEZO2 and distributed around the binding region (PMID: 29795280). These mutations could collectively and allosterically alter the binding free energy landscape in a manner that either 1) strongly reduce Yoda binding affinity or 2) equalize Yoda binding affinity for both curved and flat conformations, effectively rendering Yoda molecules silent binders (similar to how we previously described Dooku1 binding to Piezo1 PMID: 38060566).

      Another MD-related comment is that three simulation replicas (which is impressive for such a big system) show markedly different salt bridge occupancy (82.6%, 49.7%, 99.8%; stated in the text). This wide variation suggests incomplete sampling in at least one replica. The authors should provide RMSD plots for ligand and protein backbone to assess convergence and possibly discuss whether the 49.7% replica represents a genuinely distinct binding mode or incomplete equilibration.

      We have extended PIEZO1-Yoda2 replica #2 from 600 to 1400 nanoseconds. This replica shows that the salt-bridge turned ON and OFF during the simulation because the Arg side chain tends to flip. This flipping behavior is evident in the 20 µs Replica #1 (Figure 6c). In Figure 6-figure supplement 1, we analyzed our previous five replicas of MD simulations using the PACE force field. We show that the angle distributions indeed vary between replicas and subunits at the timescales currently affordable by MD technique for this large system. Therefore, it is not too surprising that the salt bridge occupancy differs between three all-atom simulations. We now provide RMSD of ligand and protein backbone for each Replica as Figure 6 supplement 1. The time evolution of Yoda2 binding poses across all simulation replicas are now illustrated in Figure 6-figure supplement 2, which shows that Yoda2 is mobile, yet remain stable in this overall hydrophobic binding site, consistent with our previous report (PNAS2023 PMID: 38060566). We also added all corresponding analysis of Yoda2-PIEZO2 in the same figures.

      (5) The Discussion proposes that PIEZO2's weaker Ca<sup>2+</sup> response to Yoda1 could partly reflect lower membrane expression. Since the authors already have fluorescently tagged PIEZO1 and 2 constructs, a simple fluorescence intensity comparison between the two (acknowledging it would reflect total rather than surface expression) could provide at least indirect support for this claim. Alternatively, if such a comparison is not feasible, the authors may consider removing membrane expression from the list of proposed explanations or explicitly acknowledging that this remains unsubstantiated speculation. The max poking currents may somewhat and roughly indicate the level expression difference too, if done exactly side by side.

      PIEZO2 expression is known to be lower than PIEZO1 in heterologous systems (PMID: 20813920; PMID: 32227462, PMID: 37102984; PMCID: PMC13423835), hence we have not attempted to test if this was the case with our tagged constructs.

      (6) The abstract or concluding remarks should highlight that Dooku1 is not PIEZO1-selective in its agonist-like action on PIEZO2, and that Cmpd15/Cmpd64 appear to be better PIEZO1-selective tools. This nuance is buried in the Results section.

      We now list these results in the abstract.

      (7) The authors should not cite PMID 31015490. Clearly, any work on MCC13 is confounded by the overwhelming expression of PIEZO1 (PMID: 42084270). Instead, the authors should also cite the literature from others who have clearly recorded stretch currents from PIEZO2 before the cited studies (eg, PMID: 37590348).

      Agreed!

      Reviewer #3 (Public review):

      Summary:

      The manuscript reports that Yoda1 and Yoda2 agonize PIEZO2 in a manner similar to PIEZO1, increasing open probability and stretch sensitivity, but the mechanism underlying this sensitivity is incomplete. Mutagenesis was shown exclusively in PIEZO1, with no corresponding mutagenesis in PIEZO2, so the proposed mechanism in PIEZO2 is inferred by homology rather than directly tested. All experiments use mouse PIEZO2, and the human ortholog should be used before generalizing the proposed reinterpretation of the field.

      Strengths:

      The pressure-clamp electrophysiology demonstrating a shift in half-activation pressure for PIEZO2 is compelling evidence in support of the central claim.

      Weaknesses:

      (1) In the single-channel recordings (Figure 1a), it's unclear how many channels were present in those patches. After applying -60 mmHg pressure, multiple channels would be activated (as seen in Figure 1e). The number of channels in the patch and their inactivation rate could significantly influence the open probability in such experiments. To overcome this, in the original Yoda1 article (Syeda, Ruhma, et al. eLife 2015), no additional pressure was used.

      To clarify the confusion, we record single-channel PIEZO2 currents less than 24 hrs after transfection and record macroscopic PIEZO2 currents 2-3 days after transfection. Hence, unlike the cited study, our single and macro currents are obtained from different patches. When patching cells for single recordings, most patches do not show any mechano-currents and those that do typically show only one current level of single-channel conductance through the recording, even when the patch is highly pressurized.

      Additionally, the reported open probability comparison (n=7 Yoda1 vs n=17 DMSO patches) has an SEM nearly as large as the effect itself (0.30 {plus minus} 0.11), consistent with a small number of outliers driving this. The underlying mean open and shut times are reported without any statistical test; only the derived open probability receives a p-value. Additionally, in Figure 1a, the Yoda1 condition noise is different from the control. This should be stated if noise filtering was applied and how, given that this could affect open probability analysis.

      This is a fair point. We have removed two outliers and have performed statistical analysis on mean dwell times. The effect of Yoda1 is still highly significant. We have replaced current traces with two of similar noise levels. We acquired all single-channel current traces at 100kHz, filtered them at 5kHz, and displayed them at 500 Hz.

      (2) The calcium imaging data in Figure 2 raise significant concerns regarding the chemical activation claim. The calcium-boosted solution (30 mM Ca2+) is not physiological and appears to be generally stressing cells rather than specifically activating PIEZO2: the control condition under CBS already shows an elevated signal, consistent with cells being unwell at this calcium concentration, and adding Yoda1 on top of this shifted baseline raises further questions about specificity rather than confirming it. Separately, it is unclear why DMSO alone produces measurable PIEZO2-associated calcium influx in HBSS, a result that is not addressed in the text. Figure 2 should clearly indicate when DMSO/Yoda1 perfusion was initiated, and y-axis labels are missing from panels A and B.

      We agree and have toned down our chemical activation claim, insisting that this activation is very weak in absence of external mechanical stimulus, being only detectable under extreme, non-physiological conditions. We also re-analysed our data (and added fluorescence scale bars, thank you) showing time-course and scatter plots from the same cells in Figure 2a. We think the “bump” seen upon DMSO perfusion in PIEZO2 cells could be amplified by the low expression of GC6 in these cells. We now discuss this point in our revisions.

      (3) In the poke experiments, an activation threshold should be calculated and reported, and amplitude data (e.g., peak current versus indentation depth) should be shown rather than only inactivation tau values. It is also unclear why mClover3- and N-GFP-tagged constructs were used in these experiments, since electrophysiological recording already confirms channel expression without requiring a fluorescent tag.

      Valid point, we are now comparing peak currents for different poking distances. We have removed our Tau analysis for our tagged-PIEZO2 clones.

      (4) For inactivation kinetics (Figure 3b), the authors use unpaired comparisons across separate cells, whereas the deactivation experiments (Figure 3c) use paired; it should be applied to the inactivation experiments as well. Deactivation kinetics for PIEZO2 itself should be shown.

      These experiments have different goals which do not require using the same protocol. Deactivation kinetics experiments were used for the chimera because this parameter was shown by us to be the most sensitive to Yoda1. Hence, if a Yoda modulation exists, but is hard to detect in the chimera, using this protocol with paired samples provide us with the highest detection sensitivity. This level of sensitivity was not needed to detect an effect of Yoda1 on PIEZO2.

      If the claim is that Yoda1 acts on PIEZO2 through the same mechanism proposed for PIEZO1, then a PIEZO1/2 chimera should be expected to show a corresponding effect on deactivation tau; instead, this chimera is reported as completely Yoda1-insensitive despite both parental channels being Yoda1-sensitive, as shown in this study.

      This discrepancy is acknowledged in the text. We do not know why the chimera is Yoda insensitive and can only speculate at this point. Of note, one must acknowledge that this chimeric swapping introduces 21 amino acid changes (vs. WT PIEZO1) which may have profound allosteric effect on binding affinity and/or efficacy. MD studies would be useful to explore this possibility in a future study.

      (5) Given that this reflects a different experimental paradigm for Yoda EC50, PIEZO1 should be included within Figure 4b. Additionally, EC50 bar plots should be present on this figure.

      Showing EC50 plots here is not possible because each cell was exposed to only one dose of Yoda1 (unpaired measurements). We have included a Yoda1 dose-response curve against PIEZO1 inactivation Tau from our prior study (PMID: 35858335) for comparison as a Figure Supplement.

      The inactivation time constant for PIEZO2 without Yoda1 is inconsistent across figures, below 20 ms in Figure 3b but above 20 ms in Figure 4c.

      As explained above in our answer to Reviewer #2, these inconsistencies likely occur because PIEZO inactivation kinetics are susceptible to modulation by a number of biological and experimental factors that are not easily traceable, making it difficult to define absolute channel kinetics.

      (6) Finally, the modeling is performed exclusively on PIEZO1, whereas the manuscript's central focus is PIEZO2. It is therefore unclear whether the proposed structural mechanism, including the basis for Yoda2's reduced efficacy on PIEZO2, can be directly extrapolated to PIEZO2.

      We have now conducted three replicate all-atom MD simulations of the Yoda2-bound PIEZO2 system. The new results show that the equivalent Arg residue in PIEZO2 (R2029) also forms a salt bridge with Yoda2, consistent with our observations from the Yoda2-bound PIEZO1 simulations. However, the current simulations do not allow us to distinguish differential efficacy of Yoda2 toward PIEZO1 versus PIEZO2. The reduced efficacy of Yoda2 on PIEZO2 may instead arise from differences in its binding affinity for the open versus closed conformations, or from contributions of cellular components that are not represented in our MD simulations, such as the cytoskeleton.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      Main:

      (1) Adding more depth and detail to the methods section will help others replicate the findings.

      Agreed.

      (2) Methods: line 325. Describe the way each compound was prepared for each concentration without undissolved particles. Avoid using the phrase "as described before" in the methods section.

      Compounds were dissolved in DMSO and simply diluted in recording solution at the time of experiments with vortex mixing.

      (3) Figure 1B (comparison of open probability): only three points out of 7 (with Yoda1) seem outside the data range of the control (DMSO). It seems very unreliable for an agonist. Moreover, in Figure 1F, the data seem very noisy. I would suggest adding more n.

      We have eliminated two outliers and reanalyzed our data, showing statistics for mean dwell times and open probability.

      (4) The authors should add to the "Yoda1 activates PIEZO2 in the absence of external mechanical stimulus" section (or the methods) how perfusion of Yoda1 was applied.

      We used manual pipetting.

      (5) Lines 165 - 171. This part should be moved to the discussion and expanded on. Particularly since the reference they allude to comes from the same group.

      This discussion part is needed to introduce the chimera experiments and thus should remain in Results.

      (6) Figure 3B. The noise range of the time constants of inactivation is a lot. Specially for transfected cells. I would suggest a couple of sentences explaining why the authors think this happens.

      This discussion is now included.

      (7) Figure 4C. Tau inac of DMSO control seems very high when compared to others. I would suggest a couple of sentences explaining why the authors think this happens.

      One difference is that DMSO concentration here is higher (0.25% vs 0.075%) to match the higher concentration of Yoda1 tested. Inactivation kinetics are subject to modulation by many parameters; hence we focus on side-by-side comparisons instead of absolute values.

      (8) Line 213. Which standard binding equation? Include in the methods.

      Done.

      Rethink calculating the EC50 with dose responses that saturate. Figure5C. Are these absolute or relative EC50s?

      EC50 of mutants are normalized to WT.

      (9) Discussion: "Our discovery that Yoda1 modulates PIEZO2 stretch currents as effectively as PIEZO1's strongly suggests that some of the reported biological roles attributed to PIEZO1 using this agonist could be (at least partly) transduced by PIEZO2. For instance, our discovery seamlessly reconciles the puzzling fact that reducing PIEZO2 expression in cells that co-express PIEZO1 also reduces the effects of Yoda1 (49, 76, 77). Along." In the referenced works (49, 76, and 77) its not checked if PIEZO1 levels remain the same when PIEZO2 was knocked out. Here, the authors should discuss this possibility.

      Good point!

      Minor:

      (1) Indicate in the figure legends, result or methods section, what the error bars represent.

      Done.

      (2) Indicate the p-value for Figure 1B.

      Done.

      (3) Figure 2. Include the ionomycin value that each group is normalized against.

      We provide now vertical scale bars for all samples.

      (4) Why not use PIEZO2 for the MD simulations?

      Done.

      Reviewer #2 (Recommendations for the authors):

      Minor comments

      (1) In the Abstract: The sentence "Although a structural framework for PIEZO1 activation by Yoda1 exists" may be confusing for readers outside the field. The authors may mean "mechanistic" or "computational" framework. Please clarify or reword.

      We have reworded the abstract.

      (2) Residue number in abstract: The abstract states "a conserved arginine in the Yoda binding site" without identifying it. Please add the residue number (R1724 in mouse PIEZO1) for clarity.

      Done

      (3) Figure 1 legend or in the method: recording mode and filter settings: The figure legend should explicitly state that single-channel recordings were obtained in cell-attached mode, and should report the filter frequency (kHz) and sampling rate used for idealization. This is essential for readers to evaluate dwell-time analysis.

      Done, but details are in the method.

      (4) Several instances throughout the text use "native" where "naïve" is clearly intended.

      Corrected, thank you.

      (5) The statement that PIEZO2 requires more mechanical force than PIEZO1 (~−60 vs ~−40 mmHg P1/2) should be interpreted cautiously without this information, and the authors should clarify whether pipette geometry was controlled between PIEZO1 and PIEZO2 experiments.

      We have shown that PIEZO2 requires more force to be opened by membrane tension relative to PIEZO1 using MscL gating as a tension-calibration system (PMID: 41703062). Pipette geometry is consistent for each type of experiment (macroscopic or single-channel recordings). We have expanded our Methods.

      (6) The finding that Dooku1slows PIEZO2 inactivation similarly to Yoda1 is striking and is currently underplayed. This raises important questions: Does Dooku1 elicit Ca<sup>2+</sup> entry in PIEZO2-expressing cells? It could at least be discussed further in the text.

      Likely not, since Yoda-induced calcium influx is very weak and requires non-physiological conditions to be detectable. But this is worth trying at some point.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      (1) Where the manuscript still has potential for improvement is the discussion, which in its current form does seem slightly self-contained and does not fully integrate the findings of previous studies on Drosophila rhodopsin7. As the introduction specifically points out that previous findings have been contradictory, this seems like a missed opportunity.

      We thank the reviewer for this helpful suggestion and agree that the previous version of the Discussion did not sufficiently integrate earlier studies on Drosophila RH7. In the revised manuscript, we have expanded and restructured the discussion to explicitly incorporate key studies, including those by Ni et al. (2017), Senthilan et al. (2019), Lazopulo et al. (2019), and Meyerhof et al. (2024). In Discussion 5.4, we directly address similarities and discrepancies, such as differences in reported expression patterns, behavioral phenotypes, and experimental conditions. We use these inconsistencies to better position our findings and propose that RH7 acts as a modulatory photoreceptor with context dependent effects, which may explain the variability observed across studies. These changes provide a more integrated and coherent view of RH7 function.

      (2) Similarly, the manuscript currently lacks a discussion of the possible relevance of rhodopsin7 (and other non-visual light receptors in other organisms) in the context of a species' environment and lifestyle, i.e., what is the relevance/benefit of having rhodopsin7 in the fly's everyday life?

      We agree that the ecological relevance of RH7 deserved a more detailed discussion. According to the suggestion, we have now expanded the discussion to address the ecological and functional relevance of RH7 in the context of environmental light conditions and species-specific lifestyles (see Section 5.5). In particular, we now highlight that RH7 is frequently retained in species inhabiting sun-exposed environments and that its presence correlates with conditions of high light exposure, especially during early developmental stages. Together with our functional data in Drosophila, showing a role of RH7 in light dependent behavioral flexibility and circadian regulation, this supports the idea that RH7 contributes to the detection and integration of environmental light cues under natural conditions.

      (3) An additional point concerns the title and abstract, which postulate rhodopsin7 roles in contrast vision as well as motion and brightness perception. Contrast remains poorly defined in the text, leaving it ambiguous whether it refers to bright/dark contrasts, e.g., along edges, or the temporal contrast that results from dark pulses (startle response). While the latter seems to apply here, the former is likely more intuitive. Thus, this aspect should be rephrased (also in the title) or properly clarified early on.

      Thank you for this comment. We agree that the term “contrast” was ambiguous, as it can refer to spatial contrast (e.g., edge detection) or temporal contrast (changes in light intensity). Our study focuses on temporal contrast, such as light-dark transitions. Accordingly, we have revised the manuscript, replacing “contrast” with the more precise term “temporal changes in light intensity” throughout the relevant sections. In addition, to clarify this further, we conducted additional experiments with graded changes in illumination. These showed that Rh7<sup>0</sup> mutants have reduced responses compared to wild type in both abrupt (e.g. 30→0 µW/cm<sup>2</sup>) and gradual (e.g. 30→5 µW/cm<sup>2</sup>) transitions, indicating that RH7 contributes to detecting temporal changes in light intensity.

      (4) Regarding motion detection, this is backed up by the optomotor response results, but the findings stand somewhat isolated from the other results, lacking a clear connection aside from general visual processing.

      We have clarified the connection between motion detection and the other visual assays. In the Results section (4.7), motion detection is now described as “relying on the processing of spatiotemporal changes in luminance across the visual field,” explicitly linking it to general luminance-based visual processing. In the Discussion (5.3), we added the concise statement “These computations rely on changes in light intensity over space and time” to further emphasize this connection. We believe these changes make the relationship between the optomotor results and the other assays clearer and easier to follow.

      (5) Lastly, brightness perception is mentioned in the abstract, but never again, possibly due to inconsistent phrasing throughout the manuscript.

      We agree that the terminology was not used consistently throughout the manuscript. To improve clarity and consistency, we replaced the term "brightness perception" in the Abstract with "temporal changes in luminance", which more accurately reflects the focus of our study.

      Reviewer #2 (Public review):

      (1) It is not that clear to me what rhodopsin does in terms of circadian regulation (even though its function might be circadianly regulated). The clear role in the light/dark distribution of activity might not be circadian per se, but mostly light/dark- driven and there is no evidence here for a role in the entrainment of the clock.

      We thank the reviewer for this important point. We agree that our current data does not provide sufficient evidence for a direct role of RH7 in circadian regulation or clock entrainment. In this revision, we have examined LD (12:12) behavior in more detail and report changes in several activity parameters (Figure 3A). While these differences could in principle involve circadian mechanisms, our experiments do not allow us to distinguish between circadian effects and acute light-driven modulation of locomotor activity. We therefore present these results without interpreting them as evidence for a circadian function of RH7, and instead focus on light-driven behavioral effects under LD conditions.

      (2) The authors should cite Lazopulo, which nicely shows that Rh7 has an important role in peripheral neurons to allow flies to escape from blue light (see below).

      We thank the reviewer for pointing this out. We have now cited Lazopulo et al. (2019) at multiple relevant points in the manuscript, specifically regarding atypical RH7 expression in peripheral neurons, the functional effects of RH7 outside the LNvs, and its protective role in light-dependent behavior (discussion 5.1, 5.4, and 5.5). We believe these additions ensure that the manuscript accurately reflects the existing literature and appropriately acknowledges the contribution of Lazopulo et al. to understanding RH7 function.

      (3) The finding showing that Galphaz but not Galphaq can trigger signaling from light-excited Rh7 is a very intriguing finding to better understand Rh7 function. Since Galphaz is related to Gi/o, it would be interesting to test those, for example, by expressing RNAi with Rh7gal4 and testing the Light-dark or light-off response behavior.

      We agree that testing additional Gi/o-type Gα subunits would be highly informative for further dissecting RH7 signaling. However, in our preliminary experiments, RNAi-mediated knockdown of Rh7 itself did not result in a robust or statistically significant behavioral phenotype under our conditions. This is consistent with previous reports that RNAi in Drosophila can show variable efficiency and often results in incomplete knockdown, leading to weak or undetectable phenotypes (Dietzl et al., 2007; Green et al., 2014; Perkins et al., 2015). Given these limitations, we did not further pursue RNAi-based approaches targeting additional Gα subunits in the current study. Instead, we complemented our experimental findings with additional comparative and in silico analyses using FlyPredictome, which support a potential association between RH7 and Gi/o-type signaling components. These results have now been incorporated into the revised manuscript (Discussion 5.2). We agree that further functional validation of Gi/o-type G protein involvement, for example using genetic mutants, interaction assays or alternative approaches, would be an important direction for future studies.

      (4) The change in the locomotor activity distribution between light and dark in LD conditions provides a nice assay for Rh7 function. Since Lazopulo et al. (2019) have shown that wildtype but not Rh7 mutants do escape from blue light, it would be important to compare and discuss these LD behavior data with the Lazopulo results. Precisely, is this nighttime preference linked to blue light?

      To address this point, we conducted additional experiments, which are now included in the supplementary materials. Instead of the usual white light–dark (LD) cycles, we tested blue light–dark and green light–dark conditions. However, we observed only minor differences and no significant shift in light preference, as reported by Lazopulo et al. (2019). A likely explanation for this discrepancy is the difference in experimental light intensity. In our assays, we used moderate light intensities, approximately 30 µW/cm² for white light and 5–6 µW/cm<sup>2</sup> for color lights. Lazopulo et al. used substantially higher light intensities (2480 µW/cm<sup>2</sup> for white light and approximately 600 µW/cm<sup>2</sup> for colored lights). Even the higher intensities used in our arrhythmia experiments (~120 µW/cm<sup>2</sup>) remained well below those applied in their study.

      Importantly, the behavioral paradigms differ: Lazopulo et al. assessed acute light preference/avoidance, whereas our experiments quantify locomotor activity distribution across the day under LD conditions. The latter is strongly shaped by circadian regulation and integrates multiple internal and external factors. Therefore, wavelength-dependent avoidance behavior observed under acute conditions may not directly translate into changes in daily activity patterns under moderate LD conditions. Although we cannot directly replicate the strong avoidance of blue light or preference for green light described by Lazopulo et al., our results do not contradict those of Lazopulo. The reduced activity during the midday phase in the wild-type flies, which is less pronounced in Rh7<sup>0</sup>, may suggest a potential protective function or preventive behavior in the WT flies. Since the moderate light intensities used in our LD assays are much less aversive, no strong wavelength-dependent preference was observed.

      (5) However, the paper would be strongly reinforced by correlating this with the LD behavior. The LD phenotype should be tested in flies with Rh7 expression rescued under Rh7gal4 control (as done for the startle response). This is important to show whether the expression pattern is likely responsible for the described Rh7 function in LD.

      We agree that assessing LD behavior in flies with Rh7 expression rescued under Rh7-Gal4 control is important to link expression pattern to function. We have now performed these experiments. The Rh7-Gal4–driven rescue results in a substantial recovery of the LD locomotor phenotype, bringing it closer to control levels than the UAS-empty condition. While the rescue does not fully reach wild-type levels, the observed trend and significant differences across specific parameters support a functional contribution of Rh7-expressing cells. These data are now included in Figure 5C and described in section 4.6.

      (6) If L5 and or M11 drivers are available, they should be used to rescue Rh7? Since expression in some clock neurons is shown, the rescue experiment should also be done with a clock neuron driver.

      Thank you for this helpful suggestion. We agree that cell type-specific rescue using L5- and/or Mi1 drivers, as well as clock neuron drivers, would be highly informative.

      However, implementing these experiments is currently not straightforward. Targeting these neuronal populations requires the use of split-Gal4 driver lines, which can differ in expression strength and are therefore not quantitatively comparable across combinations. In addition, the required genotype would be highly complex: the two split-Gal4 components will be located on separate chromosomes, the UAS-Rh7 transgene is on another chromosome, and the Rh7<sup>0</sup> mutation resides on the third chromosome. Combining all necessary elements in a single line would therefore require extensive genetic recombination. Importantly, we aim to avoid introducing mutations or markers on the X chromosome, as these are known to influence behavioral readouts. However, many of the available lines are in a white<sup>-</sup> background, and assembling the full rescue genotype while maintaining a controlled genetic background across all chromosomes is therefore particularly challenging. For these reasons, we have not pursued these rescue experiments in the current study but consider them an important direction for future work.

      (7) In the same line, can the LD phenotype (or startle response phenotype of Figure 4) be restored by expressing Rh7 under ppk control, as shown for the blue light avoidance phenotype by Lazopulo et al?

      We thank the reviewer for this suggestion. However, in our experiments, we did not observe a blue-light avoidance phenotype comparable to that described by Lazopulo et al. (2019). Since this behavioral effect did not occur in our assay, we did not perform rescue experiments with ppk-regulated Rh7 expression. As previously discussed, the absence of pronounced blue light avoidance in our experimental setup is likely due to the moderate light intensities we used, which are significantly lower than those applied in Lazopulo et al.

      Therefore, a ppk-mediated rescue would not be meaningful in our context.

      (8) Finally, the Rh7 "darkfly" rescued flies should be tested in LD.

      We agree that testing Rh7Darkfly rescue flies under LD conditions provides important insight into Rh7 function. We have now performed these experiments. The Rh7Darkfly rescue leads to a marked shift of the LD locomotor phenotype toward the Darkfly phenotype, with a stronger effect than observed in the Rh7 rescue lines. While the rescue does not fully recapitulate either wild-type or Darkfly controls, the observed trend supports a contribution of RH7 to the modulation of LD behavior in this genetic background. These data are now included in Figure 5C.

      Reviewer #3 (Public review):

      (1) The authors should clarify exactly what tissues were taken for the comparative qPCR. This is particularly interesting in terms of the retina. Since Rh7 appears not to be expressed within the photoreceptor cells of the retina, this raises the important question as to which cells it is expressed in. To address this important question, it would also be helpful to include an expression analysis of the retina itself (by extending the RH7-GFP expression patterns and/or adding HCR in situ of the ommatidia array). The cell types of the retina are very well classified, and some evidence already exists for Rh7 expression in support cells (e.g., Charlton-Perkins et al., (2017); PMID: 28562601). This study has a unique opportunity to investigate this further by adding these critical data for a more complete picture of Rh7.

      We thank the reviewer for this helpful comment. We have now clarified in the Materials and Methods exactly which tissues were collected and analyzed for the comparative qPCR experiments. Regarding Rh7 expression in the retina, in our hands, we did not detect signals in retinal support cells, likely due to low expression and masking by autofluorescence. However, low Rh7 mRNA levels detected by qPCR in retinal tissue, together with the faint staining reported by Kistenpfennig et al. (2017), suggest that expression in these cells is possible. We have added this clarification, along with the observation by Lazopulo et al. (2019), who reported Rh7 expression in multidendritic neurons, to the Discussion (section 5.1) to provide a more complete overview of RH7 localization.

      (2) Mammalian opsins should be included in the phylogenetic analysis illustrated in Figure 2A and indicate their position on the tree. This will allow readers to better put the authors' statements regarding the intermediate position of Rh7 into perspective. In addition, note that the distinction between red and deep red is easy to miss regarding the Rh7 cluster. Perhaps the authors could use a more distinct colour scheme, for example, orange and deep red.

      In the revised Figure 2A, we have included both mammalian melanopsins and lophotrochozoan opsins, which support our interpretation of RH7 as a primitive opsin. The color scheme has been updated to more clearly distinguish the different clades, and tardigrades are now represented with a red triangle rather than a separate color. These changes improve clarity and better highlight the intermediate phylogenetic position of RH7.

      (3) More details should be provided on the optomotor response experiments. Specifically, specifications of the frequencies used for the optomotor response are needed. Results show a relatively large level of variation, which may be due to different angular perspectives that flies may have had while viewing the stimulus. If possible, provide videos as examples, as they will make it clearer to viewers how much flies could move around in the setup (from the methods, it seems they could move within the 2.2 of the 3 cm diameter of the arena, which would lead to substantial differences in the visual angle of the viewed grating.

      We would like to thank the reviewer for this valid point. We agree that, due to the relatively simple design of our optomotor apparatus, the flies may have different viewing angles of the rotating grid. To illustrate this point, we have added representative video footage and further photographs of the experimental setup to the supplementary material. A more sophisticated optomotor apparatus that maintains a fixed viewing angle for the animals would certainly reduce experimental variability. Nevertheless, our current, simple setup yielded robust and statistically significant optomotor responses. To further strengthen the robustness of these results, we have increased the sample size from n = 20 to n = 30, thereby confirming the observed effects.

      Recommendations for the authors:

      Reviewing Editor Comments:

      (1) Claimed impact of rh7 on circadian regulation.

      As the data are presented at the moment, there is no evidence for a role in circadian regulation. At present, the data can be fully explained by the acute effects of light on behavior. Either remove the circadian from the text or consider specific entrainment and rescue experiments (see suggestions from Reviewer 2).

      We thank the editor for this important comment. We agree that the original version of the manuscript overinterpreted the role of RH7 in circadian regulation, and that the observed phenotypes can be explained by acute effects of light on locomotor behavior under LD conditions. In the revised manuscript, we have substantially restructured and clarified the interpretation of our findings. We now explicitly frame our results as light-driven behavioral effects under LD (12:12) conditions and have removed claims suggesting a direct role of RH7 in circadian entrainment. Furthermore, we have also added new rescue experiments, including Rh7-Gal4–driven Rh7 and Rh7Darkfly rescue, which provide further functional insight. These data show partial restoration of the locomotor phenotype and genotype-dependent shifts in activity patterns, supporting a modulatory role of RH7 in light-dependent behavior, while not directly addressing circadian clock function.

      We have further revised the text to ensure that conclusions remain strictly aligned with the presented data. In addition, we now emphasize that our data provide a basis for future studies exploring the potential role of RH7 in circadian entrainment.

      (2) Improved discussion section

      Both Reviewers 1 and 2 point out several aspects that should be better taken care of, especially embedding the new results into the context of the existing literature on rh7- Lazopulo et al 2019, Ni et al 2017, Meyerhof et al 2024 were particularly mentioned.

      We have addressed the reviewers’ suggestions by revising the Discussion section. We now refer to Meyerhof et al. (2024), Lazopulo et al. (2019), and Ni et al. (2017) at multiple points throughout the Discussion to better place our findings in the context of the existing literature on RH7 function. These references are now included in Sections 5.1, 5.4, and 5.5 of the Discussion.

      (3) The addition of vertebrate melanopsins, as pointed out by Reviewer 3 (they suggest mammalian, but consider adding other vertebrate and also lophotrochzoan proteins), in the phylogenetic tree will help to put the evolutionary ancestrality claim into a better perspective.

      We performed new bioinformatic analyses using RefSeq proteomes and carefully selected representative species across relevant clades to construct a balanced phylogenetic tree. These additions support our interpretation of RH7 as a primitive opsin and help place its intermediate phylogenetic position into better perspective. The results are presented in the revised Figure 2A, which now also includes mammalian melanopsins and lophotrochozoan opsins.

      (4) There were several questions raised on the qPCR and optomotor response experiments (Reviewer 3), as well as the definition of contrast (Reviewer 1).

      We have addressed the reviewers’ comments by substantially improving the clarity and presentation of the qPCR and optomotor response experiments, as well as the definition of “contrast.” We now provide a more detailed description of the qPCR analysis in the Methods section. For the optomotor response, we have added representative images and videos of the experimental setup to the Supplementary Material to increase transparency. We further clarified that the term “contrast” was previously used ambiguously and may refer to different concepts. In the revised manuscript, we now consistently refer to “temporal changes in light intensity” to specify that our study focuses on light-dark transitions. In addition, we included additional experiments with graded changes in illumination, which show reduced responses in Rh7 mutants compared to wild type under both abrupt and gradual transitions.

      (5) Supplementary Material needs sorting

      Accession numbers are in Supplementary File 2, not Supplementary File 1. Supplementary Material S2B is in Supplementary File 3 - this is really confusing. Supplementary Materials S3 is probably Supplementary File 1, and the phylogenetic tree shown there actually looks identical to the tree shown in Figure 2A of the main manuscript.

      We sincerely apologize for the confusion regarding the Supplementary Material numbering and file assignments. This issue likely arose during the upload process or transfer from the bioRxiv version of the manuscript. We have now carefully checked and corrected the Supplementary Files to ensure that all accession numbers, figures, and files are correctly assigned and consistently labeled throughout the revised submission.

      Reviewer #1 (Recommendations for the authors):

      (1) Here, I will address specific aspects of the manuscript, elaborating on the points mentioned in the public review and also listing detailed suggestions.

      As mentioned in the public review, the discussion could do a better job of relating the obtained findings to previous publications. For example, the paper by Ni et al. (2017) investigates the role of Drosophila rhodopsin7 in circadian light entrainment and its interplay with dcry, which seems relevant in the context of rhodopsin7 apparently being only present in CRY-negative clock neurons (except DN1a).

      We thank the reviewer for this helpful suggestion. We have expanded the manuscript to further explore the potential relationship between RH7 and DCRY. Specifically, we performed additional bioinformatic analyses, which are now presented in Results Section 4.1, and in discussion sections 5.4 and 5.5 addressing this aspect. While previous observations by Ni et al. (2017) and Kistenpfennig et al. (2017) have already pointed to a possible relationship between RH7 and DCRY, our phylogenetic analyses provide additional support for such a connection from an evolutionary perspective. Although our data do not yet allow us to infer the precise functional nature of this relationship, they further strengthen the evidence that Rh7 and DCRY are evolutionarily and functionally linked.

      (2) Another relevant paper by Meyerhof et al 2024 (doi:10.1073/pnas.2400964121) investigates the role of rhodopsin7 in shade preference and startle responses to short light pulses. The lack of shade preference and the altered startle response in rh7 mutants could be related to the authors' own findings on altered behavior in darkness. Further, the paper shows rh7 mutants to more rapidly return to baseline activity after a light pulse, which is somewhat reminiscent of the abrupt activity decrease in rh7 mutants at the start of the dark phase (18h). Generally, I recommend using the contradictory findings mentioned in the introduction as a starting point to describe where the new findings expand previous knowledge and possibly resolve contradictions.

      We thank the reviewer for this suggestion. We have revised the Discussion to integrate our findings with the available literature, including the recent study by Meyerhof et al. (2024), and explicitly compare similarities and differences between the reported phenotypes and our own observations.

      These aspects are now addressed in the newly added Section 5.5, where we discuss the evolutionary retention of RH7 in sun-exposed species and relate our phylogenetic findings to the emerging evidence that RH7 may play a conserved role in mediating responses to sun-exposed and shaded environments.

      (3) One specific aspect that does not fully convince me is the interpretation of the behavioral patterns concerning the short photoperiods (Figure 3C). The authors state that rh7 mutants lose the flexibility to shift their activity into the dark phase. However, drawing a vertical line through panels A, B, and C, it rather seems that activity peak times in wildtypes are fixed to 6-7h and 17-18h, while rh7 mutants do actually shift their peak activities with the decreasing photoperiod. A way of quantifying this would be to determine the phase differences between M- and E-peaks. It may also help to align plots in a way so that lightson of long and short photoperiod plots align. There is clearly a difference between WTs and mutants, but I would be more careful in calling this a reduction in flexibility.

      We thank the reviewer for this comment. We also noticed that the behavioral patterns under short photoperiods can be interpreted in different ways. Based on this comment, as well as the comments from the other reviewers and the handling editor, we decided not to further discuss the potential circadian component in this manuscript. We agree that additional and more targeted experiments will be necessary to better separate circadian effects from light-induced behavioral responses. These experiments are beyond the scope of the present study but will be important to further investigate the potential role of RH7 in circadian regulation. Therefore, we revised the manuscript to focus on the light-induced behavioral effects of RH7 and avoided drawing conclusions about circadian flexibility that are not yet fully supported by our data. In this process, we removed the data showing actvity under short days from the manuscript.

      Below, I list individual points according to their line number in the manuscript:

      (1) Line 1: Consider rephrasing the title based on the above comment regarding contrast.

      We have revised the title accordingly.

      The new title is: RHODOPSIN 7: An ancestral non-canonical photoreceptor shaping light-responsive behavior

      (2) Line 10: Vision is also used to adapt to the environment, so maybe change to "...also to otherwise/indirectly adapt behavior...".

      We have revised the sentence as suggested to clarify the non-image-forming role of light in behavioral adaptation.

      “Animals rely on light not only for vision but also to adapt behavior to their environment through non-image-forming pathways.”

      (3) Line 15: Consider rephrasing the title based on the above comment regarding contrast, motion, and brightness perception.

      We thank the reviewer for this suggestion. The title has been revised accordingly. The new title is: RHODOPSIN 7: An ancestral non-canonical photoreceptor shaping light-responsive behavior.

      (4) Lines 23-25: This reads as if light perception and vision are the same. Please clearly distinguish to make clear that vision is only one way in which light can be perceived and influence behavior.

      We have revised the text to clarify that vision represents only one modality of light perception and that light can influence behavior via both visual and non-visual pathways. “The ability to detect and respond to light is fundamental for many organisms and can influence behavior through both visual and non-visual pathways. Vision relies on….”

      (5) Lines 26-27: Here and also later in the introduction, it is hard to follow how different groups of opsin light receptors relate to each other (e.g., opsins (in general,) rhodopsins, r-opsins, c-opsins, non-visual opsins), etc.) This is also related to the fact that opsins can be differentially grouped based on phylogeny/structure (e.g., r- vs. c-opsins) or role/localization (e.g., visual vs. non-visual). Please revisit the introduction with a non-expert reader in mind, and try to address the groups hierarchically. In fact, a small tree-like figure of the different groups may be a simple solution.

      We thank the reviewer for this helpful suggestion. We have revised the Introduction to simplify the presentation of opsin classification. c-Opsins and r-opsins are now introduced only briefly to place RH7 within the rhabdomeric opsin family. Since Drosophila contains only rhabdomeric opsins and these are the focus of our study, we did not further expand the Introduction with a detailed discussion of c-opsins or add a classification figure.

      (6) Line 33: Please expand to "...image formation in the eye, some..." to be more precise. We have revised the sentence to clarify that rhodopsin-mediated image formation refers to visual systems.

      “While the primary function of rhodopsins is image formation in visual systems, some are also known to participate in non-image-forming functions.”

      (7) Lines 46-55: This detailed information about the different Drosophila rhodopsins is not referred to anywhere else in the manuscript. I suggest shortening and focusing on rh7.

      We thank the reviewer for the suggestion. We have shortened the section to focus on RH7, as the other rhodopsins are not discussed elsewhere in the manuscript. The revised text now highlights the debated expression and potential function of RH7.

      “Drosophila melanogaster (Dmel) has seven rhodopsins (RH1-RH7), all belonging to the ropsin group. While RH1–RH6 are expressed in well-characterized photoreceptors, the expression pattern and function of RH7 remain less clear and are still debated.”

      (8) Line 55: The statement that the expression of Rh7 remains debated also occurs later in the introduction (line 88). If in line 55, it is about the expression sites specifically, references should be added. Otherwise, it may be sufficient to only address this aspect in line 88.

      The statement in line 55 specifically refers to the expression sites of RH7. References to Ni et al., 2017 and Senthilan et al., 2019 have been added to support this point.

      (9) Line 61: Which of these features distinguishes rhodopsins from other opsin groups?

      We thank the reviewer for this comment. The RH7 section has been thoroughly revised to clarify both the features shared with other rhodopsins and those that distinguish RH7 from other opsin groups. Key distinguishing features, including the extended N- and C-terminal tails and the absence of the QAKKMNV motif in ICL3, are now highlighted at the beginning of the paragraph, while additional Drosophila-specific features, such as the palindromic RCSI, are discussed subsequently.

      “RH7 displays the canonical rhodopsin features, including seven transmembrane helices, a chromophore-binding lysine, and the LRTPXN motif located in the first intracellular loop (ICL1)….”

      (10) Figure 1: For panel B (left), please increase label sizes. For panel B (right), the color scale makes it very hard to see low-level expression (e.g., in Mi15 and below). Please try adjusting the color scale and/or consider only showing the cell types also indicated in the left part of the panel. For ninaE, please add "aka Rh1" or similar for the less informed reader.

      We have revised Figure 1 accordingly. Specifically, we increased the label sizes in panel B (left) to improve readability. For panel B (right), we adjusted the color scale to better visualize low-level expression and improve overall clarity. In addition, we updated the labeling of ninaE to “Rh1 (ninaE)” to aid accessibility for a broader audience.

      (11) Lines 88-90: What exactly were the contradictions that emerged from previous studies? Also see the comment in the public review regarding the discussion of the results.

      Thank you for pointing this out. We have clarified this in the revised manuscript. “Previous studies on RH7 have yielded conflicting results regarding its function and expression, including discrepancies in the identified neuronal populations and associated behavioral phenotypes”

      (12) Line 91: Briefly explain the characteristics of white and yellow mutations so the reader can assess why these are relevant here.

      We have clarified the role of the white and yellow genes in the genetic background. The revised text now reads:

      “Both genes are expressed in the optic system (Davis et al., 2020; Supplementary Material) and are known to affect neuronal function and behavior (Bond et al., 2024; Drapeau et al., 2003; Rickle et al., 2025).”

      In addition, we have visualized the expression data for yellow and white from Davis et al. in the Supplementary Material for more clarity.

      (13) Lines 100-101: Circadian entrainment is not a typical visual function. Please rephrase.

      The sentence has been revised for clarity and now reads:

      “As an ancestral rhodopsin, RH7 appears to contribute to basic visual functions, such as contrast processing, as well as to non-visual functions like circadian synchronization, similar to melanopsins in mammals.”

      (14) Line 105: The exact address is not necessary, mention BLASTP is enough.

      Thank you. We have now removed the exact address and we now simply refer to BLASTP.

      (15) Line 108-109: If default settings were used, the details are not needed.

      We have omitted the details, as they are not necessary.

      (16) Line 113: These settings seem to repeat line 108. Needed?

      We thank the reviewer for pointing this out. In the original version, the settings in line 108 referred to the BLAST search, while those in line 113 pertained to the phylogenetic tree, where the parameters are essential, because phylogenetic inference depends on dataset- and method-specific choices. However, this entire section has now been revised, as the phylogenetic tree has been completely rebuilt with a much broader dataset, including mammalian melanopsins and lophotrochoan r-opsins.

      (17) Line 122: Without further context, these abbreviations are non-informative and confusing to many readers. Provide details or rephrase. The same applies to DMEM, FBS, and Glo22F in the same paragraph. While many readers will understand instantly, keep the diverse audience of eLife in mind.

      We have now added explanations for all abbreviations in the paragraph to improve clarity for a broad audience. Specifically, the Gα subunits (GNAS, GNAL, GNAQ, GNA11, GNA12, GNA13, GNAZ) are now clearly defined, and DMEM, FBS, and Glo22F are also explained as Dulbecco’s Modified Eagle Medium, fetal bovine serum, and a cAMP-sensitive luciferase reporter, respectively. These changes should make the methods clearer and more accessible to all readers.

      (18) Line 144: "constant conditions" is not ideal as it could be misinterpreted as DD or LL. Please rephrase.

      We agree with the reviewer and have removed the phrase “constant conditions” to avoid potential misinterpretation.

      “All recordings were performed under 60% relative humidity and 25 °C…”

      (19) Line 148: Stating Lux values for Drosophila is not informative as the unit is based on the spectral sensitivity of the human eye. Ideally, provide a spectrum of the used light source as a supplement.

      We thank the reviewer for this suggestion. We agree that lux values alone are not informative for Drosophila, and we have now included the spectrum of the light source in Figure 3–figure supplement 1A.

      “A standard day was defined as 12 h light (30 µW/cm<sup>2</sup> ~ 100 lux, the spectrum of the light is shown in Figure 3–figure supplement 1A) and 12 h darkness”. In addition, to ensure complete consistency of the experimental conditions, we repeated some earlier experiments using the same light source as in the rest of the study, since the exact light source used in the initial experiments could no longer be verified. This ensures that all behavioral experiments presented in the revised manuscript were performed using the same light source.

      (20) Lines 149-153: The startle response protocol is hard to understand when only reading it. It could help to state when (relative to lights-on) the first dark pulse was given and how many dark pulses were given per light phase.

      We have clarified the timing and frequency of the dark pulses in the Methods section. We now specify that the first dark pulse was applied 1.5 h after lights-on and that six dark pulses were delivered during each 12 h light phase.

      (21) Lines 159ff: The 4-hour startle response assay is not clearly distinguished from the previously mentioned assay (30 min D + 1.5h L). I could help to start with e.g., "In a second assay..." and to clearly state why this additional assay was performed. That is, what information can the 4-hour assay provide that the previous assay could not?

      We have revised the text to clearly introduce the 4-hour startle response assay as a second, distinct paradigm (“In a second startle response assay…”).

      We also clarified its purpose: in contrast to the initial assay, this paradigm was designed to measure the acute startle response independently of circadian influences. To this end, flies were rendered arrhythmic and exposed to repeated 4-hour light–dark cycles, preventing re-entrainment and isolating the startle response.

      In addition, we now refer to a schematic of the light regime in Figure 3–figure supplement 1C.

      (22) Lines 161-163: As flies were kept in LL aside from the dark pulses, it could be more intuitive to talk about 72h or three 24h intervals rather than 3 days. Otherwise, one might assume that the initial constant light was followed by 3 days of LD plus dark pulses.

      We have revised the text to emphasize the total duration (“72 h”) to avoid confusion with a 24-hour LD regime. In addition, we now provide a schematic of the light regime in the Supplementary Material (Figure 3–figure supplement 1C).

      (23) Line 172: Please write out CantonS once, as otherwise it only occurs in Table 1. Also, clarify that y+ and w+ refer to the (absence of the) yellow and white mutation, respectively.

      We have revised the text to write out Canton-S (CS) upon first mention and clarified that y<sup>+</sup> and w<sup>+</sup> denote wild-type alleles of the yellow and white genes, respectively, meaning any mutations in these genes are absent.

      (24) Table 1: Consider adding "(truncated RHSOPSIN7)" or similar to the "Darkfly" cell.

      We have updated Table 1 to indicate that the Darkfly line carries a truncated RH7. The description now reads: “This line has been maintained for decades in constant darkness and carries numerous mutations, including a truncated RH7 lacking the last 21 amino acids.”

      (25) Table 2: In the formatted paper, Table 2 should appear after section 3.5 so the reader can properly interpret the applications and names.

      We have placed Table 2 immediately after section 3.5 as suggested.

      (26) Table 3: Consider adding the product IDs of the used antibodies for convenience.

      We have added the product IDs of all antibodies used to Table 3 for convenience.

      (27) Lines 180ff: This section should initially state the purpose of establishing the rh7-Gal4 line, i.e., the expression of selected gene in rh7-expressing cells. Again, keep your (lee-informed) readers in mind.

      We have revised the section to clarify the purpose and design of the Rh7-Gal4 line. It now states that the line was generated to identify Rh7-expressing cells and explains the use of a relatively large promoter region including exon 1 and 2.

      (28) Line 190 w1118 flies do not occur in Table 1. While used by a commercial company here, please still include them for completeness.

      We have added the w<sup>1118</sup> line to Table 1 for completeness, as well as the BDSC Stock #8621 line, which was used as the background for the UAS-construct flies.

      (29) Lines 192ff and 203ff: As for lines 180ff, start with a brief description of what the purpose of the respective works was.

      We have revised the section to start with a brief description of the purpose of the rescue experiments. The text now clearly states that UAS constructs were generated to assess the ability of different Rh7 variants to rescue the phenotype, with UAS-Rh7 as the wild-type rescue, UAS-Rh7<sup>Darkfly</sup> carrying the Darkfly variant, and UAS-empty serving as a control. We have added an introductory sentence to the optomotor section in Materials & Methods to clarify the purpose of the experiments: “To investigate the contribution of Rh7 in the lamina and medulla to visual motion detection, male flies were individually tested for their optomotor walking behavior.” This makes clear why the assay was performed before describing the setup and measurements.

      (30) Line 225: Just to be safe, make sure to not mix up Δ-CT and 2-ΔΔCT (see Livak & Schmittgen 2001, doi: 10.1006/meth.2001.1262).

      We confirm that ΔCT was indeed used to calculate relative mRNA levels. To clarify this, we have now added the formula to the text: ΔCT = CT_α-tubulin − CT_Rh7.

      (31) Line 229: Please state the light (cycle) conditions under which the flies were raised, as well as the sampling times at which they were fixed.

      We have now specified the light cycle conditions under which the flies were raised (12 h light:12 h dark at 25 °C) in the Methods section. For qPCR experiments, tissues (retina, lamina, and brain) were carefully dissected from adult flies without prior fixation to preserve RNA integrity. Dissections were performed during the light phase and were not restricted to specific time points. These details have been added to the revised manuscript (section 3.10).

      (33) Lines 296-297: This brief description could go at the start of section 3.2.

      The sentence describing the GsX assay (“To test the functionality of RH7, we used a GsX assay designed to determine which Gα proteins can bind to a given GPCR, in this case RH7 (Ballister et al., 2018)”) has been moved to the Methods section (now 3.3) as a brief introduction to the approach.

      (34) Line 305: Clarify that 2 different retinals were tested.

      We clarified that two different retinals were tested. The text now reads: “We observed robust activation with the Gαz chimera, with both 9-cis-retinal and all-trans-retinal (Figure 2C).”

      (35) Figure 2A, B: I suggest using a different color for the RH3,4,5, branch for better distinction from RH7.

      We have generated a new tree and adjusted the branch colors to improve clarity between RH3,4,5, branch and RH7.

      (36) See comment above regarding the shifting/flexibility of WTs vs. rh7 mutants.

      Following the reviewers and editor's recommendations, we revised the manuscript to focus on the light-dependent effects of RH7 and no longer interpret our data in terms of shifting ability or circadian flexibility. The corresponding statements have been removed or revised accordingly.

      (37) Line 348: Please change "occur" to "be triggered".

      The wording has been updated as suggested, replacing “occur” with “be triggered” in the text.

      (38) Line 355: I would mention the double mutants only after the results from the rh7 single mutants were described.

      We have adjusted the order of the text accordingly and now introduce the double mutants only after describing the Rh7 single mutants.

      (39) Line 362: See comment on line 159ff.

      We have added a sentence at the beginning of the section to clearly introduce the 4-hour startle response assay as a second, distinct paradigm: “In a second startle response assay (4-hour assay), designed to measure the acute response independently of circadian influences…” This clarifies its purpose and distinguishes it from the initial assay.

      (40) Line 368: Write "rh7 mRNA" to be precise.

      We have updated the text to use “Rh7 mRNA” for precision, as suggested.

      (41) Figure 5: If possible, please sort the panels in the order in which they are mentioned in the text. For panel E (right), the orientation of the lower schematic, relative to the upper one and the left panel, is unclear. Is it possible to add orientation indicators? Alternatively, could L5 and Mi1 neurons be indicated in the upper schematic instead?

      We thank the reviewer’s helpful suggestion. Since reorganizing the figure panels was challenging and would have affected the overall layout, we instead revised the corresponding text to ensure that the order of panel descriptions matches the figure arrangement. To address the concern regarding panel E, we have added orientation indicators to the schematic to clarify the relative positioning.

      (42) 419 Add "A)".

      We have added an A).

      (43) Line 432: Later on (line 598), it is mentioned that the other accumulated mutations in Darkfly may also have affected the observed patterns. Are there any specific mutations worth highlighting in this context aside from rh7?

      We thank the reviewer for this comment. In response, we have expanded the Discussion to highlight additional mutations in the Darkfly genome that may contribute to the observed phenotype. Nonsense mutations in HisCl1 and Vha100-1 could affect visual processing and neuronal signaling, potentially altering sensory input and synaptic function. Missense mutations in DopR, bgm, and developmental regulators such as Sox21b may further modulate activity, sleep, and neural development. We have updated the Discussion accordingly to make these points clear.

      (44) Lines 435-436: Unchanged mRNA levels do not necessarily equal the presence of the translated protein. Is there another way to properly confirm this? E.g., rh7 HCR in Darkfly?

      We agree that unchanged mRNA levels alone do not confirm the presence of translated protein. While in situ HCR does not directly measure protein levels, it provides additional information on the cellular localization and presence of Rh7 transcripts beyond qPCR measurements. We have therefore performed Rh7 in situ in Darkfly and included this data in Figure 5—figure supplement 1B.

      (45) Line 439: "activity" is too vague based on only the altered dark pulse response. I would rather suggest factors like increased protein concentrations/stability, increased sensitivity, constitutive activation, etc.

      By “activity,” we refer to the molecular activity of RHODOPSIN 7 as reflected in the behavioral response. The Results have been revised to:

      “When we exposed the Darkfly to dark pulses in a 12:12 light-dark cycle, they exhibited the opposite phenotype to Rh7<sup>0</sup> mutants, showing a stronger startle response (Figure 6A), possibly reflecting RHODOPSIN 7 adopting a constitutively active form in the Darkfly strain, driving the enhanced behavioral response.”

      (46) Lines 442-446: The no-rescue control does not fully resemble WTs as they lack the gradual activity decrease after lights-off. The abrupt decrease (also in the 2 rescues) is more reminiscent of the rh7 mutants. This could be discussed in the context of what was mentioned at the start of this section (Meyerhof et al 2024 paper).

      We agree that the rescue lines do not fully restore all aspects of the WT control locomotor pattern. One possible explanation is that the Rh7-Gal4 driver does not fully represent the endogenous Rh7 expression pattern. As described in the Results section, our in situ hybridization analysis identified additional Rh7-expressing cells, particularly in the optic system, that were not detected by the Rh7-Gal4 line (results, section 4.5). We have added this point to the Discussion to address how the broader Rh7 expression pattern may contribute to the observed behavioral effects (discussion 5.4).

      (47) Line 472: "restored the reduced startle response" reads a bit convoluted. Better write e.g., "restored the enhanced startle response that was absent in the no-rescue mutants".

      We have revised the text as suggested to clarify the phrasing.

      (48) Lines 533-535: Please provide a reference for the statements about L5 and Mi1 functional roles. Also, this is the only part where there is some connection made between rh7 (expressed in Mi1) and contrast processing (which involves Mi1). As this is a rather weak connection, please consider the last paragraph of the public review section.

      We have added references to support the functional roles of L5 and Mi1 neurons. L5 neurons relay signals from outer photoreceptors to the medulla and show strong contrast adaptation (Matulis et al., 2020). Mi1 neurons contribute to motion and contrast processing (Behnia et al., 2014; Matulis et al., 2020). To address the connection between Rh7 expression and contrast processing, we have carefully phrased the text to indicate a potential role of Rh7 in modulating contrast-related signals in Mi1, while noting that the functional link remains to be directly tested. We believe this wording, together with the added references, provides proper support for the statements and maintains a cautious interpretation.

      If contrast perception shall indeed be investigated, this may be done by performing the optomotor assay with gray stripes of different contrast, with stripes where the edges are not sharp but show a gradual change from black to white.

      We agree that contrast perception can be assessed in more detail using stimuli with defined contrast levels and gradual luminance transitions. However, our aim was not to directly measure contrast sensitivity, but rather to investigate behavioral responses to changes in luminance. We have clarified this distinction in the revised manuscript and now specify that the optomotor response reflects processing of spatial and temporal changes in luminance, while the light-off startle response measures responses to abrupt changes in luminance.”

      (49) Lines 546-547: Are there references on how activity or behavior in general can affect external light cues?

      We have added appropriate references to support this statement. In particular, we now cite Rieger et al. (2003), which demonstrates direct effects of light on locomotor activity (masking), and Helfrich-Förster (2017), which provides a comprehensive overview of circadian regulation and light-dependent behavioral modulation. These additions clarify how external light cues can directly influence behavior in addition to circadian clock control.

      (50) Lines 557-560: See comment above regarding the shifting/flexibility of WTs vs. rh7 mutants.

      We thank the reviewer for this comment. We agree that assessing shifting and behavioral flexibility would require dedicated experiments, such as jet lag or entrainment assays. We have therefore revised the focus of the manuscript and now primarily discuss RH7 function in light-dependent behavioral responses rather than broader flexibility of the circadian system. Future studies will further explore the potential contribution of RH7 to behavioral adaptation and flexibility using dedicated experimental approaches.

      (47) Lines 564-567: How many species possess dcry but not rh7? This is an important distinction, as otherwise one could assume that both must always co-occur. Alone, this provides only limited support for a potential functional interplay. The findings by Ni et al. (2017) regarding dcry and rh7 in entrainment could, however, help strengthen this point.

      We have clarified the evolutionary relationship between DCRY and RH7 in the revised manuscript. We now specify that, although DCRY is widespread across Bilateral and many non-panarthropod species possess DCRY without RH7, RH7 and DCRY show a strong evolutionary association within arthropods, with approximately 98% of DCRY-retaining arthropod species also retaining RH7. At the same time, the presence of RH7 in some lineages lacking DCRY suggests that RH7 may retain functional relevance in the absence of DCRY. Together with previous findings on the functional interaction between RH7 and DCRY in light adaptation (Ni et al., 2017), these evolutionary patterns support a conserved connection between the two light-sensing systems, while the exact nature of this relationship remains to be further investigated. These points are now shown and discussed in section 4.1 and 5.5.

      (48) Lines 579-580: Here, one could explicitly mention that this is supported by the lack of diel startle response modulation in the per mutants (Figure 4A).

      We have modified the text to explicitly highlight this point. The sentence now reads: “Dark-pulse experiments show that both wild-type controls and per<sup>0</sup> mutants, which lack a functional circadian clock, exhibit a strong startle response, consistent with the absence of diel modulation of the response in per0 mutants (Figure 4A).”

      (49) Lines 596-597: The increased night activity in Darkfly seems largely limited to the first half of the night (compare e.g. Figure 6A and Figure 3A). Again, the loss/alteration of rh7 seems to have its major effect after a transition from light to dark (see lines 442-446, start of the section).

      We thank the reviewer for pointing out this issue. The wording in the previous version could have been misleading. By “dark phase,” we meant the 30-minute periods without lighting during the dark-stimulus experiments, and not the “night phase.” We have revised the text to clearly refer to the startle response.

      We also clarify that the increased locomotor activity observed in the “Darkfly” strain outside of the startle response is likely caused by additional background mutations that accumulated during long-term rearing in constant darkness, and not exclusively by the RH7 deletion.

      (50) Line 622: See comments regarding contrast and motion perception. Do the N- and Cterminal regions of RH7 and melanopsin share similarities in sequence or additional characteristics aside from phosphorylation sites? This could support a conserved role.

      We thank the reviewer for this suggestion, which prompted us to perform a more detailed analysis of conserved features between RH7 and melanopsins. In addition to the extended and potentially highly phosphorylatable N- and C-terminal regions, we identified several conserved sequence motifs, including two in the C-terminal region and others within the transmembrane core. One of these motifs extends into the conserved DRY motif in the second intracellular loop (ICL2). These findings are now described in the Discussion (section 5.7) to highlight potential structural similarities beyond phosphorylation sites. The corresponding sequence alignments are provided in the supplementary material.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      The study by Hu et al. investigated the role of olfactory ErbB4 in regulating olfactory information processing. The authors demonstrated that ErbB4 deletion impairs odor discrimination, sensitivity, habituation, and dishabituation by using an impressive combination of techniques from morphological to electrophysiology (both slice and in vivo) and from viral injection to cell-type-specific mutation to behavioral analysis. The findings underscore the crucial role of ErbB4 in olfactory PV neurons in modulating mitral cell function and odor perception.

      Strengths:

      This study contains a pretty comprehensive set of experiments.

      Major concerns:

      (1) Line 151 page 7, "PV-Erbb4+/+ mice (generated by crossing PV-Cre mice (Wen et al., 2010) with loxP-flanked Erbb4 mice". Does this mean mice carrying PV-Cre and ErbB4 floxed allele? Or with the WT allele? This is confusing. Figures 2B and 2C, ErbB4 expression was evident in many cells that were not positive for PV. What are the identities of those cells? Are they important?

      Thank you for your positive comments regarding our study. PV-Erbb4<sup>+/+</sup> mice carried the PV-Cre transgene with the WT allele. In the revised manuscript, we have simplified the description of the genotype for clarity and have provided detailed breeding information in the "Materials and Methods" section (Line 532).

      As shown in Figures 2B and 2C, ErbB4 expression was evident in GL and GCL cells that were not positive for PV. The activation of ErbB4-expressing cells in the GL and GCL has been suggested to upregulate theta and gamma oscillations, respectively (PMID:35853717). Mammalian OB are the most abundant and varied interneurons among brain tissues, and their functional importance and diversity remain unclear (PMID:31358754 and PMID:32208366). ErbB4-expressing PV interneurons in the EPL and IPL were relatively less abundant but accounted for the majority of inhibitory inputs to M/TCs. Importantly, one PV interneuron connects with over 1000 M/TCs to mediate recurrent and lateral inhibition, linearly controlling the OB output (PMID:31358754 and PMID:39186804). This study provides evidence that ErbB4 signalling in PV interneurons is required for olfactory discrimination and dishabituation.

      (2) In Figure 4, the authors performed tetrode recordings in awake head-fixed animals. Although individual neuron spikes could be obtained by spike-sorting, this is not a "single-unit" experiment due to the nature of this approach.

      What is the odor used in Figure 4? How did the authors clean up the odor to limit the stimulation within 2 seconds? In what layer were the tetrodes placed? What is the putative cell type presented in Figure 4C? If Figure 4C is a representative neuron recorded, the odor-induced suppression of spike activity seems to be impaired in PV-ErbB4-/- animals. However, Figure 4D shows that suppressed neurons were similar between the two types of animals. Such comparisons among individual mice are difficult for in vivo electrophysiological experiments because the recorded cell type and placement of electrodes would be different. The authors should apply ErbB4 inhibitors to the same animals and compare the effects before and after. This would ensure the recording of the same population of neurons.

      Thank you for your valuable comment and suggestion. We agree that tetrode recording combined with spike-sorting is not a strict "single-unit" approach, although this method is widely accepted and consistently referred to as "single-unit recording" even "single-neuron recording" (PMID:30833706). Based on your comments, we modified the description as follows: “To obtain individual neuron spikes, units were identified by principal-component analysis scan (PCA) clustering of the spikes” (Lines 210-212).

      As shown in Figure 4, a standardised panel with eight tubes delivers eight odours: isoamyl acetate, 2-heptanone, phenyl acetate, benzaldehyde, dimethylbutyric acid, n-heptanoic acid, n-pentanol, and 2-pentanone. Odours were delivered via an odour delivery system (Thinkerbiotech), and charcoal-filtered air was supplied to the mouse’s nose at a constant rate of 1 L/min to eliminate airflow interference, which effectively limited the stimulation to 2s. We have added the above description to the revised "Materials and Methods" section (Lines 786-789).

      Author response image 1.

      The tetrodes were placed within the ventral mitral cell layer based on stereotaxic coordinates. The putative cell type is mitral/tufted (Figure 4C). Despite the presence of diverse cell types in the OB, only the spiking activity of M/TCs can be captured via tetrode recordings (Kay and Laurent, 1999; Doucette et al., 2011). We added the above description in the revised "Materials and Methods" section (Lines 764-767). As you have indicated, Figure 4C shows the impairment of odour-induced spike suppression in PV-Erbb4<sup>-/-</sup> mice. Consistently, Figure 4D shows the decreased suppression of odour-induced spike activity in blue (quantified in Figure 4I ΔMFR, ~25%), but the increased number of suppressed neurones in the PV-Erbb4<sup>-/-</sup> group (Figure 4L). Considering that applying ErbB4 inhibitors to the same animals has no selectivity for blocking ErbB4 signalling in PV interneurons, in vivo neural signals typically drift over time when performing pre- and post-inhibition comparisons. Therefore, we compared in vivo electrophysiological data at the population level according to previous studies (PMID: 35173173, PMID:28425486, and PMID:28817803).

      (3) At a glance in the heatmap in Figure 4D, excited neurons were reduced in PV-ErbB4-/- mice, but not inhibited neurons. This was different from Figure 4L. The authors need to have a criteria or threshold to show how they categorized each population.

      In Figure 4L, red denotes excited neurones, whose number decreased from 66 to 16 in the PV-Erbb4<sup>-/-</sup> group, and blue denotes inhibitory neurones, whose number increased from 81 to 148 in the PV-Erbb4<sup>-/-</sup> group. This trend is consistent with that observed in Figure 4D. The classification criteria for each population were defined as follows:

      “To determine whether the odour evoked a significant response, we used the Wilcoxon signed-rank test to compare the spontaneous (baseline) firing rate and odour-evoked firing rate of each unit–odour pair across all trials; unit–odour pairs with P > 0.05 were defined as nonresponsive, those with P < 0.05 as responsive, and responsive pairs were further categorised as excitatory (odour-evoked firing rate > spontaneous firing rate) or inhibitory (odour-evoked firing rate < spontaneous firing rate). Details are provided in the "Off-line spike sorting and statistics of the unit data" section of Materials and Methods (Lines 810-816).

      (4) Figure 4D, 4F and 4J seemed to be inconsistent. In Figure 4D before odor, there was no clear increase in the spontaneous activity in PV-ErbB4-/- mice; in Figure 4F-4G and 4J-4K, clearly, there was a high spontaneous activity in PV-ErbB4-/- mice.

      Figure 4D, 4F and 4H shows odour-evoked changes in mean firing rate (ΔMFR), calculated by subtracting the baseline firing rate. By contrast, Figures 4G and 4I show raw spontaneous mean firing rate (MFR), which was elevated in PV-Erbb4<sup>-/-</sup> mice. We have revised the description of Figure 4D in both the Results section (Line 222) and figure legends (Line 1217).

      (5) What are the neurons recorded in Figure 6E-6F? If they were MCs, loss of ErbB4 in PV neurons should not alter their intrinsic electrical properties. Rather GABAergic inputs could be altered. Indeed, the authors presented a reduction of GABAergic inputs from PV neurons to MCs.

      The neurones recorded in Figures 6E-6F are indeed mitral cells (MCs). The firing frequency of action potentials reflects not only the intrinsic electrical properties but also the balance between excitatory and inhibitory synaptic inputs. As demonstrated in this study, the loss of ErbB4 in PV neurones leads to reduced GABAergic synaptic inputs from PV interneurons to MCs, which is consistent with our reasoning and is a key factor contributing to the observed changes in the action potential firing of MCs

      (6) Figure 8E-8H, a better experiment would be specifically expressing ErbB4 or PV neurons. In Figure 8F and Figure 8I, was it the excitability after the current injection? Why not perform the spontaneous activity recording?

      According to your suggestion, we used optogenetics to activate PV interneurons and recorded inhibitory postsynaptic currents (IPSCs) in MCs. As shown in the revised Figure 9 and Supplementary Figure 1F and 1G, deleting ErbB4 of PV interneurons in the OB weakened the inhibitory modulation of MCs by PV interneurons.

      Figures 8F and 8I show the excitability after current injection. We did not measure spontaneous activity, primarily because the spontaneous firing frequency varies significantly among different cells, resulting in poor stability. In contrast, current-injection-induced excitability is more stable and quantifiable, making it more suitable for assessing specific changes in MC responsiveness caused by altered PV-MC inhibitory inputs.

      Reviewer #2 (Public review):

      Summary:

      Hu et al investigate the role of PV neurons and their expression of Erbb4 in olfactory performance through a series of behavioral tests, selective knockout experiments, and in vivo and in vitro electrophysiology. Knockout of Erbb4, either in PV cells or the whole OB, resulted in impairment of discriminating complex odors. The authors present data that inhibition is impaired in MCs, which is likely underlying the abnormal odor-evoked responses of MCs in vivo and the impaired behavioral responses.

      Strengths:

      Overall, a key strength of this manuscript is the breadth of experiments to test the role of PV Erbb4 expression on circuit dynamics and behavior. The behavioral experiments were clear and sufficiently powered.

      Weaknesses:

      The major drawback of this manuscript is the lack of depth and rigor in experiments. Some experiments are preliminary, underpowered, and not quantified. As a result, many conclusions of the manuscript are weakly supported in its current form and would require significant revisions to address these shortcomings. Major weaknesses that should be addressed are as follows:

      (1) AAV-PV-Cre-GFP is not described or validated. Is this the S5E2 enhancer or something else? What is the specificity and efficacy of this approach in selectively knocking out Erbb4 in PV neurons? Reduced Erbb4 expression in the entire OB with PCR does not validate the selectivity of this approach. At a titer of 10^12, it is unlikely to be specific. Even a small amount of off-target Cre expression will knock out the gene in non-PV cells, so the authors should show whether the gene is knocked out at the single-cell level from PV and non-PC cells. Without validation of this approach, this experiment is no different than the AAV-Cre-GFP experiments.

      Thank you for your comment and thoughtful suggestion. The AAV-PV-Cre vector used in this study was purchased from BrainVTA (catalogue number: PT-0275; vector name: rAAV-fPV-CRE-bGH polyA), which contains an fPV promoter to ensure the selectivity and a β-globin intron to enhance Cre expression efficiency. Importantly, the specificity and efficacy of this AAV-PV-Cre construct in selectively targeting PV-expressing neurones have been validated in multiple published studies (PMID:40196908 and PMID:31987494). According to your suggestions, we also performed immunofluorescence staining (co-staining for PV and ErbB4) and found that ErbB4 expression was specifically reduced in PV-positive interneurons in OB tissues injected with AAV-PV-Cre, while ErbB4 levels remained unchanged in PV-negative cells (the revised Figures 9B and 9C). This single-cell-level validation directly demonstrated that our AAV-PV-Cre-mediated knockout approach specifically targets ErbB4 in OB PV interneurons, thereby avoiding off-target effects in non-PV cells.

      (2) Figure 1D - three mice per group is insufficient. There is no control group error (the same as Figure 9). Why is it a paired t-test when there is a control group? The authors should be comparing go/go vs. go/no-go. The methods for normalization are unclear and are likely to hide the fact that n=3 is insufficient to capture a difference without extra measures to normalize the data.

      Thank you for the comment. According to your suggestions, we expanded the sample size to four mice per group and modified the statistical test from a paired t-test to an unpaired t-test in the revised Figure 1C and 1D. Since not all samples were exposed to the same blot for direct comparison, we performed normalisation of each sample relative to its internal control prior to statistical analysis to ensure the reliability of group comparisons. There was an error regarding the control group in the revised Figure 1D. Detailed information on the normalisation method and updated statistical results have been provided in the revised figure legends (Lines 1116-1118).

      (3) The analysis of LFP is limited. During what period was this quantified? Are there any differences in task-related LFP changes? Also related to in vivo electrophysiology, the authors should show examples of isolated units, including their waveforms and how units were clustered and assigned to M/TCs.

      Thank you for the comment. The spectral power of each frequency band was quantified using a 4-s sliding window during the pre-odour stimulation period (4–0 s before odour onset). Regarding task-related LFP changes, the initial recordings were affected by unavoidable interference, leading to unstable signals that precluded reliable analyses. Based on your suggestions, we have supplemented the revised manuscript with examples of isolated single units, including their representative waveforms, clustering results (e.g. principal component analysis plots), and unit assignment criteria (the revised Figure 4—figures supplement 1A and 1B). As previously noted, the tetrodes were placed in the mitral cell layer based on stereotaxic coordinates. Consistent with established literature (Kay and Laurent, 1999; Doucette et al., 2011), the putative cell type recorded using this approach was mitral/tufted cells (M/TCs). Detailed methodological parameters for spike sorting, unit isolation, and cell type identification are provided in the "Materials and Methods" section (Lines 764-767 and Lines 803-805).

      (4) The authors use 80pA and 100pA to elicit equivalent AP spiking in MCs to determine if recurrent inhibition differs, but do not actually show that AP spiking is the same across groups. This should be quantified.

      There seems to be a prominent increase in the firing of MCs in PV-Erbb4+/+ mice before odor presentation, but not in PV-Erbb4-/- mice. What is the significance of this?

      Thank you for your valuable comment and suggestion. According to your suggestions, we quantified the AP firing frequency of MCs in both groups under the respective stimulation currents, and statistical analysis confirmed that there was no significant difference in the AP spiking levels between the two groups (the revised Figure 8—figure supplement 1A).

      We speculate this prominent pre-odour firing increase in PV-Erbb4<sup>+/+</sup> mice (but not in PV-Erbb4<sup>−/−</sup> mice) stems from interference caused by the opening of the solenoid valve during odour clearance prior to stimulation—this artefact was present in the initial recordings of control mice but was eliminated during the data acquisition for PV-Erbb4<sup>−/−</sup> mice. This was not statistically significant. To avoid this interference, we strictly defined the analysis windows, and the spontaneous firing rate was calculated by averaging the spikes recorded during the 4–2 s period before odour stimulation, excluding the interference-prone interval immediately before odour onset. This rigorous window selection ensured the reliability of our comparisons of spontaneous and odour-evoked firing between the groups.

      (5)There is a disconnect between the in vivo firing rates of MCs and ex vivo firing rates. In slice, the authors note that the spontaneous activity of MCs is elevated in the KO, but this is not observed in vivo, where conditions are physiological. Therefore, it is unclear whether the concept of signal-to-noise changes in slice (higher spontaneous, lower evoked), indeed translate to something in vivo. It would be important to know what the PV cells are doing in vivo. Perhaps they have low firing rates prior to odor onset, which may explain the lack of observed difference in baseline FRs in MCs. The authors should have this data in their tetrode recordings, which would offer insight into when inhibition is recruited.

      Thank you for your valuable comments, which helped clarify the consistency between in vivo and ex vivo electrophysiological data. In ex vivo slice recordings, we measured both spontaneous and evoked excitatory firing rates of MCs, and found that the spontaneous activity of MCs was elevated in PV-Erbb4<sup>−/−</sup> mice (Figures 6A and 6B). Importantly, this observation is consistent with our in vivo data: M/TCs in PV-Erbb4<sup>−/−</sup> mice exhibited significantly higher spontaneous firing rates during excitatory responses to odour presentation (Figures 4F and 4G). However, for inhibitory responses during odour presentation, M/TCs in PV-Erbb4<sup>−/−</sup> mice showed significantly lower spontaneous firing rates in vivo (Figures 4H and 4I). Thus, the overall in vivo spontaneous activity of MCs appeared unchanged owing to opposing changes in excitatory and inhibitory subpopulations, and there was no true discrepancy between the ex vivo and in vivo results. We agree that in vivo recording of PV interneuron activity would be invaluable for understanding their functional state under physiological conditions. Unfortunately, this is technically unfeasible with the current experimental setup, primarily because of the sparse distribution of PV interneurons in the OB. As a complementary alternative, we characterised the key electrophysiological properties of PV interneurons in ex vivo slices (e.g. action potential and mEPSC, the revised Figure 7—figure supplement 1), which will provide additional insights into the underlying cellular mechanisms.

      (6) Since PV neurons are required for gamma oscillations, why is it that KOs have higher gamma oscillations? Is it indeed the case that PV cells have a hypofunctional phenotype in this model? Again, recording from PV cells in vivo would help make sense of this.

      Thank you for your valuable comments, which were critical for clarifying the functional consequences of ErbB4 knockout in PV interneurons. The elevated gamma oscillations in the OB of PV-Erbb4<sup>-/-</sup> mice appear to be primarily driven by the increased action potential firing frequency of PV interneurons that we observed in OB slice recordings (the revised Figure 7—figure supplement 1). A similar phenomenon has been reported in the hippocampus (PMID:24050403).

      Indeed, the PV cells displayed a hypofunctional phenotype in this model. Our optogenetic experiments provided direct evidence for this (the revised Figure 9—figure supplement 1). Specifically, optogenetic activation of PV interneurons in AAV-PV-Cre-injected mice (selective ErbB4 knockout in OB PV interneurons) induced weaker inhibitory postsynaptic currents (IPSCs) in MCs than in controls (the revised Figure 9—figure supplement 1). This indicates that ErbB4 loss induces PV interneurons to be more excitable, but impairs their ability to inhibit neighbouring MCs.

      We acknowledge that in vivo recordings of PV interneurons would further clarify their functional state under physiological conditions. As noted earlier, this remains technically challenging using our current setup; however, our ex vivo mechanistic data and optogenetic findings collectively support these conclusions.

      (7) A clearer picture of how PV cell inhibition changes with Erbb4 KO would be achieved with optogenetically evoked IPSPs, rather than changes in mini frequency.

      Thank you for the comment. Based on your suggestions, we used optogenetics to activate PV interneurons and recorded the optogenetically evoked inhibitory postsynaptic currents (oIPSCs) in MCs. As shown in the revised Figure 9 and Supplementary Figure 1F and 1G, deleting ErbB4 in PV interneurons in the OB weakened the inhibitory modulation of MCs by PV interneurons.

      Reviewer #3 (Public review):

      Summary:

      The authors investigate the role of ErbB4 in parvalbumin (PV) interneurons within the olfactory bulb (OB) and its regulation of odor discrimination behavior in mice. They demonstrate that odor discrimination increases ErbB4 kinase activity and that the loss of ErbB4 in the OB impairs the dishabituation of odor response and discrimination of complex odors. The study also characterizes the expression of ErbB4 in the OB, showing it is enriched in PV neurons. Furthermore, the authors utilize a mouse model in which ErbB4 is knocked out in PV neurons and perform a variety of behavioral, electrophysiological, and local field potential (LFP) recording experiments to characterize alterations in olfactory bulb activity. They then use a model in which ErbB4 is specifically knocked out in PV neurons in the OB and show that this manipulation disrupts odor-related behaviors in mice.

      Strengths:

      The study's strengths lie in its use of a diverse range of techniques, including RNAscope, IHC, and Western blotting, to assess the presence of ErbB4 in PV neurons within the OB. Additionally, the authors employ various behavioral tests to evaluate the effects of ErbB4 manipulation in different mouse models, alongside comprehensive electrophysiological experiments and LFP recordings to examine the impact of these manipulations on OB physiology.

      Weaknesses:

      While the data presented in this paper are interesting, several major concerns reduce my enthusiasm for this study, as outlined below:

      (1) In reviewing Figure 1C/D, there are several concerns regarding the clarity and interpretation of the data:

      (a) While the Western blot for ErbB4 in other figures (Figure 1F, 2I) of the manuscript shows a clear single band, the blot presented in Figure 1C (for both p-ErbB4 and total ErbB4) shows multiple bands, which is unexpected. This discrepancy raises concerns about the consistency of the results.

      (b) The data presented in Figure 1D uses only 3 mice per group, and the reported p-value of 0.0492, while technically significant, is very close to the threshold. This raises concerns about the robustness of the finding, especially given the small sample size. Additionally, the p-ErbB4 band intensity in the Go/No-Go condition in Figure 1C does not appear to show a clear increase over the Go/Go condition, which is not congruent with the bar graph in Figure 1D showing a 50% increase in p-ErbB4/ErbB4 levels.

      (c) It is a standard practice in many journals to include full, uncropped Western blot images as supplementary material. This transparency helps ensure that no bands are selectively shown or omitted and increases confidence in the presented data.

      Thank you for your comment and thoughtful suggestion.

      (a) The multiple bands observed for both p-ErbB4 and total ErbB4 in the original Figure 1C are likely attributable to the high concentration of the primary antibody used initially (Santa Cruz Biotechnology), which has since been discontinued. In the revised manuscript, we have replaced the original antibody with an anti-ErbB4 antibody (Cat# 4795, Cell Signalling Technology), which showed a single ErbB4 band (the revised Figure 1C). To detect p-ErbB4, we first performed immunoprecipitation with a phosphorylated tyrosine antibody to enrich the total phosphorylated proteins, followed by immunoblotting for ErbB4.

      (b) According to your comments, we have expanded the sample size to four mice per group and modified the statistical test to an unpaired t-test in the revised Figure 1D.

      (c) We included all relevant uncropped blot images in the Supplementary Material (the revised Figure 1, 2—figure supplement 1).

      (2) In Figure 2, the authors used the anti-ErbB4 antibody sc-283 from Santa Cruz to assess the expression of ErbB4 in PV neurons and the absence of its expression in PV-ErbB4 knock-out mice. However, this particular antibody has been shown to produce non-specific bands in Western blotting and also generate non-specific labeling in IHC. This non-specificity has been demonstrated in Vullhorst et al. (2009, J Neurosci), raising significant concerns about the reliability of the data generated using this antibody.

      Thank you for the comment. As you have indicated, the non-specificity of the anti-ErbB4 antibody sc-283 has been reported in J Neurosci (Vullhorst et al, 2009). These antibodies have been widely used in numerous recent studies (PMID:39543371 and PMID:41297670), indicating their utility for assessing ErbB4 expression under appropriate experimental conditions (primary antibody dilution and incubation conditions). As shown in the revised Figure 2I and 2J, the absence of ErbB4 expression in PV-ErbB4 knock-out mice proved the specificity of the antibody for immunofluorescence staining. To address these potential concerns, we conducted a rigorous validation tailored to our model. In the revised manuscript, we complemented the protein-level detection with RT-PCR, which directly validated the specific knockout of Erbb4 mRNA in PV neurones (the revised Figure 2F-H). Additionally, we performed follow-up immunofluorescence staining experiments using a well-validated anti-ErbB4 antibody (19943-1-AP, Proteintech; see PMID: 37060105) to assess the expression of ErbB4 in PV neurones (the revised Figure 9B and 9C).

      (3) In reviewing the statistical analysis for the series of odor discrimination tests, there could be a potential issue with the clarity of the significance testing. Although the figure legend reports the F and p values from the two-way ANOVA, it is unclear whether these values represent the main effects or the results of a post hoc test. Additionally, it is not clear whether the asterisk in the figures reflects significance from a post hoc test or from the overall ANOVA. The methods section does not explicitly state whether a post hoc test was performed to assess differences between the knockout and control groups. Given that the tests were conducted across multiple days or conditions, a post hoc test that can adjust for multiple comparisons would be necessary to accurately identify where specific differences between the groups exist.

      Thank you for your comment and suggestion. For the odour discrimination tests, two-way ANOVA was followed by Tukey’s post hoc adjustment for multiple pairwise comparisons, which is explicitly stated in the revised Methods section (Lines 832-833). According to your suggestions, we have revised the figure asterisks to indicate significant post hoc differences between the groups.

      (4) Throughout the manuscript, the authors use different mouse models, including ErbB4 knockout specifically in the OB (AAV-Cre-GFP), ErbB4 knockout in PV interneurons throughout the brain (PV-ErbB4-/-), and ErbB4 knockout in PV interneurons within the OB (AAV-PV-Cre-GFP). For Figures 4 and 5, the authors use the PV-ErbB4-/- model to examine odor-evoked activity and neural oscillations within the OB. Since the knockout affects PV interneurons across the entire brain, it is difficult to disentangle whether the observed changes in the OB are due to local effects or broader network alterations elsewhere in the brain.

      Thank you for the comment. We first clarify the rationale for initially using the whole-brain PV-Erbb4<sup>-/-</sup> model: this model is well-validated and widely adopted in in vivo electrophysiological studies targeting brain region-specific phenomena, such as regulating synaptic plasticity in the hippocampus (PMID:24050403) and modulating sensory coding in the cortex (PMID: 37069344).

      Additionally, PV interneurons in the OB are local-projection neurones that exert stronger and more extensive inhibitory effects on M/TCs, a key feature that restricts their functional impact primarily to the local OB circuit rather than broader cross-brain network interactions, further supporting the relevance of the global model for OB-focused research.

      Furthermore, local AAV-Cre injections have notable experimental limitations in our electrophysiological recordings. Stereotaxic infusion induces mechanical trauma and local inflammation in the OB, altering basal circuit activity independent of ErbB4 deletion. AAV also yields incomplete mosaic gene ablation among PV interneurons, introducing a variable knockout efficiency that complicates the interpretation of local electrophysiological readouts. In comparison, the global PV-Erbb4<sup>-/-</sup> line mediates uniform, complete ErbB4 deletion across all PV interneurons, avoiding viral artefacts and rendering our OB electrophysiological measurements more reliable for assessing endogenous local circuit function.

      (5) While the electrophysiological experiments shown in Figures 6-8 provide valuable insights into the reduced inhibition to MCs in PV-ErbB4 knockout mice, it appears that the authors did not record from PV interneurons themselves. Since PV interneurons are central to the proposed mechanism, directly recording them would provide critical information on how the ErbB4 knockout affects their intrinsic properties, synaptic inputs, and firing behavior. Without these direct recordings, the conclusions about the specific role of PV neurons in regulating MC activity remain somewhat indirect. Prior studies have established that knockout of ErbB4 in PV interneurons reduces mEPSC frequency in PV neurons (Del Pino et al., 2013).

      Thank you for your valuable comment and suggestion. According to your suggestions, we have supplemented the electrophysiological experiments (the revised Figure 7—figure supplement 1) with direct recordings from PV interneurons in ex vivo slices. These recordings revealed that ErbB4 knockout alters some properties of PV interneurons (e.g. action potential frequency), reduces mEPSC frequency (consistent with Del Pino et al., 2013), and modulates their firing behaviour, directly confirming that ErbB4 deletion affects PV interneurons.

      (6) In Figure 9, the authors knock out ErbB4 in PV neurons in the OB with AAV-PV-Cre-GFP and show with western blotting that ErbB4 expression is reduced in the mouse injected with AAV-PV-Cre-GFP. However, it is not clear whether ErbB4 was selectively knocked out in PV neurons without the quantification from IHC assays.

      Thank you for the comment. To verify the selective knockout of ErbB4 in OB PV neurones, we performed an additional experiment: immunofluorescence co-staining for PV and ErbB4; quantitative analysis confirmed a significant reduction of ErbB4 in PV interneurons in AAV-PV-Cre–injected mice (the revised Figure 9B and 9C).

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      Other concerns:

      (1) No supplemental Figure 1 was shown.

      We apologise for the oversight. Supplemental Figure have been included in the revised manuscript (the revised Figure 2—figure supplemental 2).

      (2) In line 59, page 3, abbreviations of mitral/tufted cells (M/TCs) or "MCs" were confusing.

      We have clarified the abbreviation by explicitly defining "mitral cells (MCs)", with "M/TCs" retained for mitral/tufted cells to avoid ambiguity (Line 56-59).

      (3) The quality of blots in Figure 1C was less satisfactory, with lots of noisy bands. Maybe antibodies from Cell Signaling should be used.

      We optimised the experiment as suggested. In the revised Figure 1C, we have used an anti-ErbB4 antibody (Cat# 4795, Cell Signalling Technology) combined with the immunoprecipitation-immunoblotting workflow.

      (4) The authors should describe the serotype as well as the promoters of AAV-Cre-GFP used in the experiments.

      As you suggested, we have supplemented the details of AAV-Cre-GFP in the Methods section: Viruses driven by the CAG promoter, including pAOV-CAG-EGFP-T2A-Cre (catalogue No. CN396, serotype AAV2/8) and pAOV-CAG-EGFP-2A (catalogue No. CN394, serotype AAV2/8) were purchased from Obio Technology, Shanghai, China (Lines 568-571).

      (5) The authors should describe the binary mixtures of isoamyl acetate Vs. Heptanone. Simply 6/4 Vs. 4/6 is not easy to follow.

      As you suggested, we have clarified the binary odour mixtures in the Results section: (60%/40% binary mixtures of these odours, "6/4" refers to 60% isoamyl acetate + 40% heptanone, and "4/6" refers to 40% isoamyl acetate + 60% heptanone, in volume) (Lines 111-113).

      (6) Figure 1G, "0 limonene" AAV-Cre-GFP group did not show the error bar.

      We apologise for the omission—error bars for the "0 limonene" AAV-Cre-GFP group have been added to the revised Figure 1.

      (7) Figure 2A, the green signal for ErbB4 was not that strong, it was hard to visualize the expression of ErbB4 in five layers of OB.

      Thank you for the comment. The revised Figure 2A shows an enhanced green signal for ErbB4, clearly indicating its distribution in all OB layers.

      (8) The authors should clearly label or indicate the cell type of neurons recorded in Figure 6, Figure 7, and Figure 8A-8C.

      As you suggested, we have clearly labelled the cell types in the revised Figures 6, 7, and 8A–8C: all recorded neurones are mitral cells (MCs).

      (9) line 320-321, page 14, "Figures 8F and 8G, a burst of conditioning 320 stimuli (40 pulses at 100 Hz)", the authors should indicate the stimuli as a tick or scale on Figures 8F and 8I.

      As per your suggestion, we have added scales and vertical ticks to the revised Figures 8F and 8I to indicate the timing of the conditioning stimuli (40 pulses at 100 Hz).

      Reviewer #2 (Recommendations for the authors):

      (1) Figure 1F is not quantified.

      As suggested, we have supplemented the quantitative analyses of Figure 1F (see the revised Figure 1G) and the statistical details in the revised legend.

      (2) Figures 2G and H are not quantified.

      As suggested, we have supplemented the quantitative analyses of Figures 2G and 2H (see the revised Figures 2H and 2J), and statistical details are provided in the revised figure legends.

      (3) Bar plots with standard error are not suitable for visualizing the distribution of data. Either show violin plots, histograms, or raw data points throughout.

      As suggested, we included the raw data points in the revised manuscript.

      (4) Figure 3 legend - (Wen et al., 2010) citations repeated.

      Thank you for the comment. We have removed the repeated (Wen et al., 2010) citation in the revised manuscript.

      (5) Does Ebbr4 deletion change the waveform shape of PV+ cells? This could influence spike sorting and cell classification.

      Thank you for the comment. According to your recommendations, we performed additional ex vivo patch-clamp recordings of PV+ interneurons, which showed that ErbB4 knockout did not alter their action potential waveform shape (e.g. spike amplitude and half-width, the revised Figure 7—figures supplement 1D and 1E). Importantly, this knockout also did not directly affect the spike waveform shapes of M/TCs in vivo (e.g. peak-to-valley ratio and half-valley width, the revised Figure 4—figures supplement 1C-1E). Therefore, we speculate that spike sorting and cell classification were not affected.

      (6) Line 327 - is this really a measure of inhibitory circuit plasticity?

      Thank you for the comment. We have replaced "inhibitory circuit plasticity" with "inhibitory circuit activity" and comprehensively updated all relevant instances throughout the manuscript to ensure consistent use of the term.

      (7) In the discussion: "Another interesting finding is that the changes in spontaneous firing rate differed for odor-evoked excitatory and inhibitory responses in vivo, suggesting that ErbB4 in PV interneurons dynamically regulates the spontaneous activity of M/TCs in response to different odors." The significance of this finding is not discussed and it is not clear what this result means. For example, does this relate to a "winner-take-all scenario"?

      Thank you for the comment. According to your recommendations, we have discussed the significance of this finding in the revised Discussion section (Lines 438-449):

      This result reveals a dual regulatory role of ErbB4 in PV interneurons in olfactory coding. For odour-evoked excitatory responses, PV interneurons (via ErbB4) constrain M/TC spontaneous firing at a low baseline, minimising background noise and enhancing the SNR. In contrast, the inhibitory responses maintain a higher spontaneous firing baseline to accentuate odour-evoked suppression. This regulation amplifies the "excitation of excited M/TCs and inhibition of inhibited M/TCs," a hallmark of the OB’s "winner-take-all" mechanism that sharpens odour identity coding, which is critical for odour discrimination. These data confirm that ErbB4 in PV interneurons does not exert a global modulation, but dynamically tailors M/TC spontaneous activity to odour-evoked responses, thereby optimising the ability of the OB to resolve olfactory cues.

      (8) The discussion on linking AD with odor discrimination impairments, and the potential role of Erbb4 was interesting. However the discussion of "fluctuation status" is not defined. What does this refer to?

      According to the comment, we have added the following wording to the Discussion section (Lines 478-497):

      As referenced by Iemi et al. (2022), "fluctuation status" herein refers to the spontaneous, endogenous fluctuations in neural activity that occur in the brain prior to sensory stimulation (i.e. pre-stimulus) or in the absence of external sensory input. External cues do not drive this state but arise from intrinsic neural dynamics, and it is primarily characterised by changes in the power of neural oscillations across multiple frequency bands (e.g., alpha, beta, and their neighbouring frequencies, collectively termed "alpha+ band" in Iemi et al. (2022)). Critically, this fluctuation status is distinct from stimulus-evoked neural responses; it reflects a pre-existing "baseline" state of the neural system that modulates subsequent sensory processing and behaviour. Consistent with Iemi et al. (2022), previous work has established that such ongoing neural fluctuations strongly predict behavioural variability in both health (e.g. slower reaction times and reduced perceptual accuracy) and disease (e.g. age-related cognitive decline and schizophrenia) by regulating neuronal excitability. In our study, we extended this concept to olfactory function, focusing on "broad ongoing fluctuations" (encompassing multiple frequency bands) and linking their dynamics to OB output. Specifically, these fluctuations influence the ability of the OB to support rapid recovery from olfactory adaptation and to mediate complex odour discrimination, thereby uncovering a novel role for endogenous neural fluctuation status in olfactory circuit function.

      Reviewer #3 (Recommendations for the authors):

      (1) For Figure 1C, I strongly recommend that the authors include full, uncropped Western blot images for both p-ErbB4 and total ErbB4 as supplementary material to improve the transparency and credibility of the findings.

      As you suggested, we have supplemented the full, uncropped western blot images for both phosphorylated ErbB4 (p-ErbB4) and total ErbB4, as the revised Figures 1 and 2 and Supplementary Figure 1.

      (2) The authors should either validate the specificity of the sc-283 antibody in their experimental conditions or consider using a more specific antibody for ErbB4 to ensure the reliability of their data.

      Thank you for your comments. As shown in the revised Figure 2I and 2J, the absence of ErbB4 expression in PV-ErbB4 knock-out mice proved the specificity of the antibody for immunofluorescence staining. To address these potential concerns, we conducted a rigorous validation tailored to our model. In the revised manuscript, we complemented the protein-level detection with RT-PCR, which directly validated the specific knockout of Erbb4 mRNA in PV neurones (the revised Figure 2F-H). Additionally, we performed follow-up immunofluorescence staining experiments using a well-validated anti-ErbB4 antibody (19943-1-AP, Proteintech; see PMID: 37060105) to assess the expression of ErbB4 in PV neurones (the revised Figure 9B and 9C).

      (3) I recommend that the authors clarify in the methods section whether a post hoc test with multiple comparison adjustments (e.g., Tukey's HSD or Bonferroni) was conducted for the behavioral tests presented throughout the study. If no such test was performed, it would be beneficial to include one to ensure accurate identification of significant differences between groups across the different experimental days or conditions.

      For the behavioural tests, we confirmed that two-way ANOVA was followed by Tukey’s post hoc adjustment for multiple pairwise comparisons, which has been clarified in the revised Methods section (Lines 832-833). Additionally, we have revised the asterisks in the relevant figures to clearly indicate significant post-hoc differences between the groups.

      (4) The rationale for using a whole-brain PV-specific knockout model (PV-ErbB4-/-) to assess OB-specific phenomena in Figures 4 and 5 should be clarified. I also recommend the authors provide or conduct additional experiments with OB-specific knockouts to determine whether the effects observed in Figures 4 and 5 are directly attributable to the loss of ErbB4 in PV interneurons within the OB.

      To clarify the rationale, the whole-brain PV-Erbb4<sup>−/−</sup> mouse line was initially used to characterise the overall functional relevance of ErbB4 in PV interneurons for OB activity and odour-evoked responses. We clarified this rationale in the revised Results section (Lines 210-211 and Lines 250-251).

      As elaborated above, AAV-mediated OB-specific knockouts suffer from injection-induced tissue injury, incomplete mosaic recombination, and uncertainties in local electrophysiological recordings, which would compromise data reliability. Moreover, OB PV interneurons act predominantly as local circuit neurones; therefore, the phenotypes observed in Figures 4 and 5 most plausibly arise from intrinsic ErbB4 deletion within bulbar PV cells rather than from long-range brain-wide network changes. For these reasons, we consider our current global PV-Erbb4<sup>−/−</sup> model appropriate to interpret the local OB circuit effects here, and we outline OB-targeted knockout manipulations as a direction for future independent follow-up research.

      (5) To strengthen their conclusions drawn from Figures 6-8, the authors should perform direct recordings from PV interneurons in the OB to assess how the ErbB4 knockout affects their intrinsic properties, synaptic inputs, and firing behavior. This would provide more direct evidence of PV interneuron dysfunction in the knockout mice.

      According to your recommendations, we have performed direct recordings of OB PV interneurons using ex vivo patch-clamp electrophysiology (the revised Figure 7—figures supplementary 1). These recordings reveal that ErbB4 knockout affects the intrinsic properties of PV interneurons, synaptic inputs (reduced mEPSC frequency and amplitude, the revised Figure 7—figures supplementary 1A and 1B), and firing behaviour (increased action potential frequency, the revised Figure 7—figures supplementary 1C), directly confirming that ErbB4 deletion affects PV interneurons themselves. These results provide direct evidence of PV interneuron dysfunction in the knockout mice.

      (6) I recommend that the authors assess molecular markers of PV interneuron inhibition, such as GAD67, in PVIs. This would help link the ErbB4 knockout to impaired PV interneuron function and its downstream effects on MC inhibition.

      Thank you for the comment. We attempted to detect GAD67 in OB PVIs using multiple commercial antibodies but encountered consistent technical limitations (e.g. weak signal specificity and high background) that precluded reliable quantitative analysis.

      To address this gap, we used optogenetics to activate PV interneurons and recorded optogenetically evoked inhibitory postsynaptic currents (oIPSCs) in MCs. As shown in the revised Figure 9 and Supplementary Figure 1F and 1G, deleting ErbB4 of PV interneurons in the OB weakened the inhibitory modulation of MCs by PV interneurons. This result provides direct electrophysiological evidence linking ErbB4 knockout to impaired PV interneuronal function and its downstream effects on MC inhibition.

      (7) For Figure 9, I recommend that the authors perform IHC to show that ErbB4 is selectively knocked out in PV neurons but not in non-PV neurons within the OB, as the Western blot analysis alone does not provide this specificity.

      According to your recommendations, we performed an additional key experiment: immunofluorescence co-staining for PV and ErbB4, with quantitative analysis confirming a significant reduction in ErbB4 in OB PV interneurons, but not in non-PV cells, in AAV-PV-Cre–injected mice (the revised Figure 9B and 9C).

    1. Author response:

      The following is the authors’ response to the previous reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      The authors demonstrate the stereoselective role of D-serine in 1C metabolism showing that D-serine competes with L-serine and inhibits mitochondrial L-serine transport. They observe expression of 1C metabolites in their metabolomics approach in primary cortical neurons treated with L-serine, D-serine and mixture of both. Their conclusions are based on the reduction in levels of glycine, polyamines and their intermediates and formate. Single cell RNA sequencing of N2a cells showed that cells treated with D-serine enhanced expression of genes associated with mitochondrial functions such as respiratory chain complex assembly and mitochondrial functions with downregulation of genes related to amino acid transport, cellular growth and neuron projection extension. Their work demonstrates that D-serine inhibits tumor cell proliferation and induces apoptosis in neural progenitor cells highlighting the importance of D-serine in neurodevelopment.

      Strengths:

      D-amino acids do not merely function as ligands at receptors but have underlying roles in signaling and metabolism. These roles are just beginning to be uncovered. The authors elucidate the metabolic role of D-serine in the context of neuronal maturation by its suppression of mitochondrial L-serine availability for SHMT2 and 1C flux. This is the strength of the manuscript. The implications for the metabolic role of D-serine in neurons is a highlight and underlines its roles in neuronal metabolism.

      Thank you for the positive assessment.

      Weaknesses:

      These are some minor issues that come up on critical assessment of the manuscript and is only intended to strengthen the manuscript. The comments below are based on the revisions made by the authors including the justification of their approach and rebuttal.

      (1) Kinetic assessment of D-serine versus L-serine: The authors have made reference to prior work by Miyamoto et al. and justify their rationale. This is acceptable.

      (2) Molecular Dynamics simulations while a good first step in modeling interactions at the active site, relies on force fields. The authors state that any elaborate study into longer simulations is beyond the scope and their simulations data are supported by other experimental work. This is justified.

      (3) The use of N2a cell line is also justified to reflect the proliferative nature of immature neurons.

      (4) With regards to caspase 3 comment, the whole blot is convincing and shows cleaved caspase-3 band at approx. 15 kDa.

      (5) Scale Bars are clearly visible and Fig S6 which was earlier S5 is legible. If possible, the authors can include an magnified inset in the merged image to show the clear activation of caspase-3.

      (6) Issue of phosphatidyl serine standard in LC-MS is justified by the use of L-serine standard due to lack of availability.

      (7) The authors mention about enantiomeric shift of serine metabolism during neural development which appears to be a discussion of prior published data from Hubbard et al 2013, Burk et al 2020, and Bella et al 2021 in Supplementary Figure panels 8 A-E.

      The authors justify by citing references to the work which may be acceptable and also the current norms of publication. This reviewer felt contrary to the fact, however it is left to the editors to make a decision on this.

      (8) The discussion section has been substantially revised and now reads well.

      (9) The relevant references have been cited. In doing so, the work integrates and elucidates a mechanistic and functional role of D-serine in neurons.

      (10) Figure S7A in the revised manuscript shows the specificity of D-serine in the cleaved caspase-3 assay which is informative.

      Comments on revised version.

      This reviewer is satisfied by the effort made by the authors based on the prior comments raised.

      Thank you for understanding our explanation.

      Reviewer #2 (Public review):

      Summary:

      This study by Suzuki et al. reports an interesting stereo-selective role of D-serine in regulating one-carbon metabolism during neurodevelopment to adapt the functional transition, probably through the competition with mitochondrial transport of L-serine. The authors provide a multi-layered set of evidence, including metabolomics, enzyme assays, mitochondrial transport competition and functional assays in immature/neural progenitor cells, to build up a conceptual integration of D-serine as both a neurotransmitter and a metabolic regulator in central neural system, which raises a broad potential interest to the neuroscience and metabolism communities.

      Strengths:

      This work provides a conceptual advance that D-serine is not only serves as a traditional neurotransmitter in central neural system but also critically contributes to metabolic regulation of neural cells. The authors performed solid metabolomic assays to validate the suppressive effect of D-serine on one-carbon metabolic pathway, providing some evidence that D-serine competitively inhibits mitochondrial serine transport, but not directly impairs SHMT2 enzymatic activity. All these data indicate a critical role of D-serine synthesis during neural maturation and suggest a potential translational strategy for targeting serine metabolism in neural tumors.

      Comments on revised version.

      My previous concerns have been appropriately addressed or discussed in this revised version of manuscript. I have to say that, at this stage, I have no further questions.

      Thank you for understanding the value of our study.

      Reviewer #3 (Public review):

      Summary:

      This manuscript presents a comprehensive and well-executed investigation into the metabolic role of D-serine in the central nervous system. The authors provide solid evidence that D-serine competitively inhibits mitochondrial L-serine transport, thereby impairing one-carbon metabolism. This stereoselective mechanism reduces glycine and formate production, suppresses cellular proliferation, and induces apoptosis in immature neural cells and glioblastoma stem cells. Developmental analyses further reveal a physiological enantiomeric shift in serine metabolism during neurogenesis, aligning with the transition from proliferation to maturation. Overall, the study bridges developmental neurobiology, cancer metabolism, and amino acid transport, uncovering a previously unrecognized metabolic function of D-serine beyond its role in neurotransmission.

      Strengths:

      (1) The discovery that D-serine inhibits one-carbon metabolism by competing for mitochondrial L-serine transport-rather than through enzymatic inhibition or receptor-mediated signaling-represents a significant and previously underappreciated mechanism. This finding has broad implications for understanding metabolic regulation during neurodevelopment and offers potential relevance for targeting metabolic vulnerabilities in cancer.

      (2) The authors integrate metabolomics, mitochondrial transport assays, molecular dynamics simulations, genetic and pharmacologic perturbations, transcriptomics, and both in vitro and ex vivo models. The breadth of experimental approaches, combined with the coherence of the findings across systems, provides strong support for the central conclusions and enhances the overall impact of the study.

      (3) The temporal shift in D-/L-serine levels during neurodevelopment is elegantly linked to the transition from proliferative to mature neuronal states. The selective vulnerability of neural progenitors and tumor cells-contrasted with the resistance of mature neurons-highlights a biologically meaningful and potentially targetable metabolic distinction.

      Thank you for recognizing the importance of our study.

      Weaknesses:

      (1) While the authors attribute D-serine's metabolic effects to competition with mitochondrial L-serine transport, the specific identity of the transporter(s) mediating this process remains undefined. This represents a meaningful mechanistic gap, as the central conclusion depends on D-serine limiting mitochondrial L-serine availability to inhibit one-carbon metabolism.

      Thank you for the comments. We acknowledge that defining the specific identity of L-serine transporters that are interfered by D-serine requires further studies.

      (2) The effective concentrations of D-serine used in vitro (IC₅₀ ≈ 1-2 mM) exceed typical brain levels (~0.3 mM). While the authors acknowledge this, a more focused discussion on whether higher local D-serine concentrations could arise in specific microenvironments-such as synaptic compartments, tumor niches, or pathological states-would help contextualize the in vitro findings and strengthen their physiological relevance. For example, disruptions in D-serine clearance or altered expression of serine racemase and transporters in disease contexts could lead to localized accumulation. Moreover, differences between extracellular and intracellular D-serine pools-and the mechanisms governing their regulation-may further influence its metabolic impact in vivo.

      Thank you for this suggestion. However, since we have discussed these points in lines 479-492, we chose not add any additional sentences in order to avoid losing the focus of this paper with speculation.

      (3) While the manuscript focuses on neural stem/progenitor cells and neural tumors, it remains unclear whether the anti-proliferative effects of D-serine are specific to neural lineages or extend to other highly proliferative non-neural cell types. A brief discussion addressing this point would help clarify the scope of D-serine's metabolic impact and whether its mechanism of action reflects a unique vulnerability in neural cells or a more general feature of proliferative metabolism. This distinction is particularly relevant for assessing the broader therapeutic potential of targeting mitochondrial L-serine transport.

      The reviewer raised an interesting point. While we speculate that other cancers requiring L-serine for proliferation may also be affected by D-serine, in this study we focused on central nervous system tumors because D-serine is produced in the central nervous system. Since cancer cells may have different metabolic profiles regardless of their tissue of origin, it would be meaningful to compare the expression profiles of metabolism-related genes with their sensitivity to D-serine.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      A minor suggestion to the authors is to include a summary schematic to clarify the main finding of the paper.

      Since there is a lot of data in the manuscript ranging from MD simulations and metabolomics and other data sets, an overall summary schematic will help the readers with a take home message.

      Thank you for the great suggestion. We added a summary schematic in Figure 4 -figure supplement 10.

      Reviewer #2 (Recommendations for the authors):

      The authors have addressed my previous concerns and further included appropriate discussions on their conclusions. I have no further questions.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      This study by Tsuji et al. explores a mechanical threat model in Drosophila using air puffs as a stimulus. The authors first establish the paradigm and show that air puffs induce cardiac deceleration along with increased locomotion. They then identify dopamine as a key regulator of this response and go on to map the underlying circuit. In doing so, they pinpoint two pairs of DA-WED neurons as critical players. They carefully used intersectional strategies to achieve relatively clean labeling of these neurons, which helps ensure that the observed effects can be attributed specifically to DA-WED neurons. They further show that DA-WED neurons are both required and sufficient to drive cardiac deceleration, and that their activity increases in response to air puff stimulation. These neurons also contribute to the locomotor response. Directly inducing cardiac deceleration via optogenetic manipulation of cardiomyocytes also increases locomotion, suggesting a link between cardiac state and behavioral output.

      Strengths:

      Overall, the experiments are thoughtfully designed, well-controlled, and clearly presented. The figures are easy to follow, and the conclusions are generally well supported by the data. The manuscript is also clearly written, with a discussion that acknowledges potential caveats and outlines future directions. The genetic tools, behavioral paradigm, heart rate measurement approaches, and stimulation methods introduced here will be valuable resources for the community.

      Weaknesses:

      A few minor points to add to the clarity of the manuscript:

      (1) The DA-WED driver (R48A08-AD ∩ VT008692-DBD ∩ TH-FLP) appears quite clean in the brain. However, since the study focuses on cardiac function and locomotion, it would be helpful to check expression in cardiomyocytes and the ventral nerve cord. This would help rule out any off-target expression that might contribute to the phenotypes and further support the idea of a descending pathway from brain dopaminergic neurons.

      We thank reviewer#1 for this thoughtful comment. We have indeed checked the expression pattern of the DA-WED driver (R48A08-AD ∩ VT008692-DBD ∩ TH-FLP) throughout the body, and failed to detect noticeable expression outside the brain (Supplementary Fig. 6d in the original manuscript). As for the heart, the whole tissue was cleared and confocal-imaged from the dorsal side. As cardiomyocytes are positioned directly beneath the dorsal cuticle of the abdomen, the expression of a driver can be best assessed this way. In contrast to the lack of apparent expression in cardiomyocytes, we could see clear expression in DA-WED neurons in the brain in the same sample (Supplementary Fig. 6d). In this experiment, however, potential expression in VNC could have been missed, as VNC is positioned on the ventral side and thus further away from the objective lens. We thus conducted an additional experiment in which we dissected out the brain + VNC and checked the driver’s expression. Our confocal imaging results revealed no expression in VNC. We have included this data in our updated manuscript as Supplementary Fig. 6e.

      (2) Since DA-WED>Kir2.1 abolishes the puff-induced locomotor response (Figure 5b), suggesting that DA-WED neurons are directly involved in mediating locomotion. In the model (Figure 5L), it might make more sense for the pathway from mechanical threat to locomotion to pass through DA-WED neurons. The authors could consider adjusting the schematic if they agree.

      As the reviewer pointed out, Kir2.1-mediated suppression of DA-WED neurons almost completely abolished puff-induced locomotion. In our original schematic, we included a pathway from mechanical threat to locomotion that bypassed DA-WED, reflecting the possibility that locomotion could be driven by multiple pathways. We agree, however, that this possibility was not directly supported by our data and that the near-complete suppression of puff-induced locomotion upon DA-WED silencing more strongly supports a model in which the predominant flow of information from puff detection to locomotion passes through DA-WED neurons. We have therefore removed the direct arrow from mechanical threat to locomotion and added a dashed arrow from DA-WED neurons to locomotion, representing a pathway that may promote locomotion independently of DA-WED-mediated cardiac deceleration (Fig. 5m; Supplementary Fig. 9i).

      We have updated the legend of Fig. 5m as follows:

      “Model. DA-WED neurons promote locomotion, through and/or bypassing interoception of the heartbeat (dashed arrows).”

      We also updated the legend of Supplementary Fig. 9i as follows:

      “Model. Air puff promotes locomotion while suppressing grooming. Mechanistically, air puff activates DA-WED neurons. DA-WED neurons drive not only cardiac deceleration but locomotion, potentially through a feedback from cardiac deceleration (dashed arrows). Such a DA-WED-based mechanism fails to influence grooming.”

      (3) In line 408, Figure 5K should be 5L as it's a discussion of the model.

      We thank reviewer#1 for pointing this out. Accordingly, we have made the following corrections:

      L436-439: “cardiac deceleration is accompanied by increased locomotion (Fig. 5e-l). Our data points to a scenario in which DA-WED neurons induce cardiac deceleration upon mechanical threat, which may in turn influence threat-induced locomotion (Fig. 5m).”

      (4) In Figure 5j, the x-axis is missing time labels. Even if it matches Figure 5h, adding labels would make it easier to interpret at a glance.

      We agree with reviewer#1 and added the x labels to Fig. 5j, and also to the second panels of h, j, and l.

      (5) In line 312, it would be helpful to briefly explain why a 28 ms light pulse was used, compared to other pulse durations elsewhere in the paper.

      Our system synchronized behavior, heartbeat, and optogenetics at 70 Hz (14-ms intervals). Because mechanical threat transiently elongated beat-to-beat intervals typically by 20 - 23ms, we chose 28-ms (2-frame) stimulation to best mimic this effect, over 14 (1-frame) or 42 (3-frame) ms (Fig. 1; Supplementary Fig. 2b, e, f). We have added this explanation to our manuscript, as follows:

      L326 - 328: “To approximate the 20–23 ms beat-to-beat prolongation evoked by mechanical threat (Fig. 1; Supplementary Fig. 2e, f), we used 28-ms (2-frame) green light pulses.”

      (6) The cardiac deceleration seems to recover quickly after the air puff ends, whereas the locomotor response persists longer (around 10-15 seconds; see Figure 1 and Figure 5). This difference might suggest that DA-WED neurons influence locomotion through an additional or partially independent pathway, beyond their role in cardiac regulation. It could be worth briefly discussing this possibility.

      We agree that the time course of puff-induced locomotion (Fig. 1f, Fig. 5a) is more persistent than DA-WED activation (Fig. 4f) or cardiac deceleration (Fig. 1d, Fig. 4b). Also, silencing DA-WED neurons partially reduced puff-induced cardiac deceleration (Fig. 4c) but appears to have more strongly abolished puff-induced locomotion (Fig. 5a, b). Given that our interoception model is only partially tested, we agree that it is better to mention the possibility that DA-WED neurons might influence locomotion through an additional or partially independent pathway beyond their role in cardiac regulation.

      Our “Limitation of this study” section in our original manuscript touched on this issue, as follows (L430-432):

      “Although cardiac deceleration can promote locomotion, we have not directly tested whether it is required for DA-WED–evoked locomotion, leaving open the possibility of parallel downstream pathways.”

      But to be more explicit, in our updated manuscript, we also included the following discussion:

      L439-441: “We note, however, that our data does not exclude the possibility that DA-WED neurons might influence locomotion at least partially independent of its role in cardiac deceleration”

      Reviewer #2 (Public review):

      Summary:

      The authors study cardiac deceleration during threat responses in Drosophila. Particularly, it focuses on identifying the neuronal control of this deceleration. Using behavioral and cardiac tracking and analysis, genetics, and calcium imaging, they identify two pairs of dopaminergic neurons involved in cardiac deceleration during air puff responses

      Strengths:

      The study is overall well done, and the paper is clearly written. Particularly, the work on identifying the two pairs of dopaminergic neurons involved in cardiac deceleration using a series of drivers and generating new ones is rigorous and extensive. Finally, the authors manipulate the heartbeat to investigate how it influences threat responses

      Weaknesses:

      There are, however, several points that need to be clarified, as some claims are not entirely supported by evidence.

      The authors, for example, claim that dopaminergic neurons are responsible for cardiac deceleration (during the air puff, lines 182-3, page 9). However, based on the work in this study, it seems that other neurons could be involved in this control as well. In addition to dopaminergic neurons, the authors test serotonergic and octopaminergic neurons, which, based on silencing experiments, also show an implication in heart-beat deceleration. Furthermore, because they find that dopaminergic neurons are the only ones that, upon thermogenetic activation, lead to lower heart beat frequency, they conclude that the dopaminergic neurons are responsible for air -puff induced cardiac deceleration.

      However, these activation experiments are done in a different context than the air puff experiments (at a higher temperature, which could have an effect on the heartbeat changes upon activation of different neuron groups), and because silencing of other monoaminergic neuron types during the air puff also resulted in less cardiac deceleration, one cannot exclude the implication of octopaminergic or serotonergic neurons in air-puff-induced deceleration.

      Activation experiments without high temperatures (using, for example, optogenetics) and/or in the presence of the air puff would be important to determine that the dopaminergic neurons are the main type of monoaminergic neurons involved in air-puff-induced cardiac deceleration. Otherwise, the related claims should be rephrased in a way that clearly doesn't exclude a possible implication of other monoaminergic neurons.

      We thank reviewer#2 for raising an important point. Our intention was not to claim that dopaminergic system is solely responsible for puff-induced cardiac deceleration. What we meant to convey in our original manuscript was that, after conducting experiments shown in Fig. 2, dopaminergic system was the one that made most sense to focus on, as the other system failed to show consistent results across loss- and gain-of-function experiments. We acknowledge, as reviewer #2 rightly pointed out, that consistency across loss- and gain-of-function experiments is not a logical necessity for given neurons to be causally contributing to a brain function, especially in this case where loss- and gain- of-function experiments were conducted at different temperatures. We have revised our manuscript to more precisely express our view outlined above, as follows:

      L194-196: “Together, our data demonstrates that, while not excluding the contributions of serotonergic or octopaminergic systems, dopamine system is responsible for puff-induced cardiac deceleration.”

      Regarding the interactions between the cardiac deceleration and locomotion, the authors propose, based on the results, that the optogenetic cardiac deceleration is sufficient to induce an increase in locomotion, and that it is the decrease in heartbeat that would be responsible via interoceptive pathways to trigger an increase in locomotion. In the model they propose, the DA-WED neurons would induce a decrease in heartbeat that, in turn, would trigger an increase in locomotion. There is not enough proof that cardiac deceleration is the one that triggers an increase in locomotion during air puff responses. As the authors themselves state, the experiments that would demonstrate this would involve preventing cardiac deceleration while optogenetically activating DA-WED. It can therefore not be excluded that the DA-WED neurons trigger an increase in locomotion that is possibly modulated by the cardiac activity. Both alternatives should be considered (models in Figures 4 and 5).

      We thank the reviewer for this insightful comment, which is also consistent with reviewer#1’s view. We agree that it is better to mention the possibility that DA-WED neurons might influence locomotion through an additional or partially independent pathway beyond their role in cardiac regulation, which our data does not exclude. In our updated manuscript, we included the discussion as below:

      L433-441: “Our results provide partial support for such a model. We show that (1) mechanical threat induces cardiac deceleration and locomotion (Fig. 1), (2) DA-WED neurons in the brain are responsible for threat-induced cardiac deceleration and locomotion (Fig. 4; Fig. 5a-d), (3) optogenetic cardiac deceleration is accompanied by increased locomotion (Fig. 5e-l). Our data points to a scenario in which DA-WED neurons induce cardiac deceleration upon mechanical threat, which may in turn influence threat-induced locomotion (Fig. 5m). We note, however, that our data does not exclude the possibility that DA-WED neurons might influence locomotion at least partially independent of its role in cardiac deceleration.”

      Reviewer #3 (Public review):

      Summary:

      In this elegant study, Tsuji et al. identify a relationship in Drosophila between cardiodynamics and threatening stimuli where mild air puffs elicit a brief bradycardia that coincides with locomotion increases. They then take advantage of the arsenal of genetic tools available in the fruit fly to reveal the indispensability of dopamine, through the action of Dop1R2, in this phenomenon. Further, they pinpoint the source of this dopamine to two specific pairs of neurons - DA-WED that are threat-activated. They then test and find a potential role for cardiac interoception from the heart in linking behavior and cardiodynamics.

      Strengths:

      This is an interesting and timely story that brings together the tools of fruit fly systems neuroscience and links it with physiology. The experiments are well done and tell a very nice story. In particular, the primary message of the paper - that the authors have identified specific dopaminergic neurons that regulate cardiac activity - is sound.

      Weaknesses:

      There are no important problems with the scientific approach. Rather, there are some interpretive changes I would consider.

      (1) The changes in heart rate are small (10% or so), and, as far as I can tell, are evident for a beat or two. So the data may be better interpreted not as a change in rate but as a lengthening of diastole for a beat or two. That may seem a petty difference, but it might point to particular stretch-activated systems or changes in blood flow as the determinant.

      Heart rate must be averaged over time, and so might be blurring the effects. It may be useful to produce figures centered on beat count and duration rather than time. Because the effect may even be just on a single beat, we suggest the authors try plotting the average beat duration for each beat that follows the air puff. If it's really just the first beat, using a quantification of the change of this duration relative to the average that precedes the puff may produce more striking figures.

      We thank reviewer#3 for this insightful suggestion, which also relates to the reviewer’s next comment. We tried plotting the average beat duration for each beat that follows the air puff, relative to beats preceding the puff. The reviewer’s prediction turned out to be partially true – our plot of beat-to-beat interval vs beat count around puff revealed that the interval indeed increased for the three beats following puff across different puff strengths (Supplementary Fig. 2e). Consistently, the average interval over three beats before and after puff per fly revealed larger differences for 50mL/min and especially 200mL/min but no noticeable changes for 20mL/min, so that now we detect similar cardiac deceleration across puff strength (Supplementary Fig. 2f). However, this novel analysis unfortunately came with slightly larger variance overall (Supplementary Fig. 2f). We thus prefer to stick to HR in the present manuscript, but still agree that this is valuable for a more comprehensive understanding of cardiac puff responses. We included our new plot as Supplementary Fig. 2e, f, with the following description in the Result section:

      L121-122: “Indeed, the beat-to-beat interval increased over the three beats following puff onset, and this increase was comparable across puff strengths (Supplementary Fig. 2e, f).”

      (2) The author's model that cardiac deceleration leads to walking data is only partially supported by their data. In the first figure, the relationship between cardiac deceleration and walking probability seems to be inverted relative to their model (weak stimulus -> strong cardiac effect and weak locomotor effect; strong stimulus-> weak cardiac effect and strong locomotor effect). It is possible that this discrepancy may disappear when the authors look at beat duration rather than heart rate (for instance, if following the strong stimulus, there is a very long beat that is followed by tachycardia, thus weakening their observed HR change). It would also be easier to relate this data in Figure 1 to their interoceptive model if some data were shown that illustrated the relative timing of the cardiac change and the locomotor start.

      Following the reviewer's suggestion, we re-examined the cardiac response using the beat-to-beat interval rather than heart rate. As the reviewer anticipated, this partially resolves the apparent discrepancy. Averaging the interval over the three beats before and after the puff (per fly) reveals a significant increase in beat-to-beat interval at every puff strength, with comparable magnitude across strengths (Supplementary Fig. 2e, f). However, since a comparable cardiac response, in terms of beat-to-beat interval, is accompanied by a graded locomotor response, locomotion cannot be driven by cardiac deceleration alone. Indeed, puff-induced cardiac deceleration and locomotion fail to correlate (added as Supplementary Fig. 10a in our updated manuscript). In contrast, optogenetic cardiac deceleration does increase locomotion (Fig. 5h-k), and with a strong correlation between optogenetically activated cardiac deceleration and locomotion (added as Fig. 5l in our updated manuscript). Taken together, locomotion is likely driven by both cardiac deceleration and a parallel, cardiac-independent pathway, with the latter accounting for the puff-strength dependence (Fig. 5m). We added the following description in the Result section:

      L121-122: “Indeed, the beat-to-beat interval increased over the three beats following puff onset, and this increase was comparable across puff strengths (Supplementary Fig. 2e, f).”

      Regarding the relative timing, we added a dedicated figure as Fig. 1h, which shows that the onsets of the cardiac and locomotor changes are approximately concurrent across puff strengths. They differ in their peak timing — the cardiac deceleration reaches its extremum in roughly 0.2 – 0.5 s, while the walking fraction peaks later (roughly 1 – 1.5 s). We have added the following to the Result section:

      L127-139: “A close inspection of the peri-stimulus dynamics revealed that the onsets of the cardiac and locomotor changes were approximately concurrent at puff onset across strengths (Fig. 1h). Furthermore, the peak of cardiac deceleration (roughly 0.2 – 0.5 s post puff onset) preceded that of locomotor increase (roughly 1 – 1.5 s post puff onset). Especially at lower puff strengths, locomotor response showed an additional transient dip, embedded in dominant and persistent locomotion, almost concurrently, but in the case of 50 mL/min following, cardiac deceleration (Fig. 1h). Overall, cardiac and locomotor responses begin together, and the cardiac response reaches its peak before the locomotor response does. These data are consistent with the idea that cardiac and locomotor responses are coordinated, and that cardiac deceleration may causally contribute to the locomotor response. We therefore set out to identify the neurons responsible for cardiac deceleration and to test their causal role directly.”

      We have also updated our corresponding Discussion section (chapter 1) accordingly:

      L369-389: “Cardiac deceleration is coordinated with defensive locomotion

      Our data show that air puff stimulation induces cardiac deceleration together with increased locomotion (Fig. 1). Across puff strengths, locomotion scaled with stimulus strength, whereas the cardiac deceleration did not: measured as time-binned HR, it was less pronounced at stronger puffs, while measured as the beat-to-beat interval it was comparable across strengths (Fig. 1d–h; Supplementary Fig. 2f). This indicates that locomotion is not simply a graded readout of cardiac deceleration.

      Although cardiac deceleration is often associated with freezing in mammals [1], cardiac deceleration has also been observed during early threat detection and orienting responses [78], suggesting that it reflects engagement of a defensive processing rather than motor inhibition per se. Consistent with this view, dissociation between threat-evoked cardiac modulation and freezing has been reported across taxa. In mammals, for example, disruption of autonomic output can abolish cardiac deceleration without eliminating freezing [79]. Similarly, in decapod crustaceans and Drosophila, visual stimuli elicit reproducible and time-locked changes in heart rate that accompany both freezing and fleeing [8,9,80]. While these studies establish that cardiac modulation can be dissociated from freezing, our findings additionally demonstrate that cardiac deceleration can co-occur with a predominantly locomotor response to mechanical threat and can itself causally contribute to locomotion (Fig. 5e-m). Cardiac deceleration is therefore not restricted to passive defensive states, but can act upstream of active locomotor responses.”

      We also examined HR-versus-locomotion relationships trial-by-trial and fly-by-fly, but trial-to-trial fluctuations in both signals were too large to pinpoint the timing of changes at that level, which is why we present the population peri-stimulus dynamics in Fig. 1h.

      (3) Also, since the locomotor and cardiac changes are probabilistic, it would be very useful to see how their respective probabilities change when conditioned on the other. According to their interoceptive model, locomotion should preferentially increase on trials where cardiac deceleration occurs. The authors should discuss this incongruity and also potential alternative interpretations of their cardiac manipulation experiments. Perhaps the bradycardia makes them more sensitive to threats - as suggested in the introduction? Control flies show a mild increase in locomotion following green light (Figure 5j), so perhaps by slowing the heart, they are more sensitive and thus respond more strongly to this stimulus?

      We believe that cardiac and locomotor changes are predicted to be congruent across flies only if locomotion is solely dependent on cardiac changes. Our optogenetic cardiac deceleration experiment likely corresponds to such a situation, and we indeed observed a strong correlation between cardiac and locomotor changes for retinal-fed test group but not for retinal-unfed control group (which we now present as Fig. 5l).

      As for stimulus-induced locomotion, it may reflect contributions from cardiac-state-independent locomotor pathways (Fig. 5m). In such a situation, cardiac and locomotor changes are not necessarily predicted to be congruent. Indeed, puff-induced locomotion and cardiac changes do not appear to be congruent across flies (which we now present as Supplementary Fig. 10a).

      We have added these plots as Fig. 5l and Supplementary Fig. 10a, and added the following explanation in the main text:

      L335 - 341: “Furthermore, optogenetically induced changes in HR and locomotion were strongly anti-correlated fly-wise in the retinal-fed test group (Pearson’s correlation coefficient: -0.81, p-value: 0.00538) but not in the control group without retinal (Pearson’s correlation coefficient: 0.43, p-value: 0.436) (Fig. 5l). This contrasts with puff-induced responses, in which changes in HR and locomotion were not significantly correlated (Supplementary Fig. 10a). This lack of correlation may reflect contributions from cardiac-state-independent locomotor pathways.”

      As for the possibility of bradycardia promoting locomotor response to threats (light), We thank the reviewer for raising this alternative interpretation. We agree that our experiment does not distinguish whether cardiac deceleration directly promotes locomotion or instead enhances the locomotor response to the green-light stimulus itself. Indeed, retinal-unfed control flies showed a modest increase in locomotion following green-light illumination, indicating that the light can itself influence behavior. Thus, the larger locomotor response in retinal-fed flies could in principle reflect an interaction between the optogenetically induced cardiac state and this sensory response.

      We note, however, that this interpretation would still imply a causal influence of cardiac state on behavior: cardiac deceleration would increase the gain of an externally evoked locomotor response rather than directly initiating locomotion. Because our experiment does not discriminate between these possibilities, we have revised our manuscript to state that experimentally induced cardiac deceleration can promote locomotion or potentiate a light-evoked locomotion.

      L346–L350: "We also note that retinal-unfed controls showed a modest locomotor increase following green-light illumination (Fig. 5j, k), leaving open whether cardiac deceleration directly promotes locomotion or potentiates a light-evoked locomotion. In either case, our data support a modulatory influence of cardiac state on locomotor output.”

      We thank the reviewer for significantly strengthening our manuscript.

      (4) Looking at the example shapes of the beats in Figure 5g versus Figure 1c, the optogenetically induced diastole has a very different shape from the naturally occurring long beat. Thus, the exact cardiac stimulus may be unnatural. If this is true across trials and animals, it may be worth considering that the funny beat (like an anxiogenic atrial fibrillation in mammals) is the source of the fear and, in turn, locomotor behavior (also interesting!) rather than being a true replication of the cardiac events seen following the puff stimulus.

      We thank the reviewer for this insightful comment. We agree that the optogenetically induced cardiac deceleration does not fully reproduce every feature of the puff-induced heartbeat, and we have been careful not to claim that it does. Our aim was to test whether cardiac deceleration can influence locomotor state, not to claim that the optogenetically induced beat is an exact replica of the puff-induced response.

      At the level of HR, the two manipulations were closely matched: both produced an ~10% reduction with a similar time course. They differed in the finer beat-to-beat structure — the optogenetic deceleration was concentrated in a transient prolongation at stimulus onset, whereas the puff-induced deceleration was distributed across several beats (Supplementary Fig. 10). In both cases, however, the M-mode recordings show that the heart maintained an organized rhythm, with the manipulation producing a transient diastolic prolongation rather than sustained beat-to-beat irregularity (Fig. 1c, Fig. 5g). This argues against the possibility that a fibrillation-like funny beat underlies the behavioral effect, but leaves open the possibility of light-induced one long interval, vs puff-induced long intervals across three consecutive beats, may have contributed to behavior. We also note that our current imaging system does not yet permit a comprehensive comparison of finer heartbeat features, such as full contraction dynamics, waveform shape, stroke volume/ejection fraction, or beat-pattern irregularity quantified across trials and animals. We therefore do not intend to exclude the possibility that specific features of the optogenetically induced beat pattern contribute to the behavioral effect — an interesting question that we agree is worth pursuing.

      We have revised the manuscript accordingly. We now state, with an added figure (Supplementary Fig. 10), that the optogenetic experiment supports that experimentally induced cardiac deceleration can modulate locomotor behavior, but does not establish that the artificial cardiac pattern is identical to the mechanically evoked response. We also note the open possibility that distinct heartbeat patterns may themselves influence defensive behavior.

      L343–L346: " One limitation is that our optogenetically induced cardiac pattern (Fig. 5g; Supplementary Fig. 10b, c) is not necessarily identical to its mechanically induced counterpart (Fig. 1c; Supplementary Fig. 10d, e), which could have influenced locomotion.”

      L321-324: “To directly test whether cardiac deceleration can influence locomotion, we optogenetically induced cardiac deceleration of a magnitude comparable to the puff-induced response by expressing the light-gated anion channel GtACR1 in cardiomyocytes using Hand-GAL4 (Fig. 5e).”

      Assessing how heartbeat pattern influences behavior will require improved whole-heart imaging and more detailed quantitative analysis of heartbeat dynamics, which we are currently developing but consider beyond the scope of the present study.

      Recommendations for the authors:

      Reviewer #2 (Recommendations for the authors):

      Recommendation for the authors:

      (1) In the introduction section (around line 43), it would be important to also include relevant work on the relationship between cardiac activity and threat responses in Drosophila (Barrios et al, 2021) as this study describes the internal physiological states of fruit flies during defensive responses (including the changes in heartbeat).

      We thank the reviewer for pointing this out. The suggested paper was referenced in our original Introduction but slightly later (L78) than the location suggested by the reviewer (L44). We have now included this reference in L44 as well.

      (2) Activation experiments could be performed in the presence of an air puff. The authors show that the stronger the air puff rate, the stronger the response. Low or medium air puff could be used during optogenetic activation of serotonergic and octopaminergic neurons, and see if the activation of different neuron types enhances cardiac deceleration and increase of locomotion (to levels similar to those observed, for example, at high puff rates). Otherwise, the claim that the dopaminergic system is solely responsible should be rephrased.

      We agree that the suggested experiment can more reliably assess the potential contribution of serotonergic and octopaminergic systems. However, our intention was not to claim that dopaminergic system is solely responsible for puff-induced cardiac deceleration. Rather, consistency across loss- and gain-of-function experiments led us to focus on dopaminergic system, which allowed us to identify DA-WED neurons. We have revised our manuscript to more precisely express our view outlined above, as follows:

      L194-196: “Together, our data demonstrates that, while not excluding the contributions of serotonergic or octopaminergic systems, dopamine system is responsible for puff-induced cardiac deceleration.”

      (3) Since there is not enough proof that cardiac deceleration is the one that triggers an increase in locomotion during air puff responses and cannot be excluded that the DA-WED neurons trigger an increase in locomotion that is further modulated by the cardiac deceleration. Both options should be considered (models in Figures 4 and 5, results and discussion).

      We thank the reviewer for this insightful comment, which is also consistent with reviewer#1’s view. We agree that it is better to mention the possibility that DA-WED neurons might influence locomotion through an additional or partially independent pathway beyond their role in cardiac regulation, which our data does not exclude. In our updated manuscript, we added to our schematic model an arrow emanating from DA-WED to locomotion directly (Fig. 5m), explaining our interpretation in the corresponding legend. We also included the discussion as below:

      L439 - 441: “We note, however, that our data does not exclude the possibility that DA-WED neurons might influence locomotion at least partially independent of its role in cardiac deceleration.”

      (4) Pages 14-15 (and in discussion). It appears that in some cases, puff and threat are used interchangeably, which may be confusing, as for example the authors ask if DA-WED could be general threat detectors in this context, meaning, if I understand correctly, that they are involved in all the aspects of the behavioral response to an air puff. However, the term general threat detector may be understood to mean not specific to air puff but also other types of threats, which is not addressed in this study. I suggest this be rephrased to avoid confusion. Also, they should be clear in the text when they refer specifically to air puff threats and when to threat responses.

      We thank the reviewer for this important clarification. We swapped the phrase “general threat detectors” with “puff detectors” for precision. We have revised our manuscript accordingly, as follows:

      L306 - 320: “An alternative interpretation is that DA-WED neurons function as mere puff detectors that broadly regulate puff-evoked behaviors. If this were the case, manipulating these neurons should affect all behavioral outputs induced by puff. In addition to promoting locomotion, air puff suppressed grooming predominantly within 3 s of puff onset, consistently across puff strengths; grooming during the later 10–20 s window was variable, either remaining suppressed, returning to baseline, or reversing to an increase depending on puff strength (Supplementary Fig. 9a–c). However, silencing DA-WED neurons failed to disrupt puff-induced grooming suppression (Supplementary Fig. 9d–f), despite markedly reducing cardiac deceleration (Fig. 4b, c) and locomotion (Fig. 5a, b). Likewise, photoactivation of DA-WED neurons failed to suppress grooming (Supplementary Fig. 9g–i), while robustly inducing cardiac deceleration (Fig. 4i, j) and locomotion (Fig. 5c, d). Thus, manipulation of DA-WED neurons does not reproduce the full behavioral repertoire triggered by puff. These findings argue against the idea that DA-WED neurons function as mere puff detectors and instead support a more specific role in coordinating cardiac and locomotor responses.”

      To better distinguish “external threat” vs “threat responses”, we have also made the following changes in our main text:

      L303-305: “These findings suggest that DA-WED neurons coordinate cardiac deceleration with locomotor responses upon mechanical threat.”

      L341-343: “These observations are consistent with the possibility that cardiac deceleration may influence locomotor responses upon mechanical threat”

      L437-439: “Our data points to a scenario in which DA-WED neurons induce cardiac deceleration upon mechanical threat, which may in turn influence threat-induced locomotion (Fig. 5m).”

      L477-478: “While our data are consistent with a model in which DA-WED neurons couple cardiac deceleration to locomotor responses upon mechanical threat”

      (5) In Supplementary Figure 3, the R74C07 labels anterior and posterior sensilla. Since the external sensilla on the posterior abdomen were excluded based on the Aes1N driver's result, the phenotype is likely due to the anterior sensilla. However, those are not included in the summary in the i) panel. Why is that?

      We thank the reviewer for pointing this out. Our policy was that “When multiple drivers labeled the given neurons, we considered such neurons as indispensable for cardiac deceleration only when those drivers produced consistent results (hence, e.g. external sensilla on the posterior abdomen were excluded based on Aes1N driver's result, despite R74C07 driver's result suggests otherwise)”. Accordingly, sensilla on the eye compound (“anterior” sensilla in reviewer’s comment) labeled by R74C07 driver were excluded by “R38B08AD-VT043775DBD” split combination’s result. Our original legend of Supplementary Fig. 3i explained our policy, but to avoid confusion, our updated legend now includes above explanation as well, as follows:

      “(hence, e.g. external sensilla on the posterior abdomen were excluded based on Aes1N driver's result, despite R74C07 driver's result suggests otherwise; similarly, sensilla on the eye compound labeled by R74C07 driver were excluded by “R38B08-AD VT043775-DBD” split combination’s result).”

      (6) There seems to be a strong off response to air puff in medial and not in lateral DA-WED neurons, suggesting that the single pair of neurons could have a different function in the context of air puff responses. That should be discussed.

      We agree with the reviewer that there may be differences in puff responses in medial vs lateral DA-WED neurons (Supplementary Fig. 8c). We have included this in our Result section as follows:

      L281 – 283: “We note, though, that the medial neurons tended to show offset response-like activities more pronounced than their lateral counterparts (Supplementary Fig. 8c), potentially hinting at functional heterogeneity within DA-WED neurons.”

      (7) Grooming: In Supplementary Figure 9c, although not significant, the silencing of DA-WED does seem to have an effect on the grooming profile- averaging over the 10-second time window does not reveal a significant effect, but a finer analysis may reveal some differences. There seems to be an increase in grooming after 10s? (in e-h).

      We added the 10–20 s window data as Supplementary Fig. 9c, f, i, l. We note, however, that this window falls outside the period of robust puff-evoked grooming suppression. In wild-type flies, air puff suppressed grooming predominantly within 3 s of puff onset, and this suppression was consistent in direction across all puff strengths (Supplementary Fig. 9a, b). Grooming during the 10–20 s window, by contrast, was variable, either remaining suppressed, returning to baseline, or reversing to an increase depending on puff strength (Supplementary Fig. 9a). We therefore regard the 0–3 s window as reflecting the most reliable puff-evoked grooming response. Within this window, we did not detect statistically significant effects of neuronal or cardiac manipulation on the grooming suppression. Independently of this, we also examined the average grooming fraction during the 10–20 s window: the apparent differences there are driven by a few unusually high-magnitude values and are not statistically significant even when those values are retained (Supplementary Fig. 9f, i, l).

      We also made the following changes to the Results section (and added Supplementary Fig. 9c, f, i, l):

      L308 – 317: "In addition to promoting locomotion, air puff suppressed grooming predominantly within 3 s of puff onset, consistently across puff strengths; grooming during the later 10–20 s window was variable, either remaining suppressed, returning to baseline, or reversing to an increase depending on puff strength (Supplementary Fig. 9a–c). Silencing DA-WED neurons failed to disrupt puff-induced grooming suppression (Supplementary Fig. 9d–f), despite markedly reducing cardiac deceleration (Fig. 4b, c) and locomotion (Fig. 5a, b). Likewise, photoactivation of DA-WED neurons failed to suppress grooming (Supplementary Fig. 9g–i), while robustly inducing cardiac deceleration (Fig. 4b, c) and locomotion (Fig. 5c, d)."

      L333 – 334: “In contrast, this manipulation failed to alter grooming behavior (Supplementary Fig. 9j-l).”

      We also spotted an inaccurate description in our original legend, which read “Change in grooming fraction, calculated for each fly as the % difference between the mean fraction during the 10 s following stimulation onset and the mean fraction during the 10 s baseline period preceding stimulation.” This was an error, and we have instead used “during the 3 s following stimulation onset” window as we accurately described in our original Method (L579 – 582: “Puff-induced changes in walking and grooming were quantified by comparing the mean fraction during the 10 s and 3 s, respectively, following puff onset with the mean fraction during the 10 s baseline period preceding puff onset.”). We have corrected this error in our updated legend. We apologize for any confusion this error might have caused.

      Reviewer #3 (Recommendations for the authors):

      (1) Showing the model in Figure 4k as puff in parallel leads to locomotor effects independently of DA-WED, which is incongruent with the next figure where they discuss their interoceptive model. It might be useful to present the interoceptive model as a competing model in 4K that will be tested in the following figure.

      Our intention there was to graphically summarize the tentative model that was plausible consistent with data presented in Fig.1-4. While we much appreciate the reviewer’s suggestion, we prefer not to present interoception idea in Fig. 4k: since the interoception idea comes from observations in Fig. 5a-d, we fear that presenting interoception model in Fig. 4k could be confusing without looking at Fig. 5a-d. Still, the reviewer’s suggestion gave us an opportunity to revisit our manuscript’s structure and for that we are thankful.

      (2) The effect the authors observe is similar to one that has been [1.1] recently published in zebrafish larvae (Herrera et al. 2026 and Hernandez-Nunez et al. 2026), where lengthened heartbeats accompany active avoidance behavior following threats. Interestingly, this effect seems to be particularly conserved amongst smaller animals like fish larvae and insects, where heartbeats may represent a stronger sensory stimulus. It may be worthwhile for the authors to discuss these parallels. Further, some of the difficulties about interpreting direct optogenetic manipulation of cardiac function are discussed and explored in the Herrera et al. paper.

      We thank the reviewer for highlighting these studies and this intriguing parallel. We agree the correspondence across distant taxa is striking. In larval zebrafish, cardiac dynamics and behavioral state are coupled following threat (Herrera et al., 2026), and dedicated vagal sensory neurons encode HR, including subsets responsive to cardiac deceleration, through a largely stimulus (including optogenetic cardiac pacing)-invariant population code (Hernandez-Nunez et al., 2025). Together with the demonstration in mice that optogenetically induced tachycardia can drive an anxiety-like state (Hsueh et al., 2023), and our present findings in Drosophila, these results suggest that cardiac-interoceptive influence on behavior is a broadly shared feature of nervous systems across taxa.

      We find intriguing the reviewer's suggestion that such coupling may be especially relevant in small animals. Indeed, in small animals, the heart may perturb the internal state more globally - in small animals, the per-beat change in physiological state relative to body size may be proportionally larger, rendering each beat a stronger signal rather than being buffered by a large, compartmentalized vasculature. Alternatively, the compactness of small nervous systems could allow an interoceptive cardiac signal to reach motor circuits through few intervening synapses. In Drosophila, almost any neuron can reach any other within roughly four synapses (Scheffer et al., 2020; Dorkenwald et al., 2024; Schlegel et al., 2024), although whether synaptic path lengths are shorter in Drosophila than in larger brains remains unknown. We note, however, that the demonstration of cardiogenic affective control in mammals (Hsueh et al., 2023) indicates the phenomenon is not restricted to small animals, and so we consider the size question open.

      Finally, following the reviewer's pointer to the interpretive considerations raised by Herrera et al., we have added text acknowledging that our optogenetic manipulation may engage the cardiac state through multiple routes. The term interoception is used broadly to include neural as well as humoral, blood pressure, or gas-exchange-related sensing of the cardiac state, and we note that distinguishing among these routes would require targeted manipulations we have not performed.

      We have added the following section to our Discussion:

      L453 – 474: “ Cardiac dynamics can modulate behavior

      Our findings echo a growing body of work linking cardiac dynamics to behavior across distant taxa. In larval zebrafish, cardiac dynamics and behavior are coupled during threat [85], and dedicated vagal sensory neurons encode HR, including its decreases, through a stimulus-invariant population code86. In mice, optogenetically induced tachycardia can drive anxiety-like behavior [87]. And here we find that cardiac deceleration accompanies, and can promote, locomotion in Drosophila. Cardiac influence on behavior thus spans insects, fish, and mammals.

      How cardiac state might be sensed in Drosophila is unknown, and several routes are conceivable. Drosophila heart receives rich neuronal innervation [51,52], although whether these neurons relay sensory information from the heart is unknown. If so, neurons could directly detect the heartbeat, analogous to the cardiac afferents that mediate cardiac interoception in vertebrates [86,87]. Alternatively, the heartbeat could be sensed mechanically or through gas-exchange-related cues. In mammals, the cardiac pressure pulse can be detected directly within the brain by mechanosensitive central neurons88. In zebrafish, cardiac activity can causally influence behavior through its oxygen supply [85]. In insects, although the circulatory architecture differs, the heartbeat contributes to pressure changes in the hemocoel and tracheal system and resultant gas exchange [89,90], which could in principle be detected. While present study does not distinguish among these possibilities, establishing how cardiac state is sensed would provide a foundation for dissecting how central commands and peripheral physiological states interact to coordinate survival behaviors.

      (3) Serotonergic inhibition or knockout seems to diminish cardiac deceleration (lines 159-162), yet activation leads to increased heart rate (lines 170-171). The authors should discuss some possible explanations for this paradoxical result.

      While we can only speculate, one possibility is that serotonergic neurons modulate cardiac control in a context-dependent manner. During mechanical threat, serotonergic activity is indispensable for cardiac deceleration, perhaps by gating the threat-responsive cardiac deceleration pathway involving DA-WED. In contrast, thermogenetic activation of serotonergic neurons outside this context may recruit broader downstream targets, including circuits that induce cardiac acceleration. We have added the following sentences in our Result:

      L183 – 187: “Serotonergic system, on the other hand, provided paradoxical results (Fig. 2g-k, Supplementary Fig. 5c-g): this could be because serotonergic system is required for threat-induced cardiac deceleration, while broad serotonergic activation outside this context possibly engages downstream circuits that promote cardiac acceleration.”

      (4) The split-GAL4 technology is a well-established approach in Drosophila research. The authors don't need to go into so much detail about its mechanism in the results (lines 199-205).

      We have compressed our detailed explanation about split-GAL4 technology as follows:

      L212 – 214: “In this approach, GAL4 is divided into DBD and AD hemi-drivers, and functional GAL4 is reconstituted only in cells expressing both components (Fig. 3c).”

    1. Author response:

      Reviewer #1 (Public Review):

      Summary:

      This study by Z. Moradi, S. Jahedazad, and colleagues presents a refined two-choice assay paradigm for investigating thermotactic behavior in groups of Drosophila melanogaster. The authors developed an experimental setup that maintains a stable temperature profile and utilized supervised classifiers based on extracted locomotion parameters to distinguish between temperature conditions within the arena as well as antennal ablation status. The integration of a Braitenberg vehicle model to simulate fruit fly exploration patterns and U-turn behaviors at thermal boundaries represents a valuable contribution to the study of collective thermotaxis.

      Strengths:

      (1) The detailed description of the behavioral assay and the rigorous calibration methods make the experimental setup reproducible.

      (2) The incorporation of a state-of-the-art animal tracking system enables the precise extraction of multiple locomotion parameters, providing valuable insights into the fruit fly exploration as well as for predicting temperature-dependent behavioral responses. The methodology could be potentially adopted in other studies.

      (3) The authors' decision to study thermotactic behavior in groups is a noteworthy addition. The finding that overall staccato movement patterns remain largely unaffected by antennal ablation, while the frequency and duration of pairwise encounters increase with temperature, offers valuable insights into individual sensory processing vs the influence of collective behavior.

      Weaknesses:

      (1.1) The study investigates groups of fruit flies, which is an interesting contrast to previous single-fly studies. While group dynamics are mentioned as potentially important, no direct comparison or analysis was conducted between individual vs group, which would have been a straightforward and valuable addition. 

      We appreciate the reviewers' suggestion regarding a direct single-fly versus group-fly comparison. In response, we have added a preliminary analysis comparing single-fly and group-fly trials, with the results presented in the revised manuscript under “Group-Enhanced Heat Avoidance in Drosophila Correlated with Pairwise Encounter Duration” This analysis provides an initial assessment of whether the group-level heat avoidance response differs from that observed in individual flies.

      We must, however, be transparent about the limitations of this additional data. Due to exceptional conditions in Iran during this period, and the completion of the degree program under which this research was conducted, a full comparative dataset could not be collected. The analysis presented is therefore based on preliminary data and should be interpreted as indicative rather than conclusive, and we have clearly noted this limitation in the manuscript.

      We would also like to clarify the scope and intent of this work. As engineers, our primary contribution is methodological: we aimed to develop tools and a framework for temperature-response analysis in Drosophila, with particular focus on enabling such analysis at the collective level, a setting that has received comparatively less attention. A direct behavioral comparison between single and multi-fly conditions was not the original objective of this study. We believe the core contribution of the paper, the arena implementation methodology, analysis pipeline, and collective behavior characterization, stands independently, and we hope the added preliminary comparison addresses the reviewers' concern in the spirit in which it was intended.

      (1.2) The strength of intergroup interactions remains unclear, as the pairwise encounter parameters appeared to have low significance according to the importance factor analysis.

      Thank you for raising this point. First of all, we would like to clarify that, in response to this and concern 21, we have revised the figure, which was previously based on one-way ANOVA scores, to a permutationbased feature importance score (Figure 3). This updated method better reflects the functional contribution of each feature in relation to our trained classifiers. As demonstrated, for the classification of antennal deficits, encounter duration emerges as the fourth most significant feature affecting classification performance. 

      Moreover, we inserted a new section “Group-Enhanced Heat Avoidance in Drosophila Correlated with Pairwise Encounter Duration”, deeply explain the relationship between enhanced AI values in groups (than individual trials) and pairwise interactions.

      We recognize that the impact of social interactions on group thermal responses is a compelling yet underexplored area that deserves further investigation. Therefore, we included some suggestions in the “Limitations and Future Directions” section of our updated manuscript.

      (2) The manuscript does not clearly articulate the novelty of the work; the innovative aspects are present but not effectively highlighted.

      We appreciate your comment and have revised the manuscript accordingly. In particular, we have revised the Introduction section, which now includes a detailed explanation of the novelty of our work and highlighting its distinctions from previous related studies.

      (3.1) The descriptions of the locomotor parameters and Braitenberg modeling, which constitute the most critical components of the study, are not optimally presented in the main text. 

      We revised our manuscript. For your reference, please check out “Table 1” and the “A Simple Braitenberg Vehicle Recapitulated Fly Heat-Avoidance Navigational Strategy” section.

      (3.2) The authors should provide a more detailed rationale for why certain locomotion parameters emerged as more influential (i.e., with higher importance scores) than others. Additionally, clearer explanations from a physical or mechanistic perspective would help readers better appreciate and interpret the significance of these findings.

      We tried to consider this in the entire revision process of our manuscript.

      Reviewer #2 (Public Review)

      The authors develop an experimental framework to precisely control temperature in an arena and make quantitative measurements of thermal avoidance behavior in Drosophila. They find that wild-type animals show robust heat avoidance behavior and suggest that antennal ablation reduces this heat avoidance. They also make a novel claim that antennal inputs do more than simple heat detection but play a role in navigation strategies like centrophobism and are needed for decision-making at thermal boundaries. The fundamental two-choice behavior paradigm or the use of peltier modules for temperature control have been employed previously in the field. The strength of this work lies in detailed behavioral measurements. However, the study falls short due to a lack of adequate experimental controls. The authors then model this behavior as a classical Braitenberg vehicle of sensory-motor transformation. Overall, the paper has some interesting insights into in-depth analysis of Drosophila navigation in thermal gradients, but their evidence only partially supports their claims.

      Reviewer #3 (Public Review)

      Per my training and expertise, my evaluation and feedback below are focused on the behavioral components of this study and not the modeling. The authors use heat avoidance thermotaxis behavior in adult flies as a behavioral read out of decision-making with the goal of providing a novel quantitative analysis of the navigational strategies that contribute to heat avoidance behavior. Breaking down a specific behavior (here, heat avoidance) into component behavioral motifs can provide a more detailed analysis that can contribute to deeper understanding of navigational strategies within Drosophila and potentially aid understanding of navigational strategies at a broader level. The authors describe temperature preference behaviors, as has been previously reported and examine the role(s) of thermoreceptors localized to the antennae compared to the rest of the fly. The thermotaxis behavior is then broken down into several parameters with the goal of gaining deeper insight into how and when the fly initiates and generates heat avoidance behavior. The work would be further strengthened and clarified by more completely setting the findings within the context of the field both by including relevant citations and via text that describes this within the manuscript. Additionally, while the authors discuss choosing the temperatures in the assay to allow for more "straightforward interpretation", it would be important to note that this might not be what the fly actually experiences and although it might drive a "decision" it might not be revealing the ethologically accurate behavior.  

      We interpret the reviewer’s point as a request to distinguish the temperatures used in our assay from the temperatures a fly would typically encounter in a natural setting. Our selected temperatures were chosen to provide experimentally clear thermal contrasts and facilitate quantitative interpretation; however, the temperature experienced by a fly in nature can vary spatially and temporally and may not correspond to the controlled conditions used here. Thus, a behavioral choice observed in our assay should not automatically be interpreted as an ethologically exact representation of natural thermal decision-making. We have clarified this point in the revised manuscript and now frame the assay as a controlled test of thermotactic behavior rather than a direct reproduction of a natural thermal environment.

      Additionally, Figure 2 in particular can be revised to aid the reader in understanding and evaluating the results. For example, writing out the terms on the y-axis (or making a table a reader could easily reference) and including statistically significant findings on the figure itself would allow the reader to more easily draw their own conclusions. 

      Table 1, included in the revised version, defines locomotor features along with their corresponding symbols. In Figure 2, blue median lines depict significant deviation from the baseline at 25°C for the wild-type group. Moreover, in the same figure, red median lines denote significant differences between wild-type and ablated groups at the warm temperature of 35°C. Features’ values (Mean ± SD) extracted from trials as well as the p-values for suitable overall statistical tests (ANOVA, welch ANOVA, Kruskal-Wallis) are included in the supplementary File 1. Adjusted p-values for all pairwise comparisons in the wild-type group are provided in Table 2.

      Finally, a more thorough discussion would help make the findings more accessible and demonstrate how these findings have the potential to be of broad interest to many disciplines. For example, placing findings in the context of navigation and quantitative behavioral analysis across species and referring to figures within the discussion section itself.

      We agree with the reviewer and have substantially revised the Discussion to better connect our findings to navigation and quantitative behavioral analysis. The revised Discussion places the locomotor features and thermal decision-making results in the broader context of behavioral navigation and explicitly refers to the relevant figures when interpreting the findings. We have also clarified which conclusions are directly supported by the present data and which represent potential broader applications or directions for future work.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Comments:

      (1) The current study focuses on transcriptional regulation of the sex chromosomes. It would be interesting to know whether perturbation of pre-rRNA synthesis also affects transcription of autosomal genes.

      Our RNA-seq analysis shows that BHM-21 treatment markedly affected the transcription of X- and Y-linked genes, with no obvious influence on the transcription of autosomal genes in pachytene spermatocytes (Figure 4B).

      (2) Is ribosome biogenesis still active during prophase I of male meiosis? Additional discussion of the timing and extent of rRNA synthesis at this stage would help place the findings in a broader biological context.

      To determine whether ribosome biogenesis remains active during meiotic prophase I, we examined 47S pre-rRNA levels by qPCR in spermatogonia (Spg) and prophase I spermatocytes. As shown in Figure S2, pre-rRNA transcript levels were extremely low in prophase I spermatocytes compared to Spg, indicating an arrest of rRNA synthesis upon meiotic entry. Notably, we observed prominent redistribution of nucleolar components to the XY body during prophase I. These findings suggest that reduced engagement of nucleolar components in rRNA biogenesis may facilitate their redistribution and their participation in other biological processes. We have added this discussion to the revised manuscript (Lines 283-289).

      (3) A recent preprint reports active RNA polymerase II-mediated transcription of Y chromosome genes within nucleolus-like bodies (NLBs) during prophase I of meiosis in Drosophila male germ cells (https://doi.org/10.64898/2026.05.20.726666). These findings suggest that the meiotic nucleolus may have species-specific roles in regulating sex chromosome gene expression. It would be valuable for the authors to discuss how their findings compare with these observations and the potential evolutionary implications.

      In Drosophila spermatocytes, the nucleolus is reorganized into a nucleolus-like body (NLB). This structure serves as a platform for RNA polymerase II-mediated transcription of Y-linked fertility genes. In contrast, in mouse spermatocytes, nucleolar components such as pre-rRNA and NPM1 are redistributed to the XY body. Their accumulation promotes Pol II exclusion and meiotic sex chromosome inactivation (MSCI). The transcriptional outcomes differ between the two species: Y-linked genes remain transcriptionally active in Drosophila, whereas sex chromosomes are transcriptionally silenced in the mouse. These findings suggest that nucleolar organization has been evolutionarily adapted in a species-specific manner to meet distinct requirements for sex chromosome regulation during spermatogenesis. We have discussed this point in the revised manuscript (Lines 317-326).

      Reviewer #2 (Public review):

      Summary:

      The authors showed the localization pattern of nucleolus components, including Pre-rRNA, a precursor of rRNAs, changes during meiotic prophase I, particularly with the localization of these nucleolar components to the X-Y body, which shows inactivation of RNA polymerase II transcription, during pachynema. The localization of Pre-rRNA depends on ATR kinase and gammaH2AX. The chemical inhibition of rRNA transcription disrupts the binding of pre-rRNA to the X-Y body and suppresses the inhibition of the RNA polymerase II-mediated transcription on the sex chromosomes.

      Strengths:

      The cytological analysis, combined with the chemical inhibition, provided solid evidence to support the idea that, together with the remodeling of the nucleolus structure, pre-rRNA is an essential component of sex chromosome inactivation in male mouse meiosis. The role of pre-rRNA in sex chromosome inactivation in male meiosis helps our understanding of how the X-Y body, which would be a biological condensate, would be formed; e.g. for example, this Pre-rRNA may promote phase separation.

      Weaknesses:

      However, there is limited information on how Pre-rRNA is recruited to only sex chromosomes and how the RNA promotes the inactivation of sex chromosomes. Of course, these will be a target of future study. One major weakness of this paper is a poor description of the results, with fair presentation and interpretation of the data.

      Following the reviewers suggestions, we have modified the manuscript. As listed below, we have addressed all the concerns raised by the reviewers point by point.

      Recommendations for the authors:

      Reviewer #2 (Public review):

      Major points:

      (1) The authors studied the localization of pre-rRNA, which is the center of this study. However, the general structure of this RNA was poorly described in the text. For example, how this pre-rRNA is different from mature rRNAs. Importantly, how the authors detected pre-rRNA, not other rRNA species, should be described in the Figure and the text.

      The primary pre-rRNA transcript contains the sequences that give rise to the mature rRNAs, together with the external transcribed spacers (5′-ETS and 3′-ETS) and internal transcribed spacers (ITS1 and ITS2). During rRNA maturation, these spacer regions are progressively removed through a series of processing steps and are therefore absent from mature rRNAs (PMID: 22342225). To specifically detect pre-rRNA, we performed RNA-FISH using probes targeting the ITS1 and ITS2 regions as described in the Methods section (Line 380-398). This probe design strategy has been reported in our previous study and cited in the Methods section (PMID: 34980897). Following your suggestion, we have now added a brief description of the general structural features of pre-rRNA and its distinction from mature rRNAs in the Introduction (Lines 36-39).

      (2) For the dynamics of the localization of pre-RNA and/or NMP1 during the meiotic prophase I, it is very important to check the localization of these components in zygonema (or leptonema) by ChIP-seq (Figure 2C) to address whether these signals bind to the sex chromosome prior to pachynema.

      As suggested, we performed additional ChIRP-seq and CUT&Tag-seq to detect the localization of pre-rRNA and NPM1 in leptotene/zygotene spermatocytes (GSE346625, GSE346622). The results indicate that neither pre-rRNA nor NPM1 associates with sex chromosomes at the leptonema-zygonema stage prior to pachynema (Revised Figure S3).

      (3) For Pre-rRNA ChIP, how did the author IP the RNA? Do they have specific antibodies against the RNA? Please explain this in the text.

      The pre-rRNA-associated chromatin was not isolated using an RNA-specific antibody. Instead, we employed Chromatin Isolation by RNA Purification (ChIRP), a well-established method for mapping RNA–chromatin interactions (PMID: 24457971). In this assay, biotinylated antisense DNA oligonucleotides complementary to pre-rRNA sequences were used to specifically capture pre-rRNA together with its associated chromatin, followed by streptavidin-based purification. The experimental procedure has been described in the Methods section (Lines 467-475).

      (4) For Pre-rRNA ChIP-seq and CUT&Tag-seq (Fig. 2C, 3C), the signals are enriched in specific genomic regions. Please show where they are and discuss them.

      Pre-rRNA/NPM1 signals appear to be enriched within γH2AX-positive regions of the sex chromosomes (Figure S8). This spatial overlap is consistent with our finding that ATR-mediated DNA damage response signaling drives the sequestration of nucleolar components to the XY body. Supporting this interpretation, inhibition of ATR or loss of H2AX markedly reduced the enrichment of both pre-rRNA and NPM1 on the sex chromosomes. We have discussed this point in the revised manuscript (Lines 155-158).

      (5) In Figure S2, the staining patterns of PLRE1 and FBL are different; FBL seems to bind to chromosome axes, which should be mentioned in the text and, if possible, discussed in terms of the differential localization of nucleolar components on the X-Y body.

      FBL was specifically enriched on the unsynapsed axis of the X and Y chromosomes, where SPO11-mediated DSBs occur. However, POLR1E exhibited a diffuse distribution in the XY body. Thus, it is possible that these nucleolar proteins may be involved in meiosis-related events in the XY body, such as meiotic DSB repair. The differential localization pattern suggests that the nucleolar components may play distinct roles in the meiotic prophase I. We have included the description and discussion of this part in the revised manuscript (Lines 302-306).

      (6) Graphs in Figure 3 showed the order of the binding after ATRi washing: gammaH2AX>NPM1>Pre-rRNA. This kinetic difference is confirmed and should be mentioned in the text (and discussed).

      We agree that the distinct recovery kinetics of γH2AX, NPM1, and pre-rRNA upon ATRi washout support a hierarchical recruitment model. After ATRi washout, γH2AX signals reappeared most rapidly, followed by the gradual re-accumulation of NPM1 and pre-rRNA. This distinct kinetics suggests that ATR-dependent γH2AX signaling precedes the recruitment of NPM1 and pre-rRNA. We have included related information in the revised manuscript (Lines 155-158).

      (7) Figure 3C: It is clear that the absence of pre-rRNA and NMP1 in the gammaH2AX KO testis. It is important to show the localization patterns of these components in pachytene KO cells; e.g., no change in the localization.

      As suggested, we performed additional IF-FISH analysis in wild-type and H2AX-knockout pachytene spermatocytes to examine the subcellular localization of pre-rRNA and NPM1. Both pre-rRNA and NPM1 were prominently enriched at the XY body in wild-type pachytene spermatocytes. In contrast, this XY body-associated enrichment was lost in H2AX-knockout pachytene spermatocytes. Notably, pre-rRNA remained colocalized with NPM1 in H2AX-knockout cells. These observations suggest that H2AX is required for the recruitment of pre-rRNA/NPM1 to the XY body, but is not required for their spatial association. These new data have been included in Figure S9 and described in the revised manuscript (Lines 164-166).

      (8) EU incorporation experiment in Figure 4: Signals of EU in this figure are different from those in Figure1 C. This suggests the distinct loci for rRNA production between leptonema and pachynema. Please explain more. More importantly, it is very important to show the amounts and production rates of ribosomes or rRNAs during distinct stages of prophase I.

      5-EU (5-ethynyl uridine) is a nucleoside analog that is incorporated into all newly synthesized RNA, including both rRNA and mRNA, during active transcription. Therefore, the 5-EU signals we observed reflect the global transcriptional activity of all RNA polymerases (Pol I, Pol II, and Pol III), rather than rRNA production specifically. In pachytene spermatocytes, the XY body undergoes meiotic sex chromosome inactivation (MSCI), a process in which transcription on the sex chromosomes is largely silenced. However, Pol II-mediated transcription is robustly active on the autosomes during this stage. Therefore, the 5-EU signals we detected in pachytene cells predominantly originate from active Pol II transcription on autosomes, while the XY body remains largely devoid of 5-EU incorporation due to MSCI.

      Following the reviewer’s suggestion, we further quantified pre-rRNA transcript levels at different stages of meiotic prophase I using quantitative RT-qPCR. Pre-rRNA transcript levels were extremely low in prophase I spermatocytes compared to Spg, indicating an arrest of rRNA synthesis upon meiotic entry (Revised Figure S2). These findings suggest that reduced engagement of nucleolar components in rRNA biogenesis may facilitate their redistribution and their participation in other biological processes. We have discussed this point in the revised manuscript (Lines 283-289).

      (9) It is very important to show the localization of X-Y body markers such as Brca1, ATR, etc., in spermatocytes treated with BMH-21 to know which process is prevented with this inhibitor.

      As suggested, we examined the localization of ATR and BRCA1 in pachytene spermatocytes following BMH-21 treatment. ATR localization to the XY body was unaffected by BMH-21 treatment. Together with our finding that ATR inhibition disrupts pre-rRNA accumulation at the XY body, these observations support the notion that ATR signaling is required upstream of pre-rRNA recruitment. In contrast, BRCA1 enrichment at the XY body was reduced by BMH-21, suggesting that BRCA1 accumulation at the XY body is potentially regulated by pre-rRNA. We have included these data in Figure S11C and S11D and added the corresponding description in the revised manuscript (Lines 180-181).

      (10) Figure 4A clearly shows the localization of pre-rRNA in the X-Y body depends on active PolI transcription. Where is pre-rRNAs, which resided in the X-Y body after the treatment? Spreading to the nucleoplasm or degradation. Is it very important to analyze the amounts of rRNA species, including pre-rRNAs, under these conditions (and also during normal prophase I)?

      As shown in Figure 4A, the prominent enrichment of pre-rRNA at the XY body was lost upon BMH-21 treatment. Instead, the residual pre-rRNAs were dispersed in the nucleoplasm. We also observed that BMH-21 treatment markedly reduced total pre-rRNA levels in pachytene spermatocytes (Author response image 1). Therefore, these results indicate that BMH-21 disrupts the enrichment of pre-rRNA at the XY body and reduces overall pre-rRNA abundance.

      Author response image 1.

      BMH-21 reduces pre-rRNA levels in pachytene spermatocytes. RT-qPCR analysis of pre-rRNA in pachytene spermatocytes treated with BMH-21 (2.5 μM, 12 hours). Data are presented as mean ± SEM (n=3 biological replicates).

      (11) The authors need to study the localization of nucleolar components including Pre-rRNA, in female meiosis.

      We agree that examining the localization and dynamics of nucleolar components during female meiosis would be of considerable interest. However, the present study focuses specifically on the redistribution of nucleolar components to the XY body during male meiotic prophase I. The XY body is a male-specific chromatin domain formed by the largely unsynapsed X and Y chromosomes and is closely associated with meiotic sex chromosome inactivation and the ATR-dependent DNA damage response. Because female meiotic cells lack an equivalent XY body structure, investigating nucleolar organization during female meiosis would address a distinct biological question that is beyond the scope of the present study.

      Minor points:

      (12) Line 61-62, subtelomeric region: "pseudo-autosomal region" is better.

      We have replaced "subtelomeric region" with "pseudoautosomal region (PAR)" in the revised manuscript.

      (13) Figure 1A: Please add the localization of pre-RNA (and other nucleolar components) in the mouse ES cells, etc., as a control. How the nucleolus in germ cells is similar or different from that in typical somatic cells is important.

      We examined the localization of pre-rRNA in mouse embryonic fibroblasts (MEF) as a representative somatic cell type (Figure S1A). Pre-rRNA showed a similar nucleolar localization pattern in MEFs and spermatogonia (SPG), indicating that the general organization of pre-rRNA within the nucleolus is comparable between these two cell types.

      (14) Line 83, in situ: Should be italicized.

      We have corrected all instances of "in situ" to italicized format (in situ) throughout the manuscript.

      (15) Figure 1A and text: Please explain what Scp3 is and why the authors used this.

      Synaptonemal complex protein 3 (SYCP3) is a major structural component of the lateral elements of the synaptonemal complex, a proteinaceous structure formed between homologous chromosomes during meiotic prophase I. SYCP3 localizes along meiotic chromosome axes and is widely used as a marker to visualize chromosome organization and distinguish different substages of meiotic prophase I based on characteristic patterns of chromosome synapsis (PMID: 42059593). Therefore, we used SYCP3 staining to visualize meiotic chromosome axes and to identify the developmental stage of spermatocytes. We have now added a clear description of SYCP3 and the rationale for its use in the revised manuscript (Lines 54-56).

      (16) Figure 1A and others, dispersion ratio: Please explain what the ratio is in the text and/or the legend.

      The dispersion ratio is defined as the area of pre-rRNA signal divided by the total nuclear area (delineated by DAPI staining). This ratio reflects the degree of spatial dispersion of pre-rRNA within the nucleus: a higher ratio indicates a more diffuse distribution, whereas a lower ratio indicates a more concentrated localization. The dispersion ratio of NPM1 was calculated using the same method as that for pre-rRNA. We have now added a detailed explanation of this definition to the legend of Figure 1A.

      (17) Figure S1A, top panels: A small portion of the signal of POLR1E (yellow) is out of the nucleus (white circle) and overlaps with c-Kit. What does this mean? Need to clarify.

      The appearance of this small portion of POLR1E signal was most likely due to non-specific staining or an imaging artifact, as it was not reproducibly observed in other cells or independent experimental replicates. To avoid potential misinterpretation, we have replaced the original image with a new representative panel from the same experimental condition in the revised Figure S1A.

      (18) Line 93. GC: Should be "NPM1", since this is the result.

      We have corrected “GC” to “NPM1” in the corresponding sentence in the revised manuscript.

      (19) Line 98-, Figure 1C: Please explain how the EU is incorporated into cells and what the "transient" means here in the legend.

      5-EU (5-ethynyl uridine) is a cell-permeable uridine analog that is incorporated into newly synthesized RNA during active transcription (PMID: 40701178; PMID: 37683610; PMID: 29431736). In our experiment, we added 5-EU to the culture medium at a concentration of 1 mM for 2 hours to transiently label newly synthesized RNA. The term "transient" refers to the short pulse-labeling period (2 hours), which allows us to capture a snapshot of active transcription at the time of labeling, rather than steady-state RNA accumulation.

      (20) Line 110, coalesce: Without live imaging, it is very hard to show that NPM1 (or pre-rRNA) bodies coalesce. The authors need to soften the wording here.

      We have replaced "coalesce" with " aggregate" (Line 116).

      (21) Line 114, pre-rRNA and NPM1 are recruited and sequestered in the X-Y body; however, in Figure 2A, B. No evidence of the colocalization of the signals with a marker for X-Y bodies or X, Y chromosomes. How is it possible to quantify the signals without the reference marker, or how is the area of the X-Y body defined (right graphs, line 114-116)? It is essential to show the colocalization analysis in cytology.

      In our study, the XY body territory was identified based on the following criteria: a. SYCP3 staining was used as the primary marker to delineate the axes of the X and Y chromosomes, which remain unsynapsed during pachynema and are embedded within the XY body. b. DAPI staining served as a secondary marker, as the XY body typically appears as a DAPI-dense region (heterochromatin-enriched) within the nucleus. Accordingly, the XY body area in our quantification (Figure 2A and 2B) was defined as the SYCP3-defined XY chromosome axis region plus the surrounding DAPI-dense chromatin territory, following the established criteria in references 20 and 38. We have now added this information to the corresponding Materials and methods section (Lines 496-501) to clarify our morphological analysis criteria.

      (22) Line 115 gradual accumulation: This is true for Pre-rRNA, but not NPM1, which showed a sudden increase mid- to late-pachynema.

      We have revised the wording from "gradual" to "dynamic" in the revised manuscript (Line 121).

      (23) Figure S3, statistical analysis: What kind of statistics did the authors use here? It seems to be a simple quantification of the ratios.

      In Figure S5 (originally presented in Figure S3), we quantified the dispersion ratio of pre-rRNA (or NPM1) across different meiotic stages. As defined in the figure legend, the dispersion ratio was calculated as the pre-rRNA (or NPM1) signal area divided by the total nuclear area (delineated by DAPI staining), which reflects the degree of spatial dispersion of the signal within the nucleus. The numbers indicated above the data points represent the mean value for each group, which facilitates direct comparison of the overall trend across different stages.

      (24) Figure S4, line 126: Lamin is not a marker for the nuclear envelope. If the authors insist on an intact nuclear envelope (NE), please use the other NE markers.

      We agree that Lamin is not a direct marker for the nuclear envelope (NE) per se. While the nuclear lamina is closely associated with the NE and provides structural support to the nucleus, it is not the envelope itself. Notably, Lamin B1 is widely used as a marker to assess nuclear envelope integrity (PMID: 15353547), because disruption of Lamin B1 localization is frequently accompanied by nuclear envelope abnormalities (PMID: 32954426; PMID: 23166514). Therefore, we consider it reasonable to use Lamin B1 staining as an indicator of NE integrity in our experimental context.

      (25) Line 143-144, Figure S5A: How did the authors define the morphology of the X-Y body (what marker was used for the morphological analysis)?

      Upon re-evaluation, we realized that SYCP3 staining, which we had originally used as a reference, lacks sufficient specificity to define the morphology of the XY body. Therefore, in the revised manuscript, we have deleted the morphological description in Page 7.

      (26) Line 145, released: No experimental evidence for the release. Please rephrase here.

      We have replaced "released" with "absent" in the revised manuscript (Line 151).

      (27) Line 165, the treatment of spermatocytes with BMH-21: This is an in vitro experiment using isolated spermatocytes? As shown above, please mention the system precisely.

      As the reviewer noted, the experiments were performed in vitro on isolated spermatocytes. Specifically, spermatocytes were isolated from mouse testes and treated with BMH-21 at 2.5 μM for 12 hours in culture medium, followed by fixation and immunofluorescence and RNA FISH analysis. We have now clarified the experimental system (Lines 172-173) and in the Methods section.

      (28) Figure S7B. Please measure the weight of the testis.

      We have now included the testis weight in the revised Figure S12B (corresponding to the original Figure S7B).

      (29) Line 194, PNA: What is PNA? Please explain it to readers.

      PNA (peanut agglutinin) is used as a marker for the acrosome of post-meiotic germ cells (round and elongated spermatids), and PNA-positive cells therefore represent post-meiotic spermatids. We have added this information in the revised manuscript (Lines 202-203).

      (30) Figure 5A, PolII staining: The images shown in the figure are not convincing (cannot see any signals), which is not consistent with the quantification. Moreover, the graph shows the "relative" amount of PolII. How did the authors define 100% values here? Mean values are not 100% in the two graphs.

      We have now corrected the y-axis to "Pol II-positive area within the XY body", which accurately reflects what was quantified. In the quantification graphs, the "Pol II-positive area within the XY body" refers to the percentage of the XY body territory that is occupied by Pol II signal. Specifically, the XY body region was defined as the region of interest based on SYCP3 staining and DAPI-dense chromatin. We have now added this definition to the Methods section (lines 496-501) to ensure clarity for readers.

      (31) For the ATAC-seq in Figure 6, what happens to the accessibility of chromatin of autosomes (and sex chromosomes) in the BMH-21-treated cells relative to the mock control? In the text, the authors compared the accessibility of sex chromosomes relative to the autosomes only in the treated cells. It is critical to show the difference in the accessibility of autosomes in the treated and untreated cells.

      The overall chromatin accessibility of autosomes remained unchanged upon BMH-21 treatment, whereas the accessibility of sex chromosomes was significantly increased under the same conditions (Figure 6B). Thus, the effect of BMH-21 on chromatin accessibility is preferentially associated with the sex chromosomes. The results have been included in Figure 6B and described in the Results section (Lines 239-245).

    1. Author response:

      Public Reviews:

      Reviewer #1 (Public review):

      Ma et al. use human-chimpanzee tetraploid cells, across different cell types, to identify the genetic causes and then transcriptomic consequences of divergence in DNA methylation. They conclude that the evolution of DNA methylation is driven primarily by cis-regulatory changes, and that the evolution of CpG sites contributes to cis-regulation while transcription factor expression underlies some trans changes. They then argue that divergence in DNA methylation is associated with changes in gene expression and may contribute to human phenotypes.

      The tetraploid model is able to provide compelling evidence that most regulatory evolution occurs due to cis-regulatory changes, and that sites that have diverged in DNA methylation level cluster together into DMRs which share similar divergence patterns and genetic architecture. This stands in intriguing contrast to trans-mechanisms which explain most variation within modern human populations. The authors proceed to show that trans-effects can be explained, in part, by nearby TF binding motifs and many cis-regulatory changes are explained by CpG-disrupting variants. While these mechanisms clearly contribution to divergence in DNA methylation, the degree to which they explain cis- and trans-regulatory divergence would be valuable.

      Next, the authors seek to show that differences in DNA methylation are functionally relevant. Consistent with previous results, they show that differences in DNA methylation are (weakly) associated with changes in gene expression. They hypothesize that genes with concordant regulatory should exhibit great methylation-expression coupling than other genes and show that cis-expression/cis-methylation pairs are more strongly correlated than trans/trans pairs. I think that looking at cis/trans or trans/cis changes would also be useful. Another limitation is that this analysis is limited to promoter regions. It is not clear how many divergent DMRs that includes and how many of those genes have differences in expression. The key question is whether differences in DNA methylation are functionally important, and the answer provided by these analyses is "sometimes".

      Finally, the authors make a case for lineage-specific selection on DNA methylation that is connected to human traits. Using a sign-test, they identify sets of genes which have likely experienced selection in humans and may underlie human phenotypes.

      In conclusion, I think this study provides a valuable resource for differences in DNA methylation between humans and chimpanzees across tissues and provides important insight into the relative abundance of cis and trans regulatory divergence. Additional research is necessary to investigate the underlying regulatory mechanisms and more care needs to be taken in exploring the functional consequences.

      Reviewer #3 (Public review):

      Summary:

      Ma et al. use human-chimpanzee tetraploid cells to examine species differences in DNA methylation. They identify differentially methylated regions under cis or trans regulation. Cis-DMRs are enriched near SNVs that disrupt or create CpGs, providing a plausible mechanism for cis changes in methylation. They also seek to identify transcription factors that might affect methylation in trans, as well as gene sets with evidence for consistent changes in methylation and expression between humans and chimpanzees, suggesting that they may underlie lineage-specific traits.

      Strengths:

      The authors have generated a new dataset across multiple different cell types examining differences in DNA methylation between humans and chimpanzees using human diploid cells, chimpanzee diploid cells, and human-chimpanzee tetraploid cells. Using this dataset, they identify that cis-DMRs are enriched near SNVs that disrupt or create CpGs compared to trans-DMRs and identify transcription factors as candidate trans-acting factors. Both identified SNVs and transcription factors are good candidates for future experimentation. The authors also find that cis-DMRs are more highly correlated with cis-expressed genes than trans-DMRs with trans-expressed genes, providing evidence that methylation and expression are linked genome-wide. Further, they apply a clever sign test approach to identify gene pathways with evidence for lineage-specific selection.

      Comments on revised version.

      They authors have addressed my concerns from their initial manuscript. In particular, the authors have noted the limitations of their study as appropriate, including the use of permissive FDR cut-offs.

      We thank the Reviewing Editor, Senior Editor, and reviewers for their careful reading of our manuscript and their constructive feedback.' We have made two changes in response to the 2nd round of reviews.

      We have replaced the paragraph “To identify the molecular mechanisms driving methylation divergence, we analyzed transcription factors (TFs) associated with trans-DMRs and sequence variants associated with cis-DMRs” with “To explore potential molecular mechanisms driving methylation divergence, we focused on two of many possible contributors: transcription factors (TFs) associated with trans-DMRs and sequence variants associated with cis-DMRs.”

      We now report the absolute numbers of sites underlying each proportion: at FDR < 0.05, 663,368 cis-regulated and 140,017 trans-regulated sites out of 932,573 divergent sites, among 24,935,901 CpG sites tested across cell types. Only CpG sites covered in all parental and hybrid samples of a cell type can be tested, so this is fewer than the 49,049,052 unique CpG positions covered by any library, and we have clarified this distinction in the Results. Per-cell-type counts are provided in Supplemental File 1.

      Second, we performed a variance partitioning analysis analogous to heritability partitioning. We decomposed total interspecies divergence (parental human minus chimpanzee) into a cis component (the allelic difference within hybrids) and a trans component (the remainder), and estimated the proportion of variance in divergence explained by each, together with their covariance. To limit sampling noise, we pooled read counts within 1-kb genomic bins. We used noise-corrected estimators based on covariances between independent replicates. For cell types with a single parental line per species, we report bounds, whose validity we confirmed in CNCC, where two parental replicates allow a direct replicate-based estimate.

      In CNCC, cis effects explained 93% (95% CI 92–95%) of the variance in divergence and trans effects 71% (70–73%), with a strongly negative covariance term (−0.64). This indicates that cis and trans changes often act in opposite directions. In the other cell types, cis effects explained 58–98% and trans effects 3–48% of the variance, depending on cell type and bound, with small covariance terms. Cis exceeded trans in every cell type under both bounds, and the results were robust to a stricter coverage threshold and consistent at single-CpG resolution.

      These analyses confirm that cis-regulation is the dominant contributor to human–chimpanzee methylation divergence. They also show that trans effects contribute more to divergence variance than the proportions of classified sites alone would suggest. We have added these results to the Results, described the method in a new Methods subsection, "Variance partitioning of methylation divergence”, and provided full results in Supplemental File 1.

    1. Author response:

      The following is the authors’ response to the previous reviews.

      Changes made independently of the reviewers' comments

      In addition to the revisions described below, we have made the following three changes, none of which affects the conclusions of the paper.

      (1) Shared control data (Figure 4c, d, l, m). The parental cells and the PIEZO1 KO and pan-KRT6 KO cell lines were assayed in parallel in the same experiments. We have therefore stated in the figure legend that the parental-cell data are shared between panels c, d and panels l, m.

      (2) Number of DEGs (Figure 4h). We have corrected the number of genes upregulated in cells cultured on the 3.0-µm-pored membrane from 69 to 68.

      (3) Yoda1 data (Figure 4e, f). Some values had been incorrectly transferred during data compilation. We have corrected these values and the corresponding graphs. The statistical results are unchanged.

      We have also provided two new files: Source data 1 (numerical data underlying all graphs) and Source data 2 (uncropped western blot images).

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      The study describes the migration of epidermal keratinocytes through porous membranes and observed a unique size selection whereby only on 3-micron membrane are keratinocytes able to migrate and reform an intact epidermis. The authors propose that the model replicates three cell states of intact epidermis, EMT, and MET. They also show that this response depends on the actin cytoskeleton, keratin 6, and Piezo1, and the migration could be stimulated with TGFbeta ligands.

      Strengths:

      Strengths of the study include the establishment of a simple yet robust in vitro model that capture all three cell states, which could be useful for future investigation of wound healing or metastasis across a range of epithelia. There is also good quantitative characterisation of the pore size effects, providing some interesting observations about the physical regulation of keratinocyte migration, and the study provides some initial insights into the regulatory mechanisms. The images and presentation are clear.

      Weaknesses:

      While there are some insights into the underlying mechanisms, there could be more detailed analysis of the key signalling pathways and functional relationships between actin, keratins, Piezo, and EMT genes. Although the extent of new biological insight is somewhat limited, the study still demonstrates the utility of the model, and these points may be important questions to address in future studies.

      We agree with the reviewer that these are important questions. We will address the functional relationships among actin, keratins, PIEZO1, and EMT genes, and the underlying signaling pathways, in future studies.

      Reviewer #2 (Public review):

      Summary:

      The revised manuscript by Nohara et al. presents a novel 3D assay that allows for stratification of epithelia, active EMT through small pores, and active MET. They show that 3um pores allow for keratinocytes to sample the pore through filopodia and up regulate EMT genes to transverse the pores to the other side of the membrane where EMT genes are down regulated as the cells re-establish stratified epithelia. The TGFbeta pathway and actin polymerization promotes movement of cells into the pores and Piezo1 and KRT6 actively block this movement. This work provides a novel 3D assay that is likely to become a benchmark to analyze these processes using a more complex system than other current culture-specific EMT and MET assays.

      Strengths:

      The strengths of the manuscript include the foundational analysis of the pathways involved in establishing the 3-compartment epithelium. The authors have incorporated live imaging, drug studies, KO analysis, and RNA-sequencing to show the relevant pathways involved. The authors were responsive to the original round of reviews and present a much-improved study with greater details on molecular markers, quantification, and clarity.

      We thank the reviewer for the positive evaluation of our revised manuscript.

      Reviewer #3 (Public review):

      Summary:

      The authors established an experimental system that reproduced three-dimensional triphasic epithelia, i.e., the original epithelium, its EMT, and MET. Keratinocytes (KCs), skin epithelial cells, placed on a microporous membrane migrated through 3.0-um or larger micropores. The 3.0-um-pored membrane induced an epithelial structure with three states: stratified KCs above the membrane, KCs showing EMT within the micropores, and a new stratified epithelium under the membrane. The membrane with larger micropores failed to maintain this triphasic epithelia. Live imaging revealed that KCs moved in a reciprocating manner, with actin-rich filopodia-like KC structures extending into and out of the 3.0-um micropores, while the cells migrated unidirectionally into larger micropores. KO of Piezo1 and keratin 6 increased KC entry to and exit from the 3.0-um micropores. Their results demonstrate that benign keratinocytes migrate through confined spaces in a reciprocating manner, which might help form triphasic epithelia, recapitulating wound healing processes.

      Strengths:

      Careful observation of the behaviour of keratinocytes on the different sized pores. CrispR-Cas9 gene editing to KO Piezo 1 and keratin 6 isoforms in HaCaT keratinocytes.

      Weaknesses:

      The authors have improved the observed weaknesses including better statistical analysis and more detail on replicates. They have also performed staining for laminin beta3 chain.

      We thank the reviewer for these comments.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      The authors have significantly improved the manuscript in the recent revision. One minor point is to please make the RNA-seq analysis, including gene lists available in the supplementary information.

      As suggested, we have added Figure 4—source data 1, which lists the differentially expressed genes (DEGs) identified by bulk RNA-seq of HaCaT keratinocytes cultured on 0.4-µm- or 3.0-µm-pored membranes.

      Reviewer #3 (Recommendations for the authors):

      I am not suggesting any further changes to the manuscript.

      We thank the reviewer for evaluating our revised manuscript.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Reviewer #1 (Public review):

      Summary:

      In this manuscript, the authors describe the use of BindCraft computational protein design to create a series of binders to the chemokine CCL25. This chemokine normally mediates CCR9-dependent trafficking of immune cells to the gut, making it a potential target for the treatment of inflammatory bowel disease and related conditions. Importantly, CCL25 also binds a scavenging receptor, ACKR4. The computational protein design approach used does not involve defining particular epitopes to be targeted, allowing a free search for any potential interaction surface.

      Among four designs tested, three were predicted to interact at a similar site on the chemokine, while a fourth clone, VUP25111, was predicted to bind to a different site. All four designs showed binding to CCL25, with similar high-nM KD values in all cases. The first three clones showed evidence of direct competition with the receptor for CCL25 binding, while VUP25111 showed incomplete inhibition of binding. In functional assays, all clones acted as antagonists except for VUP25111, which inhibited arrestin recruitment by CCR9, but did not affect G protein activation by CCR9 or arrestin recruitment by ACKR4 (which signals exclusively through arrestin and not G protein).

      Strengths:

      The work is completed to a high technical standard, and the functional diversity of the clones is intriguing. It is exciting to see pathway-selective modulation of signaling, and this basic paradigm is likely to generalize to other chemokine/receptor systems. The exceptional complexity of chemokine signaling makes this an excellent area to explore the development of modulators that can restrict signaling to a specific subset of receptors.

      Weaknesses:

      No major weaknesses were noted by this reviewer.

      We thank the reviewer for their positive response and thorough evaluation of our work. Below, we address their recommendations in detail in the private review.

      Reviewer #1 (Recommendations for the authors):

      Minor points for potential improvement:

      (1) Consider shortening the discussion section, which could benefit from a more focused discussion of the key conclusions and their implications. As written, it is rather long, and parts of it repeat material already covered elsewhere (e.g., the two-step binding mechanism is described in lines 55-64 and again in 331-335).

      We thank the reviewer for the suggestion to make the discussion more focused. We agree that parts repeat material from the introduction. As such, we have revised the discussion to reduce repetition with the introduction, including removal of the repeated description of the two-step binding mechanism, and condensing several passages.

      (2) The figures are clear, but it may be helpful to combine panels into a smaller number of figures to make direct comparisons among signaling curves more straightforward.

      We thank the reviewer for the suggestion to reduce the number of figures for easier curve comparisons. We prefer our current presentation of the figures so as not to conflate disparate themes and concepts; for example, GRK recruitment is a distinct event from receptor internalization. The pharmacological results have been compiled in Figure S8 in the supplementary to allow visual, side-by-side comparisons of the DRCs presented in the publication.

      Reviewer #2 (Public review):

      This study from de Boer, Lamme, Verdwaald and Schafer describes the de novo AI-guided design of miniproteins that target the chemokine CCL25, with the aim to modulate the activation and signalling of the chemokine receptors CCR9 and ACKR4. The study focuses on characterising four miniproteins that all bind CCL25 with good affinity. Three designs appear to prevent CCL25 binding to both CCR9 and ACKR4, with increasing concentrations of miniproteins resulting in decreased arrestin (both receptors) and mini G protein recruitment (CCR9), less inhibition of forskolin-stimulated cAMP (CCR9), and decreased GRK3 recruitment and receptor internalisation (CCR9). One miniprotein, VUP25111, changes the properties of CCL25 rather than preventing ligand/receptor interactions, resulting in greater selectivity for CCR9 over ACKR4 and a G protein-biased signalling profile (maintenance of mini G protein recruitment, GRK3 recruitment, inhibition of cAMP and receptor internalisation, but loss of arrestin recruitment). VUP25111 also maintained chemotactic migration in MOLT-4 T lymphoblast cells, whereas this response was lost in the presence of the other three miniproteins.

      Overall, this is a very interesting application of AI-designed de novo miniproteins to modulate GPCR responses by directly binding the ligand rather than the receptor. This is a conceptually very intriguing approach that could, in principle, be extended to other GPCR systems beyond the chemokine family. The authors deploy an impressive array of assays spanning multiple signalling endpoints, providing a thorough picture of how each miniprotein influences receptor activation and downstream signalling. The presentation of concentration-response relationships for CCL25 alone and in the presence of each miniprotein is particularly informative, and the figures are very well constructed throughout. The inclusion of clear cartoons illustrating the basis of each assay is a nice touch that will help readers from outside the immediate field follow the logic of each experiment.

      There are two main conclusions that are not currently as well-supported by the evidence as they might be, and that would benefit from some qualification. The first concerns the selectivity of the miniproteins for CCL25. Testing the impact of the miniproteins on CXCL12 activation of CXCR4 is an important and welcome experiment, but it addresses selectivity against only one other chemokine system, and the current claim of specificity is therefore stronger than the data allow. Additionally, at the highest concentration tested (10 µM), the more potent miniproteins (VUP25101, VUP25107) appear to show some inhibition of arrestin recruitment to CXCR4 - perhaps unsurprising given the degree of structural conservation among chemokines. The statements regarding selectivity and the lack of effect on the CXCL12/CXCR4 system would benefit from revision to more accurately reflect these observations.

      We thank the reviewer for the detailed review and suggestions for our publication. We agree with the reviewer that testing against only one additional chemokine receptor: chemokine pair is insufficient to support strong claims of selectivity. To further assess the selectivity of the miniproteins, we evaluated the effects of the VUPs against CCL20, a chemokine closely related to CCL25. CCL20 binds both CCR6 and ACKR4, providing an optimal platform to compare the effects on this non-specified target. Receptor activation was determined by β-arrestin recruitment (Fig. S6). For ACKR4, VUP25107 and VUP25112 have similar IC50 values for CCL20 and CCL25. In contrast, VUP25101 showed reduced potency towards CCL20 relative to CCL25 (CCL20 pIC50 = 6.06 ± 0.13, CCL25 pIC50 = 7.73 ± 0.08), suggesting greater selectivity. VUP25111 had no impact on activation of ACKR4 by CCL20, which may reflect a lack of engagement with the other chemokine or that it binds in a similar way as to CCL25 and does not impact chemokine-promoted ACKR4 activation. CCL20-mediated activation of CCR6 further supports the specificity of VUP25101, which showed only a modest effect at the highest concentration tested. In contrast, VUP25107 and VUP25112 showed a dose-dependent inhibition of arrestin recruitment (pIC50<sub>VUP25107</sub> = 6.99 ± 0.15, pIC50<sub>VUP25112</sub> = 7.49 ± 0.07).

      We agree that a reduction in β-arrestin recruitment to CXCR4 is apparent at the highest concentration tested (10 µM) for VUP25101 and VUP25107. To further address the selectivity of these miniproteins, we have included β-arrestin recruitment data for ACKR3 (Fig. S5), the other chemokine receptor that binds CXCL12. A similar suppression was observed for the atypical receptor as for CXCR4 at the highest concentrations, suggesting cross-reactivity at high concentrations.

      Based on the CCL20 and CXCL12 data, we have revised the text to more accurately reflect these observations. We now frame these results as an initial proof of concept demonstrating the feasibility of this design approach, while noting that further optimization and characterization of selectivity will be required to advance the miniproteins for additional applications.

      To reflect this, we have added the following text on Pg.9:

      “CCL25 specificity was experimentally evaluated by testing the miniproteins against CXCL12 by tracking arrestin recruitment to CXCR4 and ACKR3, the native agonist for this canonical and atypical receptor pair (Fig. S5). VUP25111 and VUP25112 showed no effect on CXCL12-mediated activation at any concentration, while VUP25101 and VUP25107 showed partial inhibition at the highest tested concentration (10 µM).

      In addition, the effects of the VUPs were evaluated against CCL20, a closely related chemokine to CCL25, by assessing arrestin recruitment to CCR6 and ACKR4 (Fig. S6). VUP25107 and VUP25112 displayed similar inhibitory potencies of CCL20 as to CCL25 for ACKR4 (VUP25107: pIC50 = 7.72 ± 0.21; VUP25112: pIC50 = 6.93 ± 1.03). In contrast, VUP25101 showed reduced inhibition of CCL20 relative to CCL25 (VUP25101: pIC50<sub>CCL20</sub> = 6.06 ± 0.13 v pIC50<sub>CCL25</sub> = 7.73 ± 0.08), indicating greater selectivity for the designed target. CCL20 activation of CCR6 further supports the specificity of VUP25101, which only showed a modest effect at the highest concentration tested. VUP25111 showed no inhibitory effects on CCL20 activation of either CCR6 nor ACKR4, which may indicate a lack of binding, but is also indiscernible from forming a receptor-competent complex similar to the proposed CCL25:VUP25111:ACKR4 interaction.”

      And added the following in the discussion on Pg.15:

      “The miniproteins displayed varying degrees of chemokine selectivity among CCL25, CCL20, and CXCL12, including cross-reactivity for some designs. Given that only two additional chemokines were examined, these experiments provide an initial assessment of selectivity. As chemokine selectivity was not explicitly optimized during design, broader experimental profiling and negative-design strategies may be required to establish and improve miniprotein selectivity.”

      The second concern relates to the interpretation of the preserved GRK3 recruitment, but the complete loss of arrestin recruitment observed with VUP25111. In the GRK3 recruitment experiments, 20 nM CCL25 was used, representing an EC40 concentration in this assay. VUP25111 causes a concentration-dependent reduction in CCL25-induced GRK3 recruitment, down to approximately 15% of the maximal response. It is worth considering whether this degree of reduction in GRK3 recruitment could itself be sufficient to disrupt patterns of receptor phosphorylation and thereby prevent observable arrestin recruitment. Both interpretations are complicated by the fact that the GRK3 recruitment and arrestin recruitment assays likely differ in their sensitivity and dynamic windows, making direct quantitative comparisons between them difficult. In the absence of direct measurements of CCR9 phosphorylation in the presence of VUP25111, the alternative interpretation remains open and would benefit from acknowledgement. Given recent work from the same group demonstrating that receptor internalisation is only partially dependent on arrestins (Lamme et al., 2025, J Biol Chem), further discussion of the relationship between GRK and arrestin recruitment and CCR9 internalisation would be of value to the broader GPCR audience this work is likely to attract.

      We appreciate the reviewer’s careful analysis of our results and highlighting earlier work from our group. The reviewer is correct that the discrepancy between VUP25111’s impact on GRK3 and arrestin recruitment can also be explained by the decrease in GRK3 recruitment reflecting a sufficient change in receptor phosphorylation to account for the loss of arrestin engagement and not solely by the presented interpretation of the adoption of an arrestin-incompatible conformation with retained phosphorylation. The main text has been modified on pg. 11 to reflect this potential:

      “This suggests that either activation of CCR9 by the VUP25111:CCL25 complex promotes a conformation incompatible with arrestin engagement, but still accessible for GRK phosphorylation, or the reduced GRK interaction represents the formation of a phosphorylation barcode incapable of supporting arrestin recruitment. Without direct phosphorylation measurements these possibilities cannot be separated.”

      And in the discussion on pg.14:

      “The extent of phosphorylation is not clear, and the inhibited GRK recruitment may reflect the formation of sub-phosphorylated states which cannot support arrestin recruitment nor promote efficient receptor internalization. Alternatively, the miniprotein: chemokine complex may induce a conformational state incompatible with arrestin engagement.”

      A partial phosphorylation explanation has also been added on internalization on pg.12:

      “These results suggest that the VUP25111:CCL25 complex suppresses both the arrestin-dependent and independent internalization mechanisms used by CCR9, despite likely allowing for some, albeit perhaps insufficient, GRK phosphorylation.”

      Finally, some additional justification for the use of 20 nM CCL25 across all assays would strengthen the study, as this concentration represents different points on the concentration-response curve depending on the assay and receptor in question. It ranges from an EC40 for CCR9 GRK3 recruitment and internalisation, to an EC50 for CCR9 arrestin and mini-Gi recruitment, an EC80 for CCR9 cAMP inhibition, and an Emax for ACKR4 arrestin recruitment. This has potential consequences for the interpretation and cross-assay comparison of miniprotein potency, and the authors are encouraged to acknowledge and discuss this in the context of their conclusions.

      We thank the reviewer for highlighting the need to discuss CCL25 concentration across assays. Our primary aim was to use a single CCL25 concentration to enable direct comparison of all assay outcomes against the same CCL25:miniproteins ratio, since the miniproteins are designed to antagonize the chemokine, rather than the receptor. We set the concentration at 20 nM based on the first arrestin recruitment assays to CCR9, where we initially characterized miniprotein: CCL25 activity. Importantly, CCL25 has lower potency for CCR9 than ACKR4, making it the limiting case. Selecting 20 nM ensured responses within the EC40-EC80 range for all assays. To improve clarity, we have now explicitly stated this rationale in the manuscript and noted the implications of using a single CCL25 concentration across diverse readouts on Pg.10:

      “Despite the higher potency of CCL25 for cAMP inhibition compared to arrestin recruitment, a fixed concentration of 20 nM CCL25 was used throughout this and subsequent assays to maintain a consistent CCL25:miniprotein stoichiometry. As this concentration represents different points on the respective concentration-response curves, cross-assay comparisons of apparent miniprotein potency should be interpreted qualitatively.”

      Reviewer #2 (Recommendations for the authors):

      Major points:

      (1) The conclusions regarding miniprotein selectivity for CCL25 would benefit from revision to reflect that only the CXCL12/CXCR4 system was tested as a counter-screen. The apparent inhibition of arrestin recruitment to CXCR4 by VUP25101 and VUP25107 at 10 µM should be acknowledged/discussed.

      We thank the reviewer for this comment and agree that selectivity should be more explicitly acknowledged. This point has been thoroughly addressed in our response in the public review. Briefly, we have added a similar selectivity assay but now against CCL20, which is closely related to CCL25, as well as revisiting the CXCL12 assay with ACKR3 that was originally presented in the manuscript. Statements in the text have been added to note the apparent inhibition at 10 µM for VUP25101 and VUP25107.

      (2) The conclusions regarding G protein-biased signalling driven by VUP25111 would benefit from qualification. In particular, it is worth acknowledging that a substantial reduction in GRK3 recruitment may itself be sufficient to account for the observed loss of arrestin recruitment, and that direct measurement of CCR9 phosphorylation in the presence of VUP25111 would help to resolve this. Discussion of the relationship between GRK recruitment, receptor phosphorylation, arrestin recruitment and internalisation in this context would also be of value to the broader GPCR audience this work is likely to attract.

      We agree with the reviewer that an incomplete or insufficient level of phosphorylation could also explain our arrestin and internalization results presented by the VUP25111:CCL25 complex. We have added the following to the discussion on pg. 14 and modified the results to better reflect the multiple interpretations:

      “The extent of phosphorylation is not clear and the inhibited GRK recruitment may reflect the formation of sub-phosphorylated states which cannot support arrestin recruitment, nor promote efficient receptor internalization. Alternatively, the complete inhibition of arrestin engagement cannot be easily explained by phosphorylation, and instead suggests the miniprotein: chemokine complex may induce a conformational state incompatible with arrestin engagement. Due to the clash with ECL2, the loop would need to distort to accommodate the larger ligand complex and this displacement may translate into the G protein and GRK-permissive structural state.”

      (3) The choice of 20 nM CCL25 across assays should be justified or its implications discussed, particularly given that this concentration represents different effective concentrations for each endpoint and receptor.

      The rationale for using a fixed 20nM CCL25 concentration and its implications is now discussed within the main text as well as our response in the public review.

      Modelling:

      Modelling of VUP25111 and VUP25101 binding to CCL25/receptor complexes is presented. Was the same analysis performed for VUP25112 and VUP25107, and do they similarly appear to interfere with direct receptor binding?

      We initially selected VUP25101 as a representative for VUP25112 and VUP25107 to simplify visualization. We have now extended the same modeling analysis to VUP25107 and VUP25112. These additional analyses have now been included in the revised manuscript in Fig. 3D.

      Methods:

      (1) Percentage concentrations throughout the methods are missing w/v or v/v designations.

      We thank the reviewer for their careful reading and apologize for the oversight. We have added all w/v or v/v designations in the methods.

      (2) More specific information for each BRET experiment would be useful. For example, incubation times with CCL25 and miniproteins (included for some but not all assays), and clarification of whether experiments were endpoint reads or timecourse experiments.

      We agree with the reviewer that the methods section could be clarified, as well as removing a lot of repetition. We have revised the methods.

      Specific text revisions:

      (1) Abstract, line 20: "Most drug discovery efforts target the receptors, whereas natural regulatory mechanisms focus on the chemokines". This is unclear for a non-chemokine audience without additional context clarifying that this refers to binding to or modification of the chemokine itself to modulate receptor activation.

      To clarify this distinction for a broader readership, we revised the abstract to state explicitly that natural regulatory mechanisms modulate immune responses by directly binding to or modifying chemokines, thereby altering their ability to bind receptors. We have changed the text in the abstract on Pg.2 to:

      “Most drug discovery efforts target the receptors, whereas natural regulatory mechanisms modulate immune responses by directly binding to or modifying the chemokine ligands.”

      (2) Results, line 177: "In the case of VUP25111, only the highest tested concentrations decreased CCL25 binding to either receptor, but did not completely eliminate the binding signal". This should be revised as there is a clear concentration-dependent effect of VUP25111 on CCL25 binding.

      We have revised the text to reflect that VUP25111 inhibits CCL25 binding in a concentration-dependent manner, while also making clear that this inhibition occurs with significantly lower potency than the other miniproteins. We have changed the following text on Pg.7:

      “VUP25111 shows a drastically lower inhibitory potency compared to the other binders and did not completely eliminate the binding signal.”

      (3) Line 179: "...this suggests that CCL25:VUP25111 may bind the receptors cooperatively". Please revise; the meaning is unclear.

      Our results indicate that VUP25111 does not prevent CCL25 from engaging either receptor. To avoid ambiguity, we have revised the text to explicitly state that our results are consistent with the binding of a pre-formed VUP25111:CCL25 complex to the receptor, resulting in the formation of a VUP25111:CCL25:receptor complex. We have changed the following text on Pg.7:

      “Since the binder readily complexes with the chemokine at these concentrations (Fig. 2), this suggests that the CCL25:VUP25111 complex retains the ability to bind the receptor.”

      (4) Line 216: "VUP25112 also completely impaired CCL25-mediated activation of the atypical receptor at the highest concentrations, but with significantly less potency". Please provide statistical tests to support this statement.

      We thank the reviewer for requesting clarification regarding the statistical support for this statement. Statistical analyses supporting the conclusions in line 216, as well as other figures, were included in the initial manuscript but were provided in the supplementary information. To improve clarity in the manuscript, we have added explicit references to the corresponding supplementary statistical table in the text, added appropriate significance indicators to the relevant figures, and expanded the figure legends to state the statistical test used.

      (5) Line 219: "The unique binder VUP25111, on the other hand, did not inhibit the activation of ACKR4 by CCL25 at any tested concentration". Please rephrase. While there was no concentration-dependent inhibition of arrestin recruitment to ACKR4, the addition of VUP25111 at any concentration appeared to reduce total arrestin recruitment to approximately 80% of the CCL25-alone condition.

      We would like to thank the reviewer for this careful analysis of the data. Although this may appear to be the case in the figure, there is no significant difference between the lowest concentration (2.5 nM) and vehicle condition (∞) for any miniprotein and no real difference can be claimed.

      We have specifically noted this on Pg. 9:

      “The unique binder VUP25111, on the other hand, did not significantly impact the activation of ACKR4 by CCL25 at any tested miniprotein concentration.”

      (6) Line 240: "suggest that the specific ligand interactions driving arrestin engagement with CCR9 may be more strict than for the G proteins". An alternative interpretation is that the miniprotein specifically impairs the receptor conformation important for arrestin engagement, without affecting the conformation required for G protein engagement, and this should be acknowledged.

      We agree with the reviewer that these statements would benefit from further clarification. Indeed, the observed effects may not be only due to specific ligand interactions but could also depend on specific receptor conformations required for the specific protein-protein interactions. We have adjusted the following text on Pg.10:

      “The deviations between the arrestin results (Fig. 4) and G protein (Fig. 5B) suggest that the specific ligand interactions or receptor conformations driving arrestin engagement with CCR9 may be more strict than for the G proteins.”

      Reviewer #3 (Public review):

      Summary:

      The authors employed the BindCraft platform to develop binders targeting the chemokine CCL25, a selective activator of the chemokine receptor CCR9. They successfully generated two classes of binders: one that inhibits all CCL25-mediated CCR9 activation, and another that permits CCR9 G protein signaling while simultaneously preventing arrestin recruitment. These tools will enable the dissection of arrestin involvement in regulating cell migration.

      My comments, in the order of reading:

      (1) Title: I strongly recommend removing the term "biasing" from the title. In this context, it does not convey a specific mechanistic concept. The term "biased signaling" has been used for a very broad range of mechanistically distinct pharmacological phenomena, and without a precise definition, it adds more confusion than clarity. I therefore suggest refraining from using it in the title.

      We appreciate the reviewer’s concern regarding the use of the term “biasing” given its broad and sometimes ambiguous use in the literature. Most commonly it refers to G protein versus arrestin-mediated signalling but is also used in regard to GRK specificity as well as to discrete differences in receptor trafficking (Motso et al. 2025, Cell). In our study, we use this in a specific mechanistic sense, referring to the bias VUP25111 induces upon binding CCL25. The miniprotein: CCL25 complex inhibits CCR9 arrestin recruitment, receptor internalization, and GRK3 engagement while not affecting G protein recruitment (mGi), G protein-mediated signaling (CAMYEL), and cell migration. We compare these directly to the effects of the chemokine alone, which shows robust responses across all of these receptor outputs. The use of the term “biasing” in the title is reflective of this observed change in receptor response to the modified agonist. Additionally, as noted by the reviewer below, we compare similar outputs to compare the impact on effector coupling, eg. Arrestin and mini-G protein recruitment. We strongly feel that the term “biasing” most accurately describes the phenomenon we are describing with regard to the altered receptor response to the VUP25111:CCL25 complex and thus prefer to keep the title without alteration.

      (2) Abstract, line 34: The term "bias" should be replaced. As currently used, it appears to suggest a dichotomy between G protein signaling and arrestin recruitment. However, arrestin recruitment is a consequence of G protein signaling, and it is not conceptually sound to compare a signaling event mediated by one protein family with a protein-protein interaction involving another protein family. A meaningful comparison requires experimental paradigms that differ by a single variable; in this case, there are two - distinct protein families and fundamentally different types of readouts (signaling versus protein-protein interaction).

      We agree that the term “bias” must be used with precision. One point of clarification, arrestin recruitment is not explicitly a consequence of G protein signaling. The atypical chemokine receptors, of which ACKR4 is a member, are well-established examples of GPCRs that do not bind nor activate G proteins yet still recruit arrestins (Lamme et al., 2026). While biased responses within the GPCR system are often the comparison of different events as noted by the reviewer, we compare the effects of miniproteins on the recruitment of mGi and arrestin via a BRET-based assay that assesses the direct protein: protein interactions between the receptor and effector. The lack of effect on mGi recruitment was further supported by measuring the effect of the miniproteins on downstream cAMP levels. To avoid any misunderstanding, we have revised the abstract to explicitly state that the observed effect induced by VUP25111 is evaluated through direct recruitment of effectors, rather than implying a comparison between disparate signaling outputs.

      (3) Abstract, line 34: The term "balanced agonist" should be removed. Any chosen reference ligand is, by definition, the "balanced" agonist for that analysis, regardless of its actual signaling profile. Consequently, the expression "balanced agonist" adds no mechanistic information beyond "the agonist used as reference in a particular bias calculation" and is potentially misleading, as it implies that this ligand possesses a uniquely unbiased, system‑independent signaling profile, which is not the case.

      We agree with the reviewer that the term “bias” is always relative to a specific reference ligand. Indeed, it is known that some natural chemokine:receptor pairs show some bias on its own. Therefore, we adjusted the text in the abstract on Pg.2 and removed the word “balanced”.

      (4) Abstract, line 36: I also recommend removing the term "bias" at this point. The concept of bias typically arises from experiments that quantitatively compare more than one variable. As currently written, the phrasing suggests a dichotomy between G protein- and arrestin-mediated signaling, yet the study does not assess arrestin signaling, only arrestin recruitment. Under these conditions, the use of "bias" is not appropriate. The data are clear and compelling on their own without the need for this potentially misleading terminology.

      We thank the reviewer for this comment. We would like to emphasize that our conclusions are based on the fact that we measure both G protein (mGi recruitment) and arrestin (arrestin recruitment) as protein:protein interactions. We have changed the text in the abstract on pg.2 to further distinguish between signaling and recruitment:

      “Additionally, G protein recruitment to CCR9 was unimpeded by VUP25111, suggesting that the miniprotein biased the native agonist towards G proteins.”

      (5) Introduction: This is interesting to read and generally well written, though certain statements would benefit from improved semantic precision. For example, in lines 110-111, the phrase "G protein-biased complex" should be reconsidered, as it relies on the notion of G protein- versus arrestin-mediated signaling. Arrestins themselves do not signal; what is measured here is their recruitment. Comparing G protein signaling with arrestin recruitment is therefore conceptually unsound, since arrestin engagement is a downstream consequence of G protein activation. Comparisons become meaningful only when designed to differentiate between G protein-dependent and G protein-independent arrestin recruitment, which is not the case in this study.

      Since the VUP25111:CCL25 complex suppresses arrestin recruitment to CCR9, but not G protein recruitment, we are confident representing the modified agonist as G protein-biased. Additionally, arrestin recruitment is only downstream of G protein activation in the occasion where the GPCR is phosphorylated specifically by GRK2/3 and not GRK5/6. CCR9 does not show any preference for GRKs and recruits arrestin as effectively when phosphorylated by either GRK2/3 or GRK5/6 (Lamme JBC 2025). Since G protein coupling is preserved when challenged with the VUP25111:CCL25 complex, both families of GRKs should be available for phosphorylation. We have modified the statement to better specify recruitment compared to signaling on Pg. 5:

      “Most prevent activation by impeding chemokine binding to the receptor, thus impairing all signaling and migratory responses, but one forms a G protein-biased complex with CCL25, preserving G protein recruitment while suppressing arrestin recruitment to CCR9, and selectively inhibits CCR9, but not ACKR4.

      (6) Results, 122,123: The authors should consider being more precise; possibly, the truncated CCL25 is somewhat less potent on CCR9. The authors should make a statistical test and then decide whether to rephrase or not for enhanced precision.

      The reviewer is correct that we detect a small difference in potency between full-length CCL25 and CCL25-ΔCT at CCR9. This was quantified and is reported in the supplementary Table S2, where CCL25 shows a logEC50 of -7.46 ± 0.16 compared with -7.89 ± 0.29 for CCL25-ΔCT, indicating that the truncated chemokine is slightly more potent. While the difference was determined to be statistically significant per an Extra sum-of-squares F test, we don’t consider the of the truncation to be substantially impactful, which is also in line with previous publication (Pinheiro Nat. Comm. 2025). We have therefore revised the text to note the modest increase in potency of CCL25-ΔCT compared to the native, full-length CCL25 and added statistical information in the figure legend. We have changed the text on Pg. 5 to:

      “The truncated CCL25 (CCL25_ΔCT, 1-77) activated both CCR9 and ACKR4 with similar efficacy while showing slightly enhanced potency only towards CCR9 compared to the full-length ligand (Fig. S1).”

      (7) Figure S5: This figure is currently confusing and needs clarification. The authors state in the main text that CXCR4 is stimulated with CXCL12, yet the figure legend refers to CCL25; this discrepancy should be corrected to ensure consistency. In addition, inhibition of CXCR4 by the miniprotein binders should be analyzed and presented with normalization to CXCR4 responses, not to CCL25-stimulated CCR9. To avoid misinterpretation, inhibition by the miniproteins should be quantified separately for CCR9 and CXCR4, each normalized to its own receptor-specific and functionally equivalent stimulation condition, rather than to the "other" receptor.

      We thank the reviewer for this comment and apologize for the oversight during editing. The mentions of CCL25 in Figure S5 were incorrect, and CXCL12 was indeed used in this cross-reactivity assay to stimulate CXCR4 and for subsequent normalization. We have adjusted the legend accordingly.

      (8) Results, lines 211-213: The authors should be more semantically precise. They state that no binder has any effect on arrestin recruitment to CXCR4. If I see the data, this is not really true, as 25101 and 25107 inhibit arrestin recruitment by about 50 % or more at the highest applied concentrations; only 111 and 112 are completely inactive. As already commented, normalization should be done to arrestin recruitment of CXCR4 and not CCR9.

      We thank the reviewer for this comment and agree that, at the highest tested concentrations of VUP25101 and VUP25107, substantial inhibition is observed. Additionally, we have extended our analysis of the miniprotein selectivity to include activation assays for the CCL20 receptors CCR6 and ACKR4, as well as the atypical CXCL12 receptor ACKR3. Based on these data, we have revised the text to more accurately reflect these observations. We now frame these results as an initial proof of concept demonstrating the feasibility of this design approach, while noting that further optimization and characterization of selectivity will be required to advance the miniproteins for additional applications.

      We have adjusted the text on Pg.11:

      “CCL25 specificity was experimentally evaluated by testing the miniproteins against CXCL12 by tracking arrestin recruitment to CXCR4 and ACKR3, the native agonist for this canonical and atypical receptor pair (Fig. S5). VUP25111 and VUP25112 showed no effect on CXCL12-mediated activation at any concentration, while VUP25101 and VUP25107 showed partial inhibition at the highest tested concentration (10 µM).

      In addition, the effects of the VUPs were evaluated against CCL20, a closely related chemokine to CCL25, by assessing arrestin recruitment to CCR6 and ACKR4 (Fig. S6). VUP25107 and VUP25112 displayed similar potencies towards CCL20 comparable to those observed for CCL25 (VUP25107: pIC50 = 7.72 ± 0.21; VUP25112: pIC50 = 6.93 ± 1.03) to ACKR4. In contrast, VUP25101 showed reduced inhibition of CCL20 relative to CCL25 (VUP25101: pIC50<sub>CCL20</sub> = 6.06 ± 0.13 v pIC50<sub>CCL25</sub> = 7.73 ± 0.08), indicating greater selectivity. CCL20 activation of CCR6 further supports the specificity of VUP25101, which only showed a modest effect at the highest concentration tested. VUP25111 showed no inhibitory effects on CCL20 activation of either CCR6 nor ACKR4, which may indicate a lack of binding, but is indiscernible from forming a receptor-competent complex similar to how it interacts with CCL25 and ACKR4.”

      Concerning the comment regarding the normalization to CCR9 rather than CXCR4, due to a mistake, the figure legend incorrectly stated CCL25, whereas the assay was performed using CXCL12. We thank the reviewer for bringing this up and have corrected the figure accordingly.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Reviewer #1 (Public review):

      Strengths:

      The adoptive transfer of congenically marked wildtype and Itk-/- Treg populations clearly demonstrates that ITK-deficient Treg can actively rescue pre-existing lung injury and reverse systemic secondary metrics like proteinuria in wild-type recipients, providing proof-of-concept validation for the therapeutic utility of the ITK-Treg axis.

      We sincerely thank Reviewer #1 for recognizing the strength and translational significance of our adoptive-transfer experiments. We agree that these studies provide important proof-of-concept evidence that ITK-deficient Tregs are not simply associated with protection but can actively ameliorate established pulmonary hemorrhage and associated systemic manifestations when transferred into wild-type recipients. We appreciate the reviewer’s recognition of the potential therapeutic significance of targeting the ITK–Treg axis.

      Weaknesses:

      The molecular analysis of Tregs isolated from unchallenged wild-type ITKdeficient mice has limited value to understand how the ITK-deficient Tregs protect against autoimmune pulmonary hemorrhages in lungs. Detailed molecular analysis of Tregs isolated from the lung will be helpful in understanding the mechanistic regulation and identifying further therapeutic targets.

      We thank the reviewer for this important observation and agree that detailed molecular characterization of lung-resident Tregs following pristane-induced pulmonary injury would provide additional insight into the mechanisms responsible for protection.

      The transcriptional analyses presented in the current manuscript were designed to identify intrinsic molecular differences associated with ITK deficiency in Tregs independent of the inflammatory environment. These studies revealed alterations in pathways including oxidative phosphorylation, mTORC1 signaling, MYC-associated programs, and cell-cycle regulation, thereby providing a molecular framework for the enhanced function of ITK-deficient Tregs.

      We recognize, however, that the phenotype and transcriptional program of Tregs within the injured lung microenvironment may differ from those observed under baseline conditions. We therefore consider direct molecular comparison of lung Tregs isolated from pristane-treated wild-type and ITK-deficient mice an important direction for subsequent mechanistic studies.

      Importantly, the principal functional conclusion of the current study is supported by the adoptive transfer experiments shown in Figure 5. Transfer of ITK-deficient Tregs into wild-type mice with established disease significantly reduced pulmonary hemorrhage and systemic injury, demonstrating that ITK-deficient Tregs themselves are capable of mediating protection. We have clarified this limitation and the need for future studies examining lung-resident Tregs in the revised Discussion. See page 21 line 353- 361.

      Reviewer #2 (Public review):

      The authors have addressed my comments appropriately.

      We sincerely thank Reviewer #2 for carefully evaluating our revised manuscript and for concluding that our previous responses appropriately addressed the reviewer’s concerns. We also appreciate the reviewer’s recognition of the potential relevance of our findings for the development of targeted therapeutic approaches.

      Reviewer #2 (Recommendations for the authors):

      I would strongly recommend removing Fig. 5J (IF), as there is no convincing signal for Foxp3. This is a well-known issue with Foxp3 Ab. If authors would like to include imaging, would recommend performing smFISH/RNAScope.

      We thank the reviewer for this helpful recommendation. We agree that the Foxp3 immunofluorescence signal in the previous Figure 5J does not provide sufficiently convincing visualization to support our conclusions. We have therefore removed Figure 5J from the revised manuscript.

      Importantly, our conclusions regarding the protective activity of ITK-deficient Tregs are independently supported by flow-cytometric analyses and, most importantly, by the adoptive-transfer experiments demonstrating that ITK-deficient Tregs can ameliorate established pulmonary hemorrhage in wild-type recipients.

      We appreciate the reviewer’s suggestion regarding smFISH/RNAscope and agree that this approach

      could provide valuable spatial information in future studies.

      Reviewer #3 (Public review):

      The novelty of this study lies in the association between ITK-deficient Tregs and pulmonary hemorrhage in autoimmunity. One limitation of this study is that the authors performed all experiments in ITK global knockout mice, in which not only T cells but all other cell types are deficient in ITK. Therefore, further studies are required for a mechanistic rationale for targeting ITK in severe inflammatory lung disease.

      We sincerely thank Reviewer #3 for recognizing the novelty of the relationship between ITK-deficient Tregs and protection from autoimmune pulmonary hemorrhage, as well as the potential therapeutic relevance of this pathway in chronic inflammatory disease.

      We agree that the use of a germline ITK-deficient mouse represents a limitation of the current study because it does not allow us to completely distinguish T-cell-intrinsic effects of ITK deficiency from potential contributions of other immune populations.

      However, our adoptive-transfer experiments provide important functional evidence supporting a direct role for ITK-deficient Tregs. Specifically, purified ITK-deficient Tregs transferred into wild-type recipients with established pulmonary hemorrhage significantly reduced pulmonary injury and associated systemic manifestations. These findings demonstrate that ITK-deficient Tregs are themselves sufficient to confer substantial protection within an otherwise ITK-sufficient host.

      Nevertheless, we agree that future studies using lineage-specific conditional ITK-deficient models will be important to define the Treg-intrinsic contribution of ITK signaling more precisely. Such studies, together with evaluation of ITK modulation in human Tregs and appropriate humanized models, will be important for determining the translational potential of targeting the ITK pathway in severe inflammatory lung disease.

      We have revised the Discussion to more clearly acknowledge this limitation and highlight these future directions. We again thank the editors and reviewers for their thoughtful and constructive comments. Their suggestions have substantially strengthened the manuscript and helped us more clearly define both the significance of our findings and the remaining questions that will guide future investigation. See the limitations of this manuscript.

    1. Author response:

      We thank the reviewers and editors for their constructive feedback and are in the process of preparing a detailed point-by-point response. In the meantime, we would like to underscore our main conclusions and highlight the consistency with this study and the prior fMRI literature.

      First, while the reviewers are correct to highlight the difficulty in interpreting null effects, the claims of our paper are primarily concerned with the positive findings. To our knowledge, this is the first evidence that social interaction perception is extracted in a fast hierarchy, which progresses from early visual features to mid-level social primitives to high-level information about communicative actions in the STS. This is an exciting and novel finding that sheds new light on the neural computations that support this core human ability. Importantly, the main null finding is the lack of difference in the onset latency between mid-level and anterior ROIs, rather than an inability to decode information in these regions (see below) and does not undercut this central claim.

      Second, we would like to highlight that, overwhelmingly, our results are consistent with the prior fMRI literature. For example:

      • Using our two-step regression procedure, we recover representations of motion energy in MT validating the use of this method

      • Further, we find representations of mid-level features in mid-level regions ~150 ms after stimulus onset, primarily the distance between people.

      This consistency, and the decoding of high-level features like communication exclusively in STS regions (as highlighted by reviewer 1), provides support for our method and shows that the EEG-fMRI correspondence extends beyond early visual regions.

      The reviewers also raise questions about potential inconsistencies with our prior fMRI study (McMahon et al., 2023). We would like to clarify those findings here, because the current manuscript relies on the same fMRI data, and thus we would not expect to see effects here that are not reported in that fMRI data. In our original fMRI study, we did not find an effect of facingness, joint action, or valence in any ROI. Further, in that study, the effect for communication was most robust in aSTS, rather than pSTS. The primary effect from our original fMRI study that we do not find with EEG-fMRI fusion is information about object-directed actions in LOC. We will address these in a more detailed point-by-point response and revision soon.

      Beyond the practical limitations of what we could find in the current fMRI dataset, we would also like to discuss the theoretical reasons for differences between our findings and the broader literature. First, our lack of finding an effect of valence likely reflects our stimuli, not neural representations. The Moments in Time computer vision dataset that our videos are derived from does not sample strongly negative videos. This restricted valence range is also evident in the behavioral ratings that participants provided.

      Further, there are many differences between how we have looked for an effect of facing direction compared to prior work in this area. First, we do not use a binary facing/not facing but a graded scale from facing to not facing, and, to our knowledge, ours is the only study that has investigated a facing effect in naturalistic videos. It is possible that due to the graded scale or the natural stimuli that the facing effect is too subtle for us to detect. Another possibility is that while facingness is a social cue that is encoded in the brain, it is not a dominant cue in naturalistic videos where other cues are present (e.g., the distance between people, physical contact, and contingent motion).

      Finally, on joint action, a type of physical social interaction between people, there is now convergent evidence from multiple studies that this may not be the primary type of social interaction represented in the STS. McMahon et al. (2023) found that communicative, not joint interactions, predicted STS responses. This was replicated and extended in (Zhao et al., 2025), where we find that joint action representations are more represented in lateral occipital regions, while communicative interactions are represented in the STS. From ongoing work in controlled stimuli (McMahon & Kanwisher, 2026 VSS), we have found that regions in the STS respond more to communicative interactions than joint actions. This present study provides new insight into the computations that support this, suggesting that information about communicative interactions is extracted along a spatiotemporal hierarchy, consistent with the fast timescale of visual processing, along the newly proposed lateral stream.

      References:

      McMahon, E., Bonner, M. F. & Isik, L. Hierarchical organization of social action features along the lateral visual pathway. Current Biology 33, 5035-5047.e8 (2023).

      Zhao, Y., McMahon, E. & Isik, L. Separate Neural Representations for Physical and Communicative Social Interactions: Evidence from Data-driven Voxel Decomposition. Preprint at https://doi.org/10.31234/osf.io/fmnq9_v1 (2025).

      McMahon, E. & Nancy Kanwisher. The STS Responds Preferentially to Communicative Signals. Vision Science Society; May 15–19, 2026; St. Petersburg, FL.

    1. Author response:

      The following is the authors’ response to the previous reviews

      Public Reviews:

      Reviewer #2 (Public Review):

      Summary:

      Drosophila hematopoiesis has been shown to be governed by a number of signaling pathways such as JAK/STAT and Dpp. This important study shows the role of nutrient sensing and autophagy in determining blood cell differentiation. The authors show that General control non-derepressible 5 (Gcn5), a histone acetyltransferase affects blood cell differentiation. Gcn5 also negatively regulates autophagy through its effector TFEB which directly regulates autophagy genes. The authors also show that mTORC1 modulates Gcn5 levels and through it, TFEB activity thus acting as a fine-tuning mechanism that maintains optimal levels of autophagy.

      Strengths:

      The main strength of the work lies in the interesting finding that cellular metabolic processes such as autophagy have a direct role in blood cell differentiation and has the potential to be of interest to those working on vertebrate haematopoiesis as well. The report has generated intriguing data, using promoters specific for sub-sections of the lymph gland, that different cellular subsets of the lymph gland contribute differently towards haematopoiesis, but this is not followed up in detail and the final conclusions are derived from a combination of whole lymph gland perturbations as well as those from specific promoters.

      Weaknesses:

      (1) Gc5 seems to be expressed throughout the lymph gland but modulating it in the subsections does not have the same result. It is very striking that the knockdown of Gcn5 in the prohemocyte population does not have an effect on differentiation whereas overexpression does. The modulations of Gcn5 in PSC also have variable effects across hemocyte subpopulations which is not explored in the manuscript.

      We have now explained and discuss why Gcn5 modulation could be affecting the PSC size. Please check Discussion section Paragraph 1 line 10 onwards.

      Interestingly, also the domain deletion constructs show a differential effect on blood cell differentiation when altered solely in the prohemocytes which is not explained.

      Currently, with our observations all that we can comment about that data is that expression of domain deletion mutants causes aberrant hematopoiesis indicating a dominant-negative phenotype since they are expressed in the wild-type genetic background. Beyond this, we will be exploring mechanistically how these domains are functioning during hematopoiesis in future studies. We have already described the dominant negative effect in the text: Discussion Section Paragraph 3.

      While Gcn5 can be seen in all sections of the lymph gland in the first figure, under the HHLT-Gal4 and Hml-Gal4, Gcn5 looks cytoplasmic and almost completely excluded from the nucleus strikingly unlike Gcn5 expression under the Collier-Gal4 and Dome-Gal4.

      We have now revised Figure 1 and have only included the images with Collier-Gal4 and Dome-Gal4 which clearly shows both the niche cells, Dome-positive progenitors and Dome-negative cells of the primary LG lobe essentially showing that Gcn5 is expressed throughout the primary LG lobe. In Fig. 1C-F’, Gcn5 expression is both in the nucleus and cytoplasm as this molecule shuttles between cytoplasm and nucleus. The staining pattern with the other Gal4 could be due to problems in the immunofluorescence protocol and acquisition parameters. We have now removed those images from Figure 1. Please check revised Figure 1.

      The rest of the experiments in the manuscript are done with multiple promoters, with autophagy flux measured by modulating Gcn5 with a pan hemocyte promoter, but the mTORC1-Gcn5 axis is explored using chemical modulators which affect the whole of the lymph gland (Fig7) or using two pro-hemocyte promoters (Fig8).

      We have used a pan-hemocyte promoter for the autophagy analysis to investigate if Gcn5 regulation over autophagy is a hemocyte-specific effect which we indeed see. We have removed the western blot data now in the revised manuscript where we looked at Atg8 and p62 levels in whole larval lysates when Gcn5 was perturbed using hemocyte driver as the results were puzzling and difficult to comprehend given the complete absence of a p62 band in Gcn5 knockdown conditions. Also, it’s worth noting that Hml-Gal4 is also active in the LG hemocytes. We did 2 alternate promoters for prohemocytes to cross-validate some of our results and the chemical modulators experiment was done since effects like mTOR inhibition/nutrient sensing effects are systemic and hence such modalities were employed.

      (2) The knockdown of Gcn5 seems to affect the gland size (A compared to B and C). Since mTORC1 is a central regulator of cell size, it is possible that some of the effects seen in these knockdowns are potentially through mTORC1 affecting size suggesting that the signalling axis between mTORC1 and Gcn5 might not be a one-way axis as suggested in Figure 9. Also, this would mean that in experiments where absolute cell counts of crystal cells or niche cells are used to assess blood cell differentiation, further analysis to consider total cell numbers in the lymph gland would strengthen the manuscript.

      It is a possibility that Gcn5 perturbation could be affecting lymph gland size although we have not seen any consistent trend that would point towards this phenotype either upon knockdown or over-expression. We believe Gcn5 controls blood cell differentiation phenotypes strongly via mTORC1. But in order to answer reviewer’s comment we have now re-analyzed our crystal cell differentiation data particularly and quantitated it and represented it as crystal cell differentiation index for dome-Gal4 specific Gcn5 modulation and for the data with genetic modulation of mTORC1 pathway. Please see Fig 3P and S10J for the revised analysis.

      (3) A genetic manipulation of mTORC1 specifically in the pro hemocytes would strengthen the role of mTORC1 in the pathway rather than the chemical modulation which affects the whole of the lymph gland.

      We thank the reviewer for their useful critique. We have now addressed this concern and we have genetically perturbed the mTORC1 pathway in the progenitors using both abrogation of TORC1 via depletion of Tor or Raptor or by activation using over-expression of Rheb. We have now included this data as Supplementary figures – Fig S10 and S11 and have described it in the results section. Please see results section “Chemical or genetic modulation of mTORC1 activity controls blood cell differentiation” in the revised manuscript.

      Recommendations for the authors:

      Editors Comments:

      Dear Rohan,

      Thank you for the substantial effort that has gone into the revision. The added data and the removal of some difficult-to-interpret results have made the manuscript more coherent.

      After discussing the revised manuscript with the reviewers, our shared view is that the main interpretive issue still remains. The biology remains quite complex: Gcn5 perturbation in different lymph gland compartments still gives non-reciprocal phenotypes; the Gcn5/autophagy/mTORC1 experiments draw on different drivers, cell populations and systemic drug treatments; and the mTORC1 "override" experiment is still stronger as a pharmacological observation than as a clean pathway/epistasis result. As a result, the current framing still makes the relationship between Gcn5, autophagy, mTORC1 and haematopoiesis seem more direct than the data warrant.

      We therefore ask that you revise the text to engage more directly with these unresolved points. And we urge you to please revise the title, abstract, model and discussion so that the manuscript frames the data as supporting a broad connection between Gcn5, autophagy, mTORC1 signalling and blood cell homeostasis, rather than as establishing a resolved linear Gcn5-mTORC1-TFEB/autophagy pathway.

      Thank you for sending our manuscript for review again. We are glad that the revised data has made the manuscript more coherent along with removal of the data that was difficult to interpret.

      We would like to thank the editor for the suggestions. We have now revised the title, abstract, model of our study and also toned down our conclusions and removed extrapolations if any. We now project a broader role of Gcn5 and mTORC1 in regulating autophagy and thereby hematopoiesis in the lymph gland. Our revised discussion section addresses this critical suggestion given by the editor. Please refer to the changes made in the title, abstract, parts of the results and discussion.

      Reviewer #1 (Recommendations for the authors):

      There are still many typos along the manuscript.

      The authors changed their quantification of the crystal cell phenotype to "crystal cell index" in some figures but kept the initial "crystal cell number" in others. They should be consistent. Also, the scale of the axes in Fig. 2O , 2T and 3P is inadequate, as it is impossible to discern the distribution of the data or possible differences between genotypes.

      We thank the reviewer for this comment. We have now gone through the manuscript thoroughly and made the required changes. We have taken into consideration and reanalysed the data and changed all quantification to crystal cell differentiation index to make the data uniform and consistent. The scale of axes as suggested for Fig. 2O, 2T and 3P have been modified to ensure the data points are clearly distributed and observable.

    1. Author response:

      The following is the authors’ response to the original reviews.

      eLife Assessment:

      This important study extends a model of cortical normalization (ORGaNICs) to interacting cortical areas and shows that communication through coherence and communication subspaces can arise from a single set of dynamics. The evidence is solid, showing analytically that contrast-dependent gamma dynamics and a low-dimensional inter-areal communication subspace arise from one parameter set, though the comparisons to data remain qualitative and the analytics rest on a linearization that is not checked against numerical simulation. The work will interest neuroscientists and theorists concerned with inter-areal communication, cortical oscillations, and divisive normalization.

      We thank the editors and reviewers for this assessment. We have addressed both stated qualifications. On the linearization, we now validate the closed-form power and coherence spectra against direct numerical simulation of the full nonlinear stochastic circuit at every contrast (new SI Fig. S6 and SI Sec. II). On the comparison to data, in addition to the unfitted comparison of Fig. 2, we now provide a quantitative comparison in which the model is fitted to the experimental power and coherence spectra, with residuals reported at every contrast (new SI Fig. S7 and SI Sec. III).

      Public Reviews:

      Reviewer #1 (Public review):

      In this paper, Pal and colleagues propose a mechanistic unification of two influential accounts of inter-areal communication: communication through coherence and communication subspaces. A major strength of the paper is that it does not treat coherence and communication subspaces as independent phenomena, as typically done, but instead derives both from the same circuit with divisive normalization. In this framework, noise-driven fluctuations around the normalized fixed point determine covariance and cross-power structure (which, in retrospect, makes so much sense to be related). Then, they show how these determine linear prediction performance and the effective dimensionality of the communication subspace. They also show (however not very visually, see recommendation below for a figure) how divisive normalization is crucial to shape inter-areal coherence and the dimensionality of communication.

      I found this conceptual contribution potentially very influential, but somewhat obscured by the technical complexity of the model. The central intuition (I think) is that recurrent normalization can organize cross-area fluctuations, both frequency-specific correlations and cross-covariances. Took me a while to grasp this insight, mostly because I was stuck with the model details. Note that I have some experience with network dynamics, but not with this particular model.

      We thank the reviewer for this positive assessment. We agree that recurrent normalization shapes the cross-spectral density of the noise-driven fluctuations about the normalized fixed point, and that power, coherence, and the communication subspace can therefore be viewed as complementary readouts of the same underlying dynamics. To make this central connection explicit from the outset, we have added a new paragraph, “The core mechanism in brief” (Results, end of “Theory”), which states this mechanism before the main results are presented. The dependence of coherence and communication-subspace dimensionality on normalization is shown in SI Figs. S4e–h and S5, which are now cited wherever the role of normalization is discussed. In addition, the new Discussion subsection “Experimental predictions of the model” describes how normalization could be manipulated experimentally and the readouts expected.

      Reviewer #2 (Public review):

      Summary:

      The authors extend the ORGaNICs framework (a recurrent circuit that dynamically implements divisive normalization) to connected cortical areas with explicit top-down feedback. Because the network has a known analytical fixed point that coincides with (or closely approximates) the normalization equation, the authors can linearize about that fixed point and derive closed-form expressions for the power spectral density, inter-areal coherence, and communication subspaces. Using a two-area instantiation (V1 & V2) with a single fixed parameter set and no data fitting, they show the model reproduces: (i) contrast-response functions with steeper slope V2; (ii) gamma-band power and coherence peaks that shift to higher frequency with contrast; and (iii) a low-dimensional inter-areal communication subspace that is lower-dimensional than the within-area subspace. They derive parallel predictions of what happens by changing model parameters: feedback gain enhances inter-areal and suppresses within-area communication, and normalization is necessary for both the oscillatory dynamics and the reduced subspace dimensionality. A three-area extension (V1&V4, V1&V5/MT) is used to argue that differential top-down feedback can dynamically route functional connectivity.

      We thank the reviewer for this summary.

      Strengths:

      (1) Analytical tractability: Deriving power spectra, coherence, and communication-subspace structure in closed form from a known fixed point is genuinely valuable.

      (2) Conceptual unification: Framing coherence and communication subspaces as arising from the same normalization-driven dynamics is an elegant and useful contribution.

      (3) Breadth from few assumptions: A large range of phenomena (contrast gain, gamma dynamics) emerges from normalization-based model assumptions.

      (4) Biological grounding: The mapping of model variables onto identified cell types connects the abstract computation to known cortical microcircuitry.

      (5) The prediction that input-gain versus feedback-gain modulation produce distinct spectral signatures gives experimentalists a clear way to test the framework.

      We thank the reviewer for the positive assessment.

      Weaknesses:

      (1) Comparisons are qualitative, not quantitative: The theory/experiment panels are visual side-by-side comparisons. There is no quantitative goodness-of-fit for any predictions.

      We thank the reviewer for this comment. We agree, and have added a quantitative comparison. New SI Fig. S7 and SI Sec. III fit the model parameters to the experimental power and coherence spectra and report the residuals at every contrast.

      (2) The simulations use τ ≈ 1ms for all cell types, which the authors acknowledge is unrealistically short; realistic values would shift the gamma peaks to lower frequencies.

      We thank the reviewer for this comment. We agree. The Limitations (Discussion) state that more realistic values would shift the gamma-band oscillations to lower frequencies, and that when all time constants were released as free parameters in the fit to the experimental spectra (SI Fig. S7) they converged to values between 0.2 and 3ms. The time constants are now described consistently as effective population time constants rather than as intrinsic single-neuron time constants (Limitations).

      (3) Divisive normalization is a special case and is recovered exactly only for the identity recurrent matrix (self-normalization). Some statements that the circuit implements divisive normalization exactly need softening.

      We thank the reviewer for this comment. We agree, and have softened the statements throughout. The main text now states that exact recovery of Eq. 2 requires W<sub>11</sub> = I and β = γ = 1, that for the centre-surround W11 used in all reported results the circuit closely approximates normalization (to within 0.6%), and that the fixed point is obtained numerically, at first mention (Results, “Theory”), in the Methods (“The Model” and the new subsection “Numerical computation of fixed points”) and in the Discussion (“Normalization”).

      (4) The element-wise (multiplicative) interaction in the modulator dynamics is not tied to a specific cellular mechanism.

      We thank the reviewer for this comment. We agree: The Limitations (Discussion) state that, while weighted sums and gain control may be implemented via balanced excitatory–inhibitory mechanisms, we can only speculate about the cellular mechanisms for the element-wise products. We speculate that the element-wise product between presynaptic firing rates in Eq. 1b might be mediated by coincident spike detection (assuming that each of the spike trains is Poisson and that the synaptic current is proportional to the probability of coincident spikes within a short time window (Srinivasan & Bernard, 1976)), and that the element-wise product between postsynaptic membrane potential and presynaptic firing rate in Eq. 1c might be mediated by NMDA receptors (Polsky, Mel & Schiller, 2004; Silver, 2010) (see Discussion, last paragraph of “Biological Plausibility”).

      Reviewer #3 (Public review):

      Summary:

      The work of Pal and colleagues considers a hierarchical and multi-population version of the “oscillatory recurrent gated neural integrator circuits” (ORGaNICs) model, showing through analytics that the model captures multiple relevant experimental results: first of all, its oscillatory dynamics produce a profile with high resemblance to experimental results, both in terms of decay of power at high frequency and in terms of shifting peak as a function of stimulus contrast. Second, inter-areal communication subspace dimensionality is lower than within-area dimensionality. The authors then proceed to further characterize the model’s response properties as a function of input and feedback gain. In particular, they find that frequencies transmitted with higher strength also carry more information, that changing gain modifies the dimensionality of communication subspaces, and that these properties can be used in a three-layer model, where an upstream area can select which downstream area to communicate to, based on the strength of feedback gain.

      We thank the reviewer for the summary.

      Strengths:

      This work demonstrates that a single-circuit model with normalization properties can capture both the oscillatory dynamics and the inter-areal communication properties measured in cortical circuits, matching multiple experimental results. The full analytical tractability of the model is highly advantageous, allowing for easier exploration of parameters, replicability, and effective interpretations of results compared to purely numerical approaches.

      The work also makes a useful conceptual link between normalization, coherence-based communication, and subspace-based communication. In particular, it shows how both phenomena can emerge from the same circuit dynamics, where normalization is a key factor.

      Interestingly, the model is also extended to multiple areas, showing how attention (in the form of changes in feedback gain) can synchronize the activity of a downstream area with one of two upstream areas, thus effectively selecting which area to communicate with.

      In general, this is an interesting computational framework and a useful starting point for future modeling work. A particular strength is that it connects normalization, oscillatory dynamics, coherence, and communication subspaces within one analytically tractable model, making it possible to generate mechanistic hypotheses about when inter-areal communication should be stronger, lower-dimensional, or preferentially routed through feedback.

      We thank the reviewer for the positive assessment.

      Weaknesses:

      Although I see the analytic approach as a strength, at the same time I regard the lack of any numerical comparison as a big weakness. Circuit simulations would not only confirm the correctness of the analytics, but also offer further insights on the error margins and on the regimes where the analytics are valid. This is because, to my understanding, the analytics are based on a linear approximation around the operating regime, which means deviations might be expected, especially for high gain levels in the input, or in the feedforward and feedback pathways.

      We thank the reviewer for this comment. We agree that a numerical check of the linearization is required, and have added one. New SI Fig. S6 and SI Sec. II integrate the full nonlinear stochastic system (SI Eqs. S31–S44, with the firing-rate noise and the filtered synaptic noise of SI Sec. VI) with the Euler–Maruyama scheme (time step 10 µs; 100 independent trials of 16s at each contrast) and compare the V1 power spectra and V1–V2 coherence spectra estimated from the simulated trajectories (Welch’s method) with the closed-form expressions at all eight contrasts of Fig. 2. At the baseline parameters, the root-mean-square deviation is below 0.017 for the normalised power and below 0.018 for the coherence, and the maximum absolute deviation is below 0.072, at every contrast; residuals are shown in the lower panels of Fig. S6. The Methods (“Power and coherence spectra”) now describe this validation. On the regime of validity: the linearization holds for small fluctuations about the fixed point, as stated in the Methods, and the simulations bear this out. When the amplitudes of the noise sources are increased, the deviation between the simulated and the analytical spectra grows, and it does so first at the lowest contrasts. This is because at low contrast < 10% the activities lie near zero, and the noise fluctuations can drive them negative, where the rectification in the model clips them to zero; the linearized dynamics do not capture this clipping. Note that changing the strength of the noise does not alter the analytical results, since the plotted spectra are all normalized. The deviations do not, however, grow with the gains: changing the input or feedback gain changes the fixed point, and the linearization about the new fixed point remains valid, because its accuracy is controlled by the strength of the fluctuations relative to the fixed point, not by the gains themselves. This characterization of the validity regime is now stated in SI Sec. II. All results reported in the paper use the baseline parameters, for which the linearization is accurate at every contrast and for all reported gain values. The stable ranges of the gains are given in SI Table S2.

      Another problem is that the analytically tractable model seems to rely on effective connectivity weights that break Dale’s law. Numerical simulations with explicitly modeled excitatory and inhibitory units might give insights into effects due, e.g., to the additional transmission delays mentioned in the Discussion.

      We thank the reviewer for this comment. We agree, and have made the distinction between effective and anatomical connectivity explicit. The Results (“Theory”) and the Methods (“The Model”) now state, where the matrices are introduced, that the recurrent, feedforward and feedback matrices are effective (net) connectivity, with negative entries standing for disynaptic inhibition through interneurons that are not modelled explicitly. The Limitations (Discussion) now state that the circuit as written does not respect Dale’s law at the level of individual connections, that the posited inhibitory interneurons would introduce additional delays, and that examining how inter-areal synchronization depends on feedback delay is an important direction for future work.

      Another weakness is the use of the term “predictions” to indicate features of the model dynamics that are purely described in the context of the model parameters. Although the model’s response properties may certainly lead to predictions, I think the term requires a better contextualization in terms of neurophysiology and experimental neuroscience. The Discussion draws very interesting and valuable bridges between neuron morphology, interneuron types, and model parameters. But it seems it’s left to the reader to backtrack and figure out which biological mechanisms or experimental manipulations should correspond to changes in input or feedback gain, and how these should be distinguished from possible changes in feedforward gain.

      We thank the reviewer for this comment. Each prediction is now grounded in a candidate experimental manipulation and a measurable readout in a new Discussion subsection, “Experimental predictions of the model”, which covers each gain parameter, the frequency-resolved subspace, the routing result and normalization, and states explicitly that the proposed manipulations of the gains are speculative and rest on the hypothesized cell-type mapping. The V2 input gain is addressed in our response to the next point.

      Relatedly, the manuscript places substantial emphasis on modulation of feedback gain, but does not comparably explore modulation of the feedforward gain, β<sub>2</sub>, which regulates the V1-to-V2 drive.

      This seems important because changes in feedforward gain could also influence communication subspace dimensionality and oscillatory dynamics. Therefore, predictions related to top-down feedback modulations should be taken with a grain of salt.

      We thank the reviewer for this comment. We agree, and have added the V2 input gain to every analysis in which feedback and V1 input gain are varied. New SI Fig. S8 varies β<sub>2</sub> over the same range as β<sub>1</sub> (0.5–1.5) and reports, side by side with feedback and V1 input gain, the contrast-response functions of V1 and V2, the V1 power spectra and V1–V2 coherence spectra at 3% and 50% contrast, and the inter- and within-area prediction performance at 100% contrast. V2 input gain has a signature distinct from both feedback and V1 input gain:

      - Increasing β<sub>2</sub> leaves V1 responses unchanged and enhances only V2 responses (Fig. S8c), whereas feedback and V1 input gain enhance both areas.

      - At 3% contrast, β<sub>2</sub> produces neither the alpha peak in V1 power nor the beta-band coherence peak that appear at low feedback gain (Fig. S8f,l).

      - At 50% contrast, increasing β<sub>2</sub> shifts the gamma peak in power and coherence to higher frequencies and broadens it, like feedback gain, but also reduces its amplitude (Fig. S8i,o).

      - Increasing β<sub>2</sub> enhances inter-areal communication, like feedback gain, but leaves within-area communication approximately unchanged (Fig. S8r), whereas feedback gain reduces within-area communication and V1 input gain reduces both.

      These results are reported in the Results (“Contrast response functions”, “Inter-areal coherence”, “Communication subspaces”; the “V1 power spectra” section refers the reader to SI Fig. S8 for the V2 input gain), in the Discussion (opening summary, “Role of feedback” and “Experimental predictions of the model”).

      Last but not least, the model dynamics are split among multiple elements and nonlinear interactions, reaching a level of complexity far higher than the other ORGaNICs formulations present in the literature. The authors derive these dynamics in the supplementary material, as a dynamical system that converges to a fixed-point solution that includes “exact divisive normalization”. I wonder, however, if there could be simpler solutions that also produce normalization, either approximate or in a different form than the one proposed by the authors. Note also that the designation of “excitatory neurons” is misleading: despite the presence of two explicitly inhibitory populations, the “excitatory” units also interact with negative effective weights both recurrently and in the inter-areal interactions, thus breaking Dale’s law.

      We thank the reviewer for the comment. The complexity is, moreover, not unstructured: as now stated in the Results (“Theory”), each population performs a defined operation — principal cells y sum the gain-modulated input, recurrent and feedback drives, u accumulates the normalization signal, a implements the division, and q provides the sign inversion required by the feedback term in the dynamics of a, and it is through these populations that normalization is implemented dynamically, and simultaneously across the reciprocally coupled areas, rather than imposed as a static input–output relation. Whether a materially simpler circuit could produce normalization, approximately or in a different form, while retaining analytical tractability is an open question that we do not resolve here; we would regard such a circuit as a valuable simplification of the present framework. On terminology: we agree, and have changed it. The y population is now called “principal cells” (or “principal neurons”) throughout the main text, figure captions and SI; “excitatory” is reserved for the anatomically excitatory populations in the hypothesised cell-type mapping (Discussion, “Biological plausibility”); the distinction between effective and anatomical weights is stated where the matrices are introduced (Results, “Theory”); and the Limitations state that the principal cells interact through mixed-sign effective weights both recurrently and across areas.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      First of all, my sincere apologies for my long delay. It has been quite a hectic period.

      If I could suggest one improvement, it would be to add an early conceptual figure and/or minimal toy model that illustrates the core mechanism before introducing the full circuit. For the illustration, I would try to get inspiration from illustrations of the original Semedo et al paper. Such a figure could show how divisive normalization shapes the covariance/cross-power structure, how this affects coherence, and how the resulting eigen spectrum gives rise to a low-dimensional communication subspace. Starting from this stripped-down mechanism would make the novel insight more transparent, after which the more biologically motivated model would be easier to appreciate.

      We thank the reviewer for this suggestion. We agree that the core mechanism should be stated before the full circuit is introduced, and have done so in the text rather than with a new figure. A new paragraph, “The core mechanism in brief”, closes the “Theory” section (Results), before any result is presented. It follows the progression the reviewer outlines: the noise-driven fluctuations about the normalized fixed point are characterized by the cross-spectral density matrix (Eq. 6); the power spectra are its diagonal entries, the coherence its normalised off-diagonal entries (Eq. 7), and the communication subspace follows from its frequency-resolved covariance through reduced rank regression, so that power, coherence and the communication subspace are complementary readouts of the same underlying dynamics. How normalization shapes this matrix, by creating a resonance and by suppressing weakly driven neurons, which lowers its rank, is stated in the Discussion (“Unified view of inter-areal communication”), and removing normalization removes all three effects (SI Fig. S4e–h). The full circuit is then introduced as the implementation of this mechanism. We have not added a schematic figure, because the corresponding panels already exist: the with/without-normalization comparison (SI Figs. S4 and S5).

      Minor comments/suggestions:

      The authors forgot to cite other work modelling communication subspaces. Citing them could improve impact. Disclaimer: I am among the authors of one of them.

      https://www.nature.com/articles/s41467-023-42519-5

      https://www.science.org/doi/full/10.1126/sciadv.adl6120

      https://www.pnas.org/doi/10.1073/pnas.2404039122

      https://www.biorxiv.org/content/10.64898/2026.05.18.725829v1.abstract

      We thank the reviewer for these references. We have added all four (Barbosa et al. 2023; Gozel & Doiron 2024; Clark & Beiran 2025; Mastrogiuseppe et al. 2026) in the Introduction, where communication subspaces are introduced.

      It could improve the impact if the authors could flesh out how they would test ‘experimentally testable predictions’ (e.g., lines 162, 329).

      We thank the reviewer for this suggestion. We agree, and have revised accordingly. Each prediction is now paired with a candidate manipulation and a readout in a new Discussion subsection, “Experimental predictions of the model”.

      Figure 2 c-d and e-f could make the message stronger if a correlation between model and data is shown: how good is the prediction?

      We thank the reviewer for this suggestion. We agree that a quantitative measure of agreement is needed, and have provided it as a fit rather than a correlation coefficient. New SI Fig. S7 and SI Sec. III fit the model to the experimental power and coherence spectra of Roberts et al. (2013) at all measured contrasts and show the residuals. The Fig. 2 caption and the Results (“V1 power spectra”, “Inter-areal coherence”) now cite this comparison.

      Figure 4c is very interesting and deserves more spotlight (could even be tested with available data?)

      We thank the reviewer for this suggestion. We agree, and have given this result more prominence and specified the test. It is stated in the Abstract in its own right. The Methods (“Frequency decomposition of the communication subspace”) now end with a paragraph that states how the analysis may be applied to experimental recordings: from the cross-spectral density matrix of simultaneously recorded V1 and V2 populations, its real part at each frequency is the frequency-specific covariance, whose source, target and cross blocks give the communication subspace, the prediction performance and the dimensionality at that frequency in closed form (Eqs. 20 and 22); no band-pass filtering or per-band regression is needed. The resulting test, that the dimensionality should be smallest in the band of peak V1–V2 coherence and that this band should shift to higher frequency with contrast, is stated at the end of that Methods paragraph and in the Discussion (“Experimental predictions of the model”). We have not performed this analysis, which requires the raw simultaneous recordings.

      Reviewer #2 (Recommendations for the authors):

      Major:

      (1) If possible, try to add at least one quantitative model-data comparison (variance explained) even without fitting if needed, so readers can gauge agreement beyond visual inspection.

      We thank the reviewer for this comment. We agree, and have added a quantitative comparison. New SI Fig. S7 and SI Sec. III fit the model parameters to the experimental power and coherence spectra measurements and report the residuals at every contrast.

      (2) Show how the gamma-peak predictions change under physiologically realistic time constants (e.g., 10-20 ms), so that readers get an idea.

      We thank the reviewer for this suggestion. The Limitations subsection of the Discussion now explains that if every time constant of the model is multiplied by a common factor k then every spectral feature would be shifted to a frequency k times lower with its shape preserved. The Limitations also now state that when all time constants were released as free parameters in the fit to the experimental spectra (SI Fig. S7) they converged to values between 0.2 and 3ms. The uniform 1ms values are now described throughout as effective population time constants. We decided not to add a figure because it would look identical to Figs. 2 and 3 with a relabelled frequency axis.

      (3) For the communication-subspace results, report how dimensionality estimates scale with the number of modeled/subsampled neurons, so the comparison to the experimental literature is calibrated.

      We thank the reviewer for this suggestion. We agree, and have added the analysis as new SI Fig. S9. Fig. S9 reports the dimensionality of the inter-areal (V1–V2) and within-area (V1–V1) communication subspaces (i) as a function of the number of modeled principal neurons per area, N = 9, 18, 36, 72 and 144, at the sampling fraction of the main text (30/72 of the neurons as source and as target, i.e. 4–60 neurons; the connectivity kernels and normalization pool are defined on the ring and scale with N, with no parameter re-tuned), and (ii) as a function of the number of sampled source and target neurons, 5–30, at N = 72. Each point is the mean ± SD over 200 random draws of source and target populations at 100% contrast and baseline parameters, with dimensionality defined as the rank at which prediction performance reaches 95% of its full-rank value. The dimensionality grows slowly with both quantities (roughly two-fold over the 16-fold change in N), remains far below the number of sampled neurons, and the inter-areal subspace is lower-dimensional than the within-area subspace at every population size.

      Minor:

      (1) Qualify quantitative-sounding language to reflect that comparisons are qualitative and unfitted.

      We thank the reviewer for this comment. We agree, and have revised accordingly. The unfitted comparisons are now described as qualitative: “successfully replicates key experimental observations” now reads “reproduces the main qualitative features” (Results, “V1 power spectra”), the captured trends and observations are described as qualitative in the power-spectra and coherence sections, and “align well with” now reads “qualitatively consistent with the experimental data” (Results, “Communication subspaces”). The fitted comparison of SI Fig. S7 is cited alongside the power-spectra and coherence comparisons.

      (2) Clarify in the main text the scope of the “exact normalization” claim

      We thank the reviewer for this comment. We agree, and have revised accordingly. At first mention (Results, “Theory”) the main text now states that the implementation is exact for W<sub>11</sub> = I with β = γ = 1, that for the centre-surround W<sub>11</sub> used in all reported results the circuit closely approximates normalization, and that the fixed point for the parameters used is obtained numerically by integrating the deterministic dynamics to steady state.

      Reviewer #3 (Recommendations for the authors):

      (1) Abstract: I think the text could be improved in terms of clarity and readability. For example, the (f) for frequency appears only after the 1/f<sup>4</sup>, and similarly for the explanation for “communication”. The term “high-coherence” is not properly defined.

      We thank the reviewer for this comment. We agree, and have revised the Abstract. Frequency and its symbol f are introduced together before 1/f<sup>4</sup> appears; “communication” is defined at first use (“the ability to linearly predict neural activity in one brain area from neural activity in another”); “high-coherence frequencies” is replaced by “the frequencies at which V1–V2 coherence peaks”.

      (2) L50 and L56: The term “a priori constraints” seems to refer to two general features of the model. The model, however, is much more constrained in terms of parameters and architecture. So the statement that “these two constraints alone give rise to a rich set of emergent properties” is not really corroborated by the results.

      We thank the reviewer for this comment. We agree, and have revised the Introduction. It now states the two assumptions (a hierarchy with feedforward, recurrent and feedback connections; recurrently implemented normalization within each area) and then notes that a concrete model additionally requires choices about the connectivity, the normalization pool, and the noise, which are specified in the Methods and whose influence on the results is examined in SI Fig. S4 and the SI section “Robustness with respect to model parameters”. The sentence “Remarkably, these two constraints alone give rise to...” now reads “Given these choices, and a single set of parameters, the theory gives rise to...”.

      (3) L69: “competing hypotheses”, but they were called “complementary hypotheses” in L34.

      We thank the reviewer for this comment. We agree, and have made the wording consistent. Communication through coherence and communication subspaces are now described, in the Introduction and in the Discussion (“Unified view of inter-areal communication”), as hypotheses that have been treated as alternatives in the literature and that our results show to be complementary.

      (4) L132: “all neurons perform the same computation”; this comment is a bit too generic and dismissive.

      We thank the reviewer for this comment. We agree, and have rewritten the sentence as a neutral statement where it first occurred (Results, “Theory”) and removed the duplicate sentence from the Discussion (“Biological plausibility”). In Wilson–Cowan-type excitatory–inhibitory models the same form of rate equation is applied to each population, with different signs and weights, whereas here the four populations perform different roles with structurally different equations.

      (5) L134: “unique computations to each cell type” although it is clear that different cell types have different roles in the overall dynamics, it is not clear to me which is the unique computation attributed to each of them.

      We thank the reviewer for this comment. The computation performed by each cell type is now stated at that point in the text (Results, “Theory”): principal cells y sum the gain-modulated input, recurrent and feedback drives (squaring output nonlinearity); excitatory modulator cells u accumulate the normalization signal, a weighted sum of principal-cell responses (square-root output nonlinearity); inhibitory modulator cells a implement the division, i.e. the multiplicative gain control of the recurrent and feedback drives; and inhibitory cells q track principal-cell activity and provide the sign inversion required by the feedback term in the dynamics of a (SI Eqs. S21–S22). Additionally, they all have different activation nonlinearities.

      (6) L146: “positive and negative weights”: mixed signs for feedforward and feedback weights.

      We thank the reviewer for this comment. We agree, and have revised accordingly. The phrase now reads “an embedding matrix of effective weights”, followed by a new sentence stating that all weight matrices describe effective connectivity rather than anatomical synapses and that negative weights may be implemented with disynaptic inhibition through interneurons that are not modelled explicitly, with a cross-reference to the Discussion. The same statement accompanies the definition of the matrices in the Methods (“The Model”).

      (7) L160: Again mixed signs for recurrent weights.

      We thank the reviewer for this comment. We agree, see the response above.

      (8) L189: Normalization is exact, but only for parameters different from those used. I think it should be added there that the fixed point for the parameters in use is found numerically through simulation of the dynamics.

      We thank the reviewer for this suggestion. We agree, and have added the statement in those terms. The passage now states that the implementation is exact only for W<sub>11</sub> = I with β = γ = 1, that for the centre-surround W<sub>11</sub> used in all reported results the circuit closely approximates normalization (deviates from Eq. 2 by less than 0.6%), and that the fixed point for these parameters is obtained numerically by integrating the deterministic dynamics to steady state, after which all spectra and subspaces are computed in closed form by linearising about it. The same statement is made in the Methods, in the new subsection “Numerical computation of fixed points”.

      (9) L212: There should be something more explicit to corroborate the “experimentally testable”.

      We thank the reviewer for this comment. We agree, and have revised accordingly. Each prediction is now paired with a manipulation and a readout in a new Discussion subsection, “Experimental predictions of the model”, which is cited where the predictions are stated in the Introduction and the Discussion.

      (10) L214: I think it’s important to clarify a bit more that even if both areas have input gains, the manipulation is only of the input gain in the upstream area, β<sub>1</sub>.

      We thank the reviewer for this comment. We agree, and have clarified this at that point in the text (“with the V2 input gain β<sub>2</sub> held at its baseline value”) and in the captions of Fig. 3 and SI Figs. S1–S3, each of which now states that β<sub>2</sub> is held at 1.0. β<sub>2</sub> is varied separately in new SI Fig. S8.

      (11) Figure 2: Please consider using a better color scale for the power and the coherence lines. The lower three contrasts are literally indistinguishable. Same for the top two contrasts.

      We thank the reviewer for this suggestion. We have retained the palette, for the following reasons. The palette is the “Reds” sequential scheme of matplotlib, derived from the ColorBrewer scheme of the same name (Harrower & Brewer, 2003). The curves encode an ordered variable (contrast), for which a single-hue sequential palette is the recommended choice (Zeileis et al., 2020). This encoding is also colour-vision-deficiency safe: the curves are distinguished by lightness rather than by red-versus-green discrimination, and the ColorBrewer “Reds” scheme is classified as colourblind-safe on the basis of empirical testing with colour-vision-impaired viewers (Olson & Brewer, 1997). The same palette is used in the new SI Figs. S6 and S7 for consistency.

      (12) L273: Something that confuses me is how to disambiguate between input gain and input intensity, since the theory considers effects around fixed points. This equivalence is also mentioned in the discussion.

      We thank the reviewer for this comment. In the model, the V1 input gain β<sub>1</sub> enters the dynamics only through the product β<sub>1</sub>z<sub>1</sub> (Eq. 1a), and the input drive z<sub>1</sub> is proportional to stimulus contrast (Methods). Therefore, V1 input gain and stimulus intensity are mathematically equivalent because they enter the dynamics only through their product (β<sub>1</sub> is scalar). This equivalence would not generally hold for spatially or feature-selective gain modulation, where attention can differentially modulate subsets (β<sub>1</sub> is vector) of neurons relative to the normalization pool (Reynolds & Heeger, 2009).

      (13) L375: There seems to be a lot of emphasis on modulation of the feedback gain, but related to L214, I wonder why there has been no manipulation of the feedforward gain, β<sub>2</sub>, which might be equally important in influencing the communication subspace dimensionality and in modulating the oscillatory dynamics. In terms of experimental predictions, the two might be very different, so why consider only one and ignore the other? See also statement at L388. To attribute the effect to top-down feedback, one should prove that bottom-up modulation does not produce the same effect.

      We thank the reviewer for this comment. We agree with the methodological point in the final sentence, and have acted on it. β<sub>2</sub> is now varied across the same analyses as γ<sub>1</sub> and β<sub>1</sub> (new SI Fig. S8; outcomes listed in our response to Weakness 4 above). Bottom-up modulation does not produce the same effect: increasing β<sub>2</sub> enhances inter-areal communication, as feedback gain does, but leaves within-area communication unchanged (feedback gain reduces it), leaves V1 responses unchanged, produces no low-contrast alpha or beta peaks, and reduces rather than increases the amplitude of the gamma peak. The passage at L375 (Results, “Communication subspaces”) now reports that increasing β<sub>2</sub> enhances inter-areal communication while leaving within-area communication approximately unchanged, with a substantially smaller effect than feedback gain (SI Fig. S8r); the readouts that distinguish the two gains are described in the Discussion (“Experimental predictions of the model”).

      (14) Figure 4: See comment for Figure 2.

      As for Fig. 2, we have retained the palette; see our response to item (11). The contrast values are given in the legend, the luminance ordering is monotonic in contrast, and the same palette is used across Figs. 2 and 4 and the SI.

      (15) L440: I think here it would be more honest to say that the two measures, of coherence and inter-areal communication, are not independent. If two signals are highly correlated at a certain frequency, then the prediction power will also peak for that same frequency. Or would it be possible to have conditions where it would not be the case, showing that the two measures are in fact independent?

      We thank the reviewer for this comment. We agree, and now state the dependence explicitly. The passage at L440 (Results, “Frequency decomposition of communication subspaces”), the Discussion (“Unified view of inter-areal communication”) and the Methods (“Interpretation of the results”) now state that coherence (Eq. 7) and frequency-resolved prediction performance (Eq. 22) are functionals of the same cross-spectral density matrix, so that the coincidence of their peaks is a mathematical consequence rather than an independent empirical confirmation. The claim retained is that coherence, prediction performance and the reduction in dimensionality are all generated by normalization; removing it eliminates all three (SI Fig. S4e–h).

      (16) L446: This paragraph mentions dimensionality, but only the following paragraph defines it.

      We thank the reviewer for this comment. We agree, and have moved the definition (the number of source dimensions required to reach the full-rank prediction performance, dictated by the rank of ) so that it precedes the first use of “dimensionality” (Results, “Frequency decomposition of communication subspaces”); the sentence that previously followed has been removed.

      (17) L485: See comment for L375.

      We address this together with item (13) and the corresponding point of the public review (Weakness 4). We have added a statement regarding the V2 input gain at the end of the section “Dynamic modulation of functional connectivity through feedback” (Results), and the conclusion of that section now describes the three-area result as a demonstration that differential feedback strength can control functional connectivity.

      (18) L575: I find this part a bit too vague. Within the scope of the paper, it is not clear what the network is “processing” and what kind of “balancing” it performs.

      We thank the reviewer for this comment. In this passage, “processing” refers to the computation performed by the principal cells: each cell sums its gain-scaled input, recurrent and feedback drives (Eq. 1a). “Balancing” refers to how these drives are combined: the recurrent gain control adjusts them so that the steady-state responses follow the normalization equation (Eq. 2), exactly or approximately depending on the recurrent weights. This is the mechanistic contrast with predictive coding: predictive coding matches top-down predictions against feedforward signals so as to minimize the prediction error, whereas hierarchical ORGaNICs balances the input, recurrent and feedback drives so as to maintain normalization.

      (19) L583: Similarly to above, I find these lines very confusing. In the context of this paper, there is no notion of “predictable stimulus”, so I find this part very confusing. Also, the model always produces sustained activity by construction, since it has stable steady-state solutions across a wide range of input patterns.

      We thank the reviewer for this comment. The passage refers to a limitation of the predictive coding framework. A constant, continuously presented stimulus is fully predictable, so in predictive coding the forward-propagated activity, which represents the prediction error, should be explained away and decay toward zero; cortical neurons instead maintain sustained responses to constant stimuli, barring adaptation (Burns, Xing & Shapley, 2010). We agree that our model produces sustained responses by construction, because it has a stable fixed point for a wide range of inputs; this behaviour is closer to the observed physiology than the explaining-away account.

      (20) L601, 602: I don’t think that not producing mathematically exact normalization is a significant, critical limitation in a model. We can be pretty confident that neural circuits are not, in fact, producing mathematically exact normalization. Or, to say it more constructively, simpler models that produce approximate normalization might actually be closer to the biological reality.

      We thank the reviewer for this comment. We agree, and have rewritten the passage (Discussion, “Normalization”). It no longer presents approximate normalization as a critical limitation of prior circuit models; it instead states how the present circuit differs: the normalization equation, with an arbitrary normalization pool, is a fixed point of the recurrent dynamics; the dynamics remain stable even with strong recurrent connections; and the fixed point and the linearization about it yield the power spectra, coherence, and communication subspaces in closed form.

      (21) L653: this line states that feedback is essential for network stability. But the paragraph seems to refer to top-down feedback drive, which should not be necessary for dynamical stability in the model.

      We thank the reviewer for this comment. The line refers to the feedback drive onto the inhibitory modulator cells (a), which contributes to the local normalization signal; it is this feedback-mediated inhibition, not the top-down drive to the principal cells, that is essential for stability. We have clarified the sentence accordingly (Discussion, “Role of feedback”).

      (22) L661: I think this statement is misleading and this part should be stated more cautiously. Although plausible in general, I don’t see these results anywhere in the paper. It would require a more functional connotation of the model, which now has a very homogeneous ring structure.

      We thank the reviewer for this comment. We agree, and have stated the claim more cautiously (Discussion, “Role of feedback”): the passage now describes the generative-model regime as a hypothesis (“the network is hypothesized to behave like generative models...”) rather than as a property demonstrated by the present results.

      (23) L715, L719: I feel confused by the contrast between spatially global feature-based attention and spatially-selective attention.

      We thank the reviewer for this comment. The two forms of attention differ in the domain over which neurons are selected for gain modulation. Feature-based attention is spatially global: attending to a feature boosts the neurons selective for that feature across the entire visual field, regardless of retinotopic location (Saenz, Buracas & Boynton, 2002). Spatially selective attention instead boosts only the neurons whose receptive fields overlap the attended location, regardless of their feature preference. Both are gain modulations that can be implemented in the model through the input gain: applied as a vector rather than a scalar, β<sub>1</sub> raises the gain of a selected subset of neurons relative to the normalization pool (Reynolds & Heeger, 2009), as noted in our response to item (12). On the ring, a β<sub>1</sub> profile over preferred orientation implements feature-selective gain; implementing spatially selective attention in the same way would require adding a spatial (retinotopic) dimension over which β<sub>1</sub> varies, as now noted in the Discussion (“Attention and functional connectivity”). The three-area routing result corresponds to the spatially global case, in which boosting an entire feature-selective area increases its feedback to V1 at all locations.

      (24) L729, L730: Here it is important to define exogenous and endogenous attention. If they are defined by the pathways on which they act, then the reasoning becomes circular.

      We thank the reviewer for this comment. We agree, and have defined both terms behaviourally at first use, independently of the model (Discussion, “Attention and functional connectivity”): exogenous attention as the fast, involuntary orienting driven by a salient stimulus, and endogenous attention as the slower, voluntary, goal-directed deployment of attention. The mapping onto input gain and feedback gain, respectively, is then stated as a testable hypothesis rather than as a definition, falsifiable through the divergent spectral signatures of the two gains.

      (25) Figure 7: I suggest changing the color map into a “diverging” color map centered at zero, so that negative and positive values appear visually distinct and zero has a neutral color. For example, the “seismic” or “PuOr” color maps in matplotlib would be appropriate.

      We thank the reviewer for this suggestion. We agree, and have revised Fig. 7 accordingly. It now uses the PuOr colour map, centred at zero with a shared colour bar, so that positive and negative weights in the tuning-curve, recurrent and feedback matrices are visually distinct and zero is neutral.

      References cited in this letter

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    1. Author response:

      The following is the authors’ response to the original reviews.

      We were appreciative of the quality of the work presented in this manuscript and had some points that the authors could address in a revision:

      (1) The pallium interpretation: The data clearly show that pallial activity encodes chemosensory context and predicts upcoming S-T turns. At the same time, in the absence of perturbations, one cannot conclude that the pallium is necessary for transforming chemosensory input into motor output. To align the text with the current evidence, we recommend reframing the pallium's role as correlative/predictive (and avoiding terms like "key region," "hub," or "transformation" that imply causality). The authors could also add a brief limitations note on causality.

      (2) Statistics: There were a few points related to the statistics that needed clarification/tightening. We felt that the animal-level replication was limited and with mixed ages, and the data related to events/neurons were treated as independent observations. It was unclear if the hierarchical structure of the data (events/neurons in different fish) was taken into account, how age differences were handled, and what the exclusion criteria were for 'robustly behaving fish'. We recommend reanalysing the data with fish as the unit of inference (or use clustered/mixed models with fish-level random effects), reporting effect sizes with CIs, and clarifying age (5-6 dpf) handling and any exclusion criteria.

      (3) Figure clarity/data reduction: Some of the figures were crowded, obscuring the main message. To make the main effects easy to see, we recommend that the authors aggregate across doses and move detailed, condition-by-condition results to tables/SI. We also recommend that they include per-fish distributions where helpful, standardize axes/legends, and define onset metrics in captions.

      Summary of Revision

      We thank the reviewers and editors for their overall positive evaluations and encouraging remarks, as well as for their suggestions and constructive criticisms. We have performed additional experiments and analyses, and have substantially revised the manuscript based on the reviewers’ comments and in places where we felt additional clarity was needed. Major additions and changes include:

      - We reframed the pallium’s role as correlative/predictive and avoided all the terms (e.g., “key region”, “hub”, or “transformation”) that imply causality throughout the manuscript. In Discussion, we added a brief limitation note on causality, and incorporated five recent independent OB/pallium-related studies to better contextualize our neuronal findings.

      - To improve animal-level replication, we performed new partially immobilized behavioral experiments in the microfluidic chip (now n = 8 larvae in total; i.e., increased from 5), and reanalyzed the data using linear mixed-effects models with larva as a random intercept (Figures 2, 3, Supplementary Figures 3, 5). For the presentation, IQRs are used to visualize the spontaneous structure of S-T events (Figures 2d, e, i, j, Supplementary Figures 3e, f), the freely swimming plots (Supplementary Figure 4), and chemical-elicited bout kinematic changes (Figures 3e, f, Supplementary Figures 5g, h), whereas 95% CIs are used to visualize time-dependent chemical-elicited rate changes across larvae (Figures 3b–d) and in regression plots (Figures 3g, h). We also included per-larva distributions (Figures 1e, 2b, c, f, 3b–f, Supplementary Figures 3b, c, 5a–h). These additions strengthen the behavioral findings and their presentation. For neuronal analyses (Figures 4, 5, Supplementary Figures 7–11), statistical tests were performed at the individual-larva level, as explicitly clarified in the corresponding figure legends and Methods.

      - We rearranged the figures to highlight findings, simplified analyses and their presentation (Figures 1–3, Supplementary Figures 1, 3–6). We now present the most representative concentration for the valence determination assay in Figure 1c, while leaving the rest in Supplementary Figure 1c. We added a new PCA analysis to present the valence-dependent relationship of temporal proximity and turn magnitude in chemical-evoked S-T events (Figures 3g, h, Supplementary Figure 6). We also added within-trial circular saccade-time shuffle analyses to test whether increased aversive saccade occurrence (Figure 3b) could explain the structured temporal and directional properties of chemical-evoked S-T events (Supplementary Figures 5i, j). In addition, we clarified the handling of larval age and explicitly stated in Methods that there were no additional exclusion criteria (page 19, paragraph 2). We also defined onset metrics and referenced the illustrative schematic (Figure 2a) in captions (Figure 5, Supplementary Figure 10).

      Public review:

      Reviewer #1 (Public review):

      Summary:

      This study was designed to manipulate and analyze the effects of chemosensory cues on visuomotor control. They approach this by analyzing how eye-body coordination and brain-wide activity are altered with specific chemosensation in larval zebrafish. After analyzing the dynamics of coupled saccade-tail coordination sequences - directionally linked and typically coupled to body turns - the authors investigated the effects of sensory cues shown to be either aversive or appetitive on freely swimming zebrafish on the eye-body coordination. Aversive chemicals lead to an increase in saccade-tail sequences in both number and dynamics, seemingly facilitating behaviors like escape. Brain-wide imaging led the authors to neurons in the telencephalic pallium as a target to study eye-body coordination. Pallium neuron activity correlated with both aversive chemicals and coupled saccade-tail movements.

      Recommendations for improvement are minimal. So much of the data is ultimately tabular, and the figures are an impenetrable wall of datapoints. 1c is an excellent example: three concentrations are presented, but it's rare for the three averages to trend appropriately. The key point, which is that aversive odors are repulsive and attractive odors (sometimes) attractive just gets lost in showing the three concentrations individually; it also makes direct comparisons impossible. There are similar challenges abound in the violin plots in 4e-4h, the error bars on the "fits" in 4i-4m, and so on. We recommend selecting an illustrative subset of data to present to permit interpretation and putting the rest in a supplemental table. (Presenting) less is more (effective).

      We are very grateful to the reviewer for their positive assessment and important comments. We have revised the figures to improve clarity and interpretability in line with this suggestion. Specifically, for the valence determination assay, we now present only the most representative one in Figure 1c, while the remaining concentrations are moved to Supplementary Figure 1c. In addition, the new PCA analysis reduced multiple regression plots into summary plots to show the valence-dependent relationship of temporal proximity and turn magnitude in chemical-evoked S-T events (Figures 3g, h, Supplementary Figure 6). For improved presentations, we selected a subset of the most important panels for the behavioral findings (Figures 2, 3, Supplementary Figures 3–6), added the per-larva data points and larva-level summary statistics (Figures 1e, 2b, c, f, 3b–f, Supplementary Figures 3b, c, 5a–h), and adjusted the optical transparency of the error bands (Figures 3b–h, Supplementary Figures 5g, h).

      Reviewer #2 (Public review):

      Summary:

      The manuscript by Sy SKH. et al. on pallium encoded chemosensory impact of eye-body coordination describes how the valence of chemosensory stimuli can affect the coordination of eye saccades with tail flips. They show that aversive valence stimuli can increase both the strength and frequency of tail flips through a pallium-mediated circuit.

      Overall, the manuscript is well-written and easy to follow, although the figures are quite dense, the methodology is mostly sound, and the improvement to the fish on chips system is very interesting. The methods description is thorough and welcome, making the experiments clear. The limited number of animals, and the spread between 5 and 6dpf is a concern as most of the statistics seem to have been done on the individual events, and not the number of biological samples.

      The initial behavioural experiments are very promising. However, the conclusions surrounding the role of the pallium are a lot more speculative and not supported by the results.

      We thank the reviewer for their positive assessment of our manuscript, including the clarity of the writing, methodological description, improvements to the Fish‑on‑Chips system, and very promising behavioral experiments. We also appreciate the important concerns raised about the limited number of animals and the spread between 5 and 6 dpf, as well as the strength of our original phrasing regarding the role of the pallium. As described in the above Summary of Revision, we have substantially addressed these points through additional behavioral experiments and refined statistical analyses, a more cautious framing of our neuronal findings throughout the manuscript and contextualization of our findings in Discussion, and clarifications in the revised manuscript, including the explicit specification of age and statistics in Methods (page 19, paragraph 2). In addition, we now clarify that 5 and 6 dpf larvae were intermixed across all stimulus conditions in a within‑subject design, so that age is not confounded with chemosensory valence and condition effects are estimated within animals rather than across different groups of larvae (Methods, page 18, paragraph 2).

      Comments:

      (1) The fish on chips 2.0 methods show a lot of promise for future studies of chemosensory stimuli, combined with whole-brain imaging. This will provide new avenues of research for zebrafish neuroscientists.

      We thank the reviewer for the positive assessment of the Fish‑on‑Chips 2.0 methods and their potential for future chemosensory whole‑brain imaging studies.

      (2) Chemosensory cues would have a very different timing than visual cues; timing is very important for multisensory integration. How do the authors suggest those are integrated? How would they differentiate between an integration of various cues or a different arousal state, as they describe in the introduction?

      We thank the reviewer for these important comments. In Discussion, we now explicitly consider how visual and chemosensory cues with different temporal dynamics might be integrated. We propose that visual cues may provide rapid guidance for individual movements, whereas chemosensory input may bias the selection and kinematic expression of broader orientation and gaze-shift strategies, including updating gaze after larger reorientations (page 10, paragraph 4).

      We also clarify the alternative explanation of altered arousal. The chemosensory effects were largely confined to the 10-s stimulus window and returned to baseline thereafter, which is more consistent with a rapid cue-locked adjustment rather than a sustained global state change. However, this temporal profile does not exclude a transient arousal-related contribution. We therefore state that our data establish an association between chemosensory context and enhanced eye–body coordination, while distinguishing a specific integration mechanism from transient arousal will require further experiments (page 11, paragraph 1).

      (3) Studies have looked at chemosensation in Drosophila, including multisensory integration, which should be discussed by the authors (see the work of Mark Frye, amongst others).

      We thank the reviewer for pointing out the importance of prior work on chemosensation and multisensory integration in Drosophila. In Discussion, we now relate our findings to studies showing that visual and olfactory cues jointly shape steering and odor‑tracking in flies, including work from the Frye lab, and highlight that reorientation and active visual sampling are common multisensory strategies in small animals (page 10, paragraph 4).

      (4) In the brain imaging methods, there is a mention of robustly behaving larvae. Does that mean that an exclusion criterion was used to select only 5 larvae? If so, this should be stated clearly. The authors also do not mention how they avoid the switch to a passive state that one of the coauthors has observed in closed closed-loop setup. The authors should comment on this point.

      We thank the reviewer for this clarification request. The mention of “robustly behaving” larvae was not intended to introduce any additional exclusion criterion beyond the leveling requirement already described in Methods. In the revised manuscript, we now state explicitly that there were no further exclusions of animals beyond this positioning criterion, so that the basis for the final sample size is clear (page 19, paragraph 2). We also clarify in Methods that appetitive and aversive cues were presented in brief (10-s), balanced, pseudo‑random trials, rather than as a continuous aversive exposure (page 18, paragraph 2).

      (5) Were the statistics in Figure 2 done with an n of 5, or do they assume that each tail flip and saccade is an independent event? I would imagine the latter would have inflated p-values and should be avoided.

      We thank the reviewer for highlighting this important issue. In the original analyses for Figures 2, 3, Supplementary Figures 3, 5, individual tail flips and saccades were treated as independent observations, which could underestimate variability across larvae. In the revised manuscript, we have addressed this in two ways. First, we collected data from three additional larvae and now base our analyses on eight larvae in total. Second, we re‑analyzed these data using linear mixed‑effects models including larva as a random intercept, so that multiple events from the same larva are explicitly modeled as non‑independent. The mixed‑effects analyses yields qualitatively similar conclusions to our original analysis, while avoiding inflated p‑values due to event‑level pseudoreplication. We have updated Methods and legends (Figures 2, 3, Supplementary Figures 3, 5) to describe this model specification and to clarify that larva identity was included as a random effect to account for the non-independence of multiple behavioral events recorded from the same larva.

      (7) Page 7: Why do the authors think that the cumulative effect of these minor differences could lead to very different behavioural goals? Especially when comparing to actual startle responses, which are extremely strong and stereotypical. How do their observations compare to the thermosensory navigation of larval zebrafish observed by Martin Haesemeyer, for example, or the work of the RoLi lab?

      We thank the reviewer for this important point. While the observed changes in individual motor parameters are modest compared to the large and stereotyped responses seen in startle behaviors, our interpretation is based on the principle that larval zebrafish navigation is governed by the accumulation of small, probabilistic changes in bout statistics rather than single, large motor events. This has been well demonstrated in thermosensory navigation, where subtle biases are sufficient to drive reliable temperature preference over time (Haesemeyer et al.). We have now clarified this comparison in the manuscript (page 7, paragraph 2) to better present how the cumulative effects of these small changes can give rise to distinct behavioral outcomes such as approach or avoidance.

      (8) Page 8: Figure 5, I am confused by the y-axis of g, in e and f, the values are capped at 2, whereas in g they go up to 6, with apparently a number of cells whose preference is out of the y-axis limit (especially in Q2). Having the number of cells in each quadrant would also help to assess if indeed there is some preference in the pallium towards Q1.

      We thank the reviewer for highlighting this potential source of confusion regarding Figure 4g. The difference in the y-axis caps between Figures 4f, g arises because these panels display related but distinct quantities. Figure 4f shows regional mean valence preference, averaged across ROIs and across larvae, which lies within a relatively narrow range and is therefore naturally confined to approximately −2 to 2. In contrast, Figure 4g plots the valence preference of individual motor- and valence‑encoding ROIs, which spans a broader dynamic range; for this reason, the y-axis in Figure 4g extends up to ±6. We have also made this distinction more explicit in the Figure 4 legend.

      To address the concern that a substantial number of cells might lie outside the visible axis limits in Figure 4g, we have now quantified the fraction of ROIs whose motor or valence preference values exceed the plotted range. We find that only 0.47% of ROIs have values beyond the chosen axis limits on either axis. These ROIs are plotted at the respective axis limits (i.e. values are clipped to the shown range) and therefore remain visible in the scatter plot. Thus, the plot is representative of virtually all sensorimotor‑tuned neurons included in this analysis.

      In addition, in line with the reviewer’s suggestion, we have clarified the distribution of cells across quadrants by modifying Figure 4g. Specifically, we have added a lower subpanel that shows a grouped bar plot of the proportion of ROIs in each sensorimotor quadrant (I–IV) for pallial versus non‑pallial brain regions. To make the underlying numbers explicit, the corresponding absolute ROI counts for pallial and non‑pallial regions in each quadrant are now reported in the Figure 4 legend. These additions demonstrate that pallial ROIs are strongly enriched in quadrant I relative to other quadrants and to non‑pallial regions, and they directly address the reviewer’s request for the number of cells in each quadrant.

      (9) Figure 6: How is the onset of neuronal activity determined compared to the motor stimulus? Looking at Supplementary Figure 8, it is quite unclear how the pallium is different from the OB or subpallium. The label of onset delay is also confusing in this figure.

      In our analysis, neuronal activity is aligned to tail flip onset for each S-T or T event (dotted vertical lines in neuronal traces in Figures 5a, b, Supplementary Figures 8a, b, 9–11). At each of the two time points preceding the motor event, we compare the fluorescence signal of the motor‑encoding ROIs to their pre‑event baseline; activity exceeding baseline by ≥ 2.5 S.D. is considered significantly elevated (Z‑test with Benjamini–Hochberg correction; see Methods and Figure 5 legend). In Supplementary Figure 9, pallial motor‑encoding neurons exhibit earlier statistically significant elevations relative to tail flip onset during aversive, cue‑associated S-T events, whereas OB and subpallial neurons primarily encode chemosensory input and valence and do not show the same pattern of early significant activation.

      Additionally, we have clarified in the legends of Figure 5 and Supplementary Figure 10 that ‘saccade–tail flip onset delay’ is defined as the time difference between tail flip onset and saccade onset within an S-T event (tail flip onset minus saccade onset), and we indicate how this metric is used to group “more-coupled” versus “less-coupled” S-T events. We note that this “saccade–tail flip onset delay” captures how tightly the eye and body components of S-T events are temporally coupled, and thus serves as a quantitative link between motor coordination (Figures 3g, h, Supplementary Figure 6) and the pallial premotor activation observed during aversive cues (Figure 5a, Supplementary Figure 9).

      We hope these clarifications resolve the ambiguity the reviewer noted.

      (10) Page 9: I do not think that the small differences observed in the pallium are as clear-cut as the authors make them out to be, or that they provide such strong evidence of their importance. As there are no interventions showing any causality in the presence of these pallium responses and the sensorimotor responses, these could represent different arousal states rather than any integration of sensory information.

      We thank the reviewer for this thoughtful comment. We agree that, without targeted perturbations, our pallium signals cannot be interpreted as causal for the sensorimotor responses, and we have accordingly reframed them throughout the manuscript (in Title, Abstract, Results and Discussion) as correlative/predictive rather than causal, with an explicit limitation note in Discussion. In addition, we added five related recent studies in Discussion to contextualize our pallial findings. While the pallial differences are moderate in magnitude, they are quantified at the larval level and consistently show a relative bias toward S-T events together with aversive valence, distinguishing the pallium from other regions. Please see also the response to comment 2 regarding the altered arousal point.

      Reviewer #3 (Public review):

      The manuscript investigates the coupling of saccadic eye movements (S) with directed tail flips (T). The remarkable discovery is that tail flips that are preceded by a conjugate sacced (S-T) can be credibly classified as specific "volitional" turns that are distinguished from the standard tail movements that seem to be more of a spontaneous and "impulsive" nature.

      They show that 'turning intent', as indicated by a small increase in S, is elevated by aversive odors, while 'gliding intent', as indicated by a decrease in S and an increase in undulation cycles, is elevated by appetitive odors.

      This is a very important finding, which is backed up by a thorough behavioral analysis, and the identification of neural populations in the pallium and sub-pallium that clearly distinguish between these kinds of turns is very promising. Here they identify neuronal populations that are preferentially active during - and predictive of - coupled (S-T) versus isolated (T) tail flips.

      Especially the fact that S-T turns (but not T turns) can be predicted already by pre-event, ramping, pallial activity is intriguing.

      The authors then go on and demonstrate that the frequency of (S-T) turns is modulated in fish exposed to appetitive or aversive odors.

      Specifically, they quantify the aversiveness and appetitive-ness of several odors in a free swimming assay. They select a couple of these odors based on their valence, and they demonstrate that these odors induce moderate modulation in the frequency of eye saccades (S) and tail flips (T) and (S-T) turns.

      The study is rigorous and thorough, and the findings are informative and novel.

      In important controls, they confirm that brain-wide imaging can distinguish between appetitive and aversive contexts, and they show that pallial activation by aversive odors is consistent with neural activity in the rhombencephalon that correlates with turning activity, whereas sub-pallial activation by appetitive odors correlates with rhombencephalic activity related to gliding.

      Overall, this manuscript is very good.

      We are very grateful to the reviewer for their positive and thoughtful assessment of our work. We are pleased that the distinction between saccade‑coupled (S‑T) turns and independent tail flips, their modulation by appetitive versus aversive odors, and the identification of pallial populations predictive of these events are viewed as rigorous, informative, and novel.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      Full disclosure: We reviewed the manuscript previously for Cell Reports, and we're happy to see that it is much improved. As such, our comments are pretty minimal.

      We thank the reviewer for revisiting the manuscript and for their positive assessment of the revisions. In the present revision, we also performed within-trial saccade-time shuffle analyses to directly examine whether the increased occurrence of aversive saccades could account for the temporal and directional organization of S-T events (Supplementary Figures 5i, j). These analyses showed that altered saccade occurrence alone cannot account for this organization.

      Reviewer #2 (Recommendations for the authors):

      (1) The introduction would benefit from more discussion of the existing disruption of coordination beyond Parkinson. Especially in terms of the circuits involved, as these have been well-studied, and it would provide a better understanding of the system as studied in the manuscript.

      We thank the reviewer for this suggestion. In Introduction, we now place Parkinson’s disease within the broader context of movement disorders that disrupt eye–body coordination and expand the circuit‑level discussion accordingly, emphasizing the shared involvement of cortical eye fields, superior colliculus, basal ganglia, cerebellum, and brainstem locomotor centers (page 2, paragraph 2).

      (2) "For example, a sudden surge of noxious chemical signals can trigger fleeing" - in what model and condition, what type of escape? There are a number of options to discuss here.

      We thank the reviewer for this helpful suggestion. In response, we have revised the sentence to include a concrete and well-characterized example from teleost fish (page 3, paragraph 1). Specifically, we now refer to the response to injury-released alarm substances (“Schreckstoff”), which reliably elicit rapid escape bouts. This provides a clear example of the model system, stimulus condition (alarm cue), and behavioral output (escape locomotion).

      (3) The introduction mostly mentions the methodological advantages of zebrafish, but the authors should discuss the relevance of the model to the research question. Especially with regard to the differences in chemosensory spread underwater and in the air.

      We thank the reviewer for this suggestion. We have revised the Introduction to better highlight the biological relevance of zebrafish beyond their technical advantages, emphasizing that larval zebrafish naturally use waterborne chemosensory cues to guide locomotion (page 3, paragraph 2). We also address differences between chemosensory signal propagation in water and air, noting that despite these physical differences, animals in both environments must integrate chemical cues with other sensory inputs to select appropriate behavioral responses. We believe this revision clarifies the relevance of the model to our research question.

      (4) The GitHub is missing some of the registration code used for calcium imaging. It would be useful to make sure that all the code mentioned in the manuscript is shared.

      We thank the reviewer for this thoughtful comment and for drawing attention to code availability. The calcium-imaging processing pipeline in this study used established, publicly available tools, including NoRMCorre for motion correction, as cited and described in Methods. In addition, we used custom MATLAB scripts to implement and link the affine and non-rigid registration workflow for aligning anatomical stacks to the Z-Brain Atlas. These custom scripts, together with the analysis code, have now been uploaded to the GitHub repository.

      (5) Figure 4: In subpanel c, it seems that the blank stimulus has a similar, but opposed, effect to aversive stimuli. Would it be possible to see the full 30s pre-stimulus to judge how variable the baseline is?

      We thank the reviewer for this helpful comment. In the analyses, the first 10s of each behavioral recording are discarded to avoid transient responses to the onset of light‑sheet illumination, and we normalize the time courses to the mean pre‑stimulus activity in the 10s immediately preceding stimulus onset. In the extended 40s plot provided in Figure 3b, we additionally display 10s of earlier baseline and, for visualization, normalize the traces to the mean activity in these first two 5s bins, so that baseline fluctuations across blank, appetitive, and aversive conditions can be directly compared. All conditions show modest pre-stimulus fluctuations, but the largest and most sustained increase is observed for the aversive condition and is confined to the stimulus window, whereas blank and appetitive traces remain comparatively close to baseline throughout. Thus, although some baseline variability is present, the strong aversive effect remains stimulus-locked and is not explained by pre-stimulus drift in the blank condition.

      Because this extended plot was used only to assess baseline variability in response to the reviewer’s question and does not alter the quantitative analyses or figure panels in the manuscript, we have included it in the rebuttal rather than in the revised manuscript.

      (6) Figure 5: I assume the legend is flipped between subpanels a and b? Subpanel d is used to show that the pallium has a preference for S-T events, but the result is not convincing; the motor preference is still below zero, very similar to PO, pTec or even Rh3. Furthermore, I assume the statistics have been done on all the neurons across the 5 fish, not treating them as individual samples.

      We thank the reviewer for their important comments. The legend on Figure 4 has been corrected so that the labels for subpanels a and b match the plotted data. Although the pallial motor preference is below zero, indicating a net bias toward independent tail flips, we note that the pallium is nonetheless the least T‑preferring region and shows the strongest relative preference for S-T events when motor preference is compared across all brain regions. We have clarified this relative, contrast-based interpretation in the revised manuscript. Importantly, motor‑preference statistics are computed at the individual-larva level (n = 5), averaging neurons within each region for each larva and then testing across larvae rather than treating individual neurons as independent samples. This approach is now described more clearly in Methods, and the Figure 4 legend.

      (6) Supplementary Figure 7: What are the ROI numbers for the different graphs in a and b? It is difficult to judge if the "significant" increase in activation level is due to a low level of neurons or a genuine biological result.

      We thank the reviewer for this helpful comment. To address the concern, we have revised the legend of Supplementary Figure 8 to clarify that mean ± S.E.M. values are computed across larvae using per‑larva averages and to report the ROI counts for each preference range. These changes make clear that each curve is supported by on the order of 10<sup>2</sup>–10<sup>3</sup> ROIs pooled across the five larvae, rather than by a very small number of neurons.

      Reviewer #3 (Recommendations for the authors):

      (1) Shouldn't the ipsilateral tendency relative to each preceding flip across a series of tail flips decay to chance over repeated events? In Figure 2h, the teal curve appears to be flat over twenty seconds. Isn't the laterality index calculated relative to the event at n=0? Are the individual fish laterally biased (for spontaneous flips) over 20 bouts?

      We thank the reviewer for this insightful comment. In Figure 2h, the laterality index is computed relative to the tail flip at n = 0, and the sustained ipsilateral tendency (please see also Supplementary Figure 3c) over subsequent bouts reflects that spontaneous locomotion in larval zebrafish is not a memoryless random walk. To clarify this point, we now complement the citation on history‑dependent chaining of turns with an additional reference highlighting stable individual left–right motor asymmetries in larval zebrafish (page 5, paragraph 4). This added citation provides stronger context for our observation that tail flips can remain biased ipsilaterally to the initial event over the bout window we analyze.

      (2) Do zebrafish initiate a 'turn bout' by a preceding saccade also in free swimming conditions? Are there any data available with sufficient resolution to extract saccades in freely swimming larvae?

      We thank the reviewer for this important question. In the prior free‑swimming assay, we used a large field of view (60 mm × 30 mm) at approximately 0.1 mm per pixel to track multiple larvae and quantify their position and heading. Given this combination of field of view and spatial sampling, the larval eyes occupy only a few pixels, and the small angular displacements associated with saccades are very challenging to resolve with sufficient precision. For this reason, we did not extract eye movements or define turn bouts based on preceding saccades in the free‑swimming condition, and instead focused our saccade analyses on the head‑fixed imaging setup, where magnification and resolution are optimized for quantifying eye rotations.

      We have added a brief note in Methods (page 22, paragraph 2) to clarify this limitation.

    1. Author response:

      The following is the authors’ response to the previous reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      The "multiple-demand" (MD) system is a well-known finding of human brain imaging and is thought to play a central role in cognitive control. To directly compare the MD system in humans and monkeys, Mione et al. used functional magnetic resonance imaging to measure whole brain activation in a multi-step saccadic maze task. In humans, the authors found a distributed pattern of brain activity close match to the canonical MD network and extending to adjacent regions of dorsal attention and other networks. While there was good correspondence between monkey and human data, differences were also notable in lateral frontal cortex, dorsal parietal cortex, and sensorimotor cortex.

      Strengths:

      Though previous data hint at a corresponding network in the macaque, there has been no direct comparison to human data. This study provides a direct cross-species comparison with whole-brain data of fMRI, and the findings suggest an extended and strongly interconnected brain network recruited by increased cognitive challenge.

      Weaknesses:

      In previous human imaging, the MD system is defined by overlapping activation for many kinds of cognitive demand. In the present work, however, the authors used just a single task. Although there is some overlap between putative monkey MD network and canonical MD network identified in human imaging, it should be cautious to link current findings to MD system based on limited task events.

      We agree that present conclusions are limited by data from a single task. As we note, however, our human data show that this contrast works well for identifying the usual components of the MD network, suggesting it is a suitable candidate for use in the monkey.

      Reviewer #2 (Public review):

      Summary:

      Mione et al. aim to resolve a long-standing question in comparative neuroscience: whether the macaque brain contains a functional analogue to the distributed human multiple-demand (MD) network. To address this, the authors employ a direct cross-species fMRI comparison using a multi-step saccadic maze task in humans and a simplified two-step version in macaques. By contrasting goal-directed navigation against a control condition that requires similar motor responses but no strategic planning, the study isolates the neural signatures of cognitive control across species.

      Strengths:

      The most compelling aspect of this work is its methodological alignment. Previous attempts to compare these systems often relied on comparisons of human BOLD signals and macaque single-unit recordings. By running parallel fMRI protocols, the authors establish a shared measurement basis that allows for a more direct comparison. The resulting activation maps demonstrate conserved network topology in dorsolateral and dorsomedial frontal cortex and insula.

      Weaknesses:

      However, there is concerning inter-individual variability in the macaque data, along with a notable design asymmetry between the human and monkey tasks. In the human experiment, 2-, 4-, and 6-step trials were mixed within the same blocks, whereas macaques performed only 2-step problems. This design difference likely places human participants in a state of sustained proactive cognitive control (Braver, 2012), as they must remain prepared for more demanding trials at any moment. This elevated baseline arousal may potentially inflate MD network activation even during the simpler 2-step trials in humans, making direct comparisons with the macaque data difficult.

      The authors acknowledge this concern and note that similarities between species survive despite this procedural difference. However, their own individual-level data raise doubts about how robust these "similarities" really are. A defining feature of the MD system is consistent recruitment across individuals performing the same task. In this study, however, the two monkeys show markedly different activation maps in parietal cortex. The conjunction map (Supplementary Figure 6) does not support the claim that lateral and medial parietal regions are commonly activated across both animals at any meaningful statistical threshold, even when using a permissive threshold of |t| > 1.5, corresponding to approximately p ≈ 0.13 - 0.14 (two-tailed).

      This suggests that the group-level parietal activations are largely driven by a single animal, raising questions about whether these regions can reliably be considered as part of the monkey MD network. Notably, in Premereur et al. (2018), the only other direct macaque fMRI study of a cognitively demanding task, their conjunction map between the two animals also failed to show common parietal activation during task switching. Taken together, these findings suggest that either the monkey MD network is not as similar to its human counterpart as claimed, or the monkey version of the maze task was simply not sufficiently challenging to fully engage parietal MD nodes.

      Because of the design asymmetry described above, it remains difficult to determine which of these possibilities is correct (a genuine species difference versus insufficient task demands in macaques). The authors' current claims treat the group-level activations, which appear largely driven by one animal, as reliable evidence for homology, but without consistent individual-level support, such conclusions remain tentative.

      In summary, the authors demonstrate functional correspondence between human and macaque cognitive control networks in dorsolateral and dorsomedial frontal regions. However, assertions that this extends to lateral and medial parietal cortex are not consistently supported at the individual level. While the overall conclusions are plausible, they would be significantly strengthened by demonstrating consistent activation across both animals in all claimed MD regions, ideally with a properly thresholded conjunction map.

      These are all good points, and in the revision, we have placed greater emphasis on differences as well as similarities between animals. We have also pointed out the limitations of the conjunction map. In particular, two strong components of the human MD network (vlPFC and parietal cortex) are each seen in only one of the two animals. As we note, limited task difficulty, long training, and limited statistical power may all contribute to negative results. For these regions we agree that between-animal differences limit conclusions, though provisionally, results for single animals tell against genuine species differences.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      (1) Although the whole-brain data obtained by fMRI can provide a direct comparison between species, a single cognitive task might be insufficient to link the findings with MD system. A cognitively challenging task likely activates multiple regions of the MD system; however, it may also recruit some task-specific regions, which do not belong to the canonical MD network.

      Though this is a very reasonable concern, the results suggest little influence on the present findings. In the human, strong MD activation was accompanied by activation of the DA network, perhaps reflecting the spatial content of the task. In the monkey, however, there was little evidence of DA activation, likely reflecting limited statistical power.

      (2) Based on the current work, the title seems to be too general.

      For the above reason, we think the title is reasonable – acknowledging limitations of data from single animals (see below), the cortical and subcortical distribution of monkey activations indeed suggests correspondence to the human MD network.

      Reviewer #2 (Recommendations for the authors):

      (1) Please clearly state the statistical threshold used for your conjunction analysis in Supplementary Figure 6. The current display appears to rely on |t| > 0, which is not a meaningful criterion: it effectively includes any voxel with positive activation regardless of significance. Even at a more permissive but still unjustified threshold of t = 1.5 (corresponding to roughly p ≈ 0.13-0.14, two-tailed), lateral and posterior medial parietal regions do not appear in the conjunction map. Without a properly justified threshold, it is difficult to accept the claim that these regions are commonly activated across both animals.

      The threshold and limitations of the conjunction map are now described (p. 13), and differences between animals given stronger emphasis.

      (2) Given that lateral and medial parietal activations do not survive even a low uncorrected threshold in the conjunction analysis and are therefore largely driven by one animal at the individual level, I recommend explicitly acknowledging this limitation in the Discussion rather than treating these regions as reliable components of the macaque MD network. Alternatively, acquiring data from a third monkey would help determine whether this reflects limited statistical power or genuine inter-individual variability.

      We have reworded our conclusions concerning parietal activation throughout (beginning with Abstract), emphasising their dependence on data from a single animal.

      (3) The design asymmetry between humans and monkeys makes it difficult to interpret cross-species differences in activation. For parietal and ventral prefrontal regions specifically, the monkey version of the task may simply have been insufficiently demanding to fully engage these MD nodes, which might require higher cognitive load before they are reliably recruited. Alternatively, this could reflect a genuine species difference. I recommend discussing this possibility explicitly when interpreting missing or inconsistent activations in these regions.

      These possibilities are now considered in a new paragraph of the Discussion (p. 18).

      (4) Please specify exactly how Figure 7 was thresholded and state whether FDR correction was applied separately for cortical and subcortical analyses. The colorbar suggests t > 0 as a starting point, but large empty regions within the slices imply that some higher masking or threshold was applied.

      See revised figure legend.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      Naina Gour and colleagues provide a detailed observational study in which they demonstrate that MRGPRX4, a human G-protein coupled receptor (GPCR), is expressed exclusively in human melanomas and, when expressed in mouse melanocytes, drives the development of melanomas in mice. These findings provide evidence that MRGPRX4 has the properties of an oncogene, at least in certain cellular environments.

      Strengths:

      A strength of this work is the nice historical note in which overexpression of MAS1, a GPCR, led to classic studies of transformed fibroblasts in culture and tumors in nude mice. Cloning of MAS1 led to the identification of the MRGPR family of receptors, now known to be key players in neuroimmune and neurosensory phenomena. Here, the story comes full circle with a member of the MRGPR family being linked to a tumor, specifically melanoma. Perhaps the story is not entirely surprising given that the neural crest serves as a precursor for both nerves and melanocytes. But it is nice to see.

      Additional strengths include the vast array of tools and techniques employed, from public databases to engineered mice, to establish firmly that MRGPRX4 is expressed in melanomas, although not in every malignant cell.

      We thank the reviewer for the positive assessment of our work and for noting the arc back to the original MAS1 studies, which we agree makes for a satisfying full-circle story. We would add one nuance: while the shared neural crest origin of melanocytes and nociceptors offers a plausible explanation for why an MRGPR family member could be co-opted in melanoma, we were nonetheless surprised that this property is specific to MRGPRX4. When we tested the other MRGPRX family members, some of which are also known to be expressed in sensory neurons, using the same genetic strategy (MRGPRX1, MRGPRX2, MRGPRX3; Supplementary Fig. 2B), none induced melanoma, despite arising from the same family of receptors. This suggests the oncogenic property is not simply a generic consequence of neural crest ancestry, but reflects a biology specific to MRGPRX4 itself, which we find is one of the more intriguing open questions this work raises.

      Weaknesses:

      Given the power of the strengths of the data and story, the following comment is only sort of a weakness, as the topic is addressed while being saved for future studies. Specifically, what leads to the expression of MRGPRX4? The authors posit that it is an epigenetic phenomenon, look briefly at methylation, and rather than going down the proverbial rabbit hole of what comes first, have reasonably decided to punt.

      We agree with the reviewer that understanding the precise mechanisms through which MRGPRX4 gets activated during oncogenesis is important, and we had noted this as a limitation of current findings. As we mentioned in the discussion, we hypothesize that one or more environmental modulators - UV exposure, inflammatory cues, or an aging skin microenvironment could initiate the epigenetic reprogramming underlying this expression. This will require dedicated studies and is suited for future work.

      Another concern is that given what comes across as the initial observation of MRGPRX4 being expressed in melanoma, what do all of the additional studies add?

      The expression data in human melanoma are correlative and serve only as the entry point. The subsequent studies establish MRGPRX4 as a causal, druggable driver of melanoma: it is sufficient to induce 100% penetrant metastatic melanoma in vivo, required for melanoma proliferation and invasion, signals through ligand-independent basal PI3K-AKT/MAPK activity, and is pharmacologically targetable.

      For the non-cognoscenti, and to make the manuscript more accessible, the abbreviation NC/EMT, which is also inverted to EMT/NC, should be spelled out periodically as neural crest/epithelial-mesenchymal transition.

      This is corrected in the revised version.

      Please explain how this study came about. Was it a result of someone deciding to look at expression in the GTEx project and compare it to a tumor database?

      This was a serendipitous discovery. As MRGPRs can modulate immune cell function, we were driving expression of various human MRGPRX genes in immune lineages in mice. We noticed that mice overexpressing MRGPRX4 developed spontaneous melanoma-like growths on the ear and tail. Upon investigation, we found that while the Cre driver we had used is appropriate for immune cells, it is also expressed at low levels in melanocytes. We hypothesized that our initial "immune-knock-in" strategy likely resulted in low-level knock-in in mouse melanocytes, thereby allowing MRGPRX4 to directly drive melanocytic transformation. This led us to explore MRGPRX4 expression in human malignancies, where we found MRGPRX4 was highly expressed in melanoma. Next, to directly test our hypothesis that MRGPRX4 transforms melanocytes, we overexpressed MRGPRX4 using Tyrosinase-CreER, the standard Cre driver for melanocytes. This led to a fully penetrant spontaneous melanoma phenotype (Fig. 2).

      A comment could be made to explain that while NSG and normal mice were used, the former are immunocompromised, and drawing conclusions without specifying these differences is a weakness.

      This is a fair point, and we agree the distinction deserves clarification. The two mouse systems in this study serve different purposes and are not interchangeable. The transgenic TyrCreER+; MRGPRX4LSL+/- model, in which melanoma arises spontaneously from endogenous mouse melanocytes, was studied in immunocompetent mice, allowing us to fully characterize the tumor, including the tumor immune microenvironment (Fig. 2L–O), in an intact immune setting. In contrast, the human A2058 melanoma cell studies (proliferation and metastatic seeding; Fig. 4B–J) required an immunodeficient host, since human cells would otherwise be rejected by a competent murine immune system. For these experiments, we used NSG mice, the standard immunodeficient strain used in human xenograft studies. We have updated the text to reflect this.

      In Figure 1A, the p-value of -145 begs for a little explanation. I don't recall seeing such a p-value.

      The small p-value reflects two features of the comparison: (1) both GTEx normal skin and TCGA-SKCM contain large sample sizes (hundreds of samples per group), which gives the Mann-Whitney U test (also known as the Wilcoxon rank-sum test) statistical power, and (2) MRGPRX4 expression shows minimal overlap between the two groups; it's essentially undetectable in normal skin but broadly expressed across melanoma samples. Together, these yield such a p-value. This is expected for rank-based tests applied to large, cleanly separated datasets.

      Have you considered treating the murine melanomas with murine via PD-L1? I appreciate that this comment is somewhat superfluous given the inhibition of MRGPRX4 with compound 31-2, but given the human therapeutics combined with the fact that you have done 'everything else', I wonder what might happen.

      We agree with the reviewer that testing checkpoint blockade in the MRGPRX4-driven model is a relevant direction. Our finding that MRGPRX4-driven tumors develop a PD-L1hi, neutrophil-rich microenvironment (Fig. 2M–O) makes anti-PD-L1 treatment a natural next experiment, and we would predict it to be informative both on its own and in combination with an MRGPRX4 inhibitor, given that the two target distinct compartments- the tumor-immune microenvironment versus tumor-intrinsic proliferative/invasive signaling. We consider it an important direction for future work.

      Given the basal ligand-independent signaling, might engineering variants of MRGPRX4 that do not signal be of value?

      This is a great point. A variant that disrupts basal (ligand-independent) signaling specifically would be informative. Identifying and validating such a basal-activity-disrupting variant, including confirming normal receptor expression and trafficking, is an important direction for future work.

      Reviewer #2 (Public review):

      Summary:

      This study presents a fundamental new finding - the identification of a sensory-neuron itch receptor, MRGPRX4, as an unexpected melanoma oncogene through a mechanism of lineage-inappropriate expression rather than mutation. The evidence supporting the core observation (tumor-specific upregulation, restriction to invasive transcriptional states, and sufficiency to drive fully penetrant metastatic melanoma in vivo) is compelling, drawing on convergent human genomic datasets and a well-controlled genetic mouse model. However, several of the mechanistic and translational claims - particularly regarding causal drivers of invasion, the immunosuppressive tumor microenvironment, and in vivo pharmacological efficacy - remain incomplete, relying on correlative evidence.

      Strengths

      The authors propose that MRGPRX4, normally restricted to a subset of peripheral sensory neurons, is aberrantly re-expressed in melanoma rather than through mutational mechanisms, and that this re-expression is sufficient to drive tumorigenesis through basal, ligand-independent GPCR signaling. This is a genuinely novel model for oncogenesis, and the manuscript deploys an impressive range of approaches - bulk and single-cell transcriptomics, spatial transcriptomics, proteomics, phosphoproteomics, and pharmacology - to support it.

      Strengths:

      The claim that MRGPRX4 is selectively upregulated in melanoma and confined to neural-crest-like/invasive transcriptional states is well supported, with consistent results across multiple independent human scRNA-seq datasets. The claim that ectopic MRGPRX4 is sufficient to drive melanoma is convincingly demonstrated by the fully penetrant, metastatic phenotype in the Tyr-CreER; MRGPRX4-LSL model, with appropriate specificity controls showing that MRGPRX1, MRGPRX2, and MRGPRX3 do not phenocopy this effect.

      The claim that MRGPRX4 signals through basal, ligand-independent activity is reasonably well supported by bile-acid quantification showing endogenous ligand concentrations well below the EC50 required for activation.

      We are thankful to the reviewer for the positive feedback.

      Weaknesses:

      The claim that MRGPRX4 remodels the tumor microenvironment toward an immunosuppressive state rests on flow cytometric frequency data (altered neutrophil/eosinophil ratios, increased PD-L1+ myeloid populations) but lacks any functional immune assay to demonstrate that this remodeling actually impairs anti-tumor immune responses.

      We acknowledge the reviewer’s suggestion that functional immune assays will demonstrate that MRGPRX4-driven tumor remodeling impairs checkpoint-driven anti-tumor immune response. We consider this an important direction for future work.

      The claim that the two MRGPRX4-enriched tumor subpopulations (ECM-rich and NC-like/invasive) underlie the observed invasive and metastatic phenotype is not directly tested; the authors appropriately acknowledge this as an open question, but it is worth noting explicitly that this leaves the mechanistic link between the identified cell states and the functional phenotype (proliferation, invasion, metastasis shown in Figure 4) unresolved.

      We agree with the reviewer. To test the direct role of these subpopulations in driving metastasis in our model, we need to ablate them specifically. This is possible with an intersectional genetics strategy, wherein we could use a state-specific Dre or Flp driver (e.g., a Prrx1-DreER or Prrx1-FlpO knock-in) crossed to a dual-recombinase-dependent effector allele (e.g., a Frt- or Rox-gated diphtheria toxin receptor), and then crossed to our TyrCreER-MRGPRX4-LSL model. This quadruple-transgenic strategy would allow ablation restricted specifically to MRGPRX4-driven tumor cells occupying the target mesenchymal state, for example. These genetic lines can be created but require generating or sourcing new dual-recombinase-dependent alleles and a substantially longer breeding and validation timeline (approximately 18-24 months). Together, these represent possible, if long-term, strategies for directly testing the causal contribution of these MRGPRX4-enriched subpopulations to melanoma invasion and metastasis.

      Finally, the comparison with BRAF- and NRAS-driven GEMMs (Figure 3K-L) establishes overlap in transcriptional cell states but does not report whether these canonical models themselves upregulate endogenous Mrgprx4. This omission leaves unclear whether MRGPRX4 acts as a convergent node downstream of canonical oncogenic signaling, or represents an independent, parallel route to a similar phenotypic endpoint - a distinction that matters considerably for how broadly the finding should be interpreted.

      MRGPRX4 is a primate-specific receptor with no mouse ortholog in melanocytes; thus, we cannot assess endogenous expression of MRGPRX4 in BRAF/NRAS-driven GEMMs. Nevertheless, the following observations argue against MRGPRX4 functioning solely downstream of canonical oncogenes. First, TyrCreER<sup>+</sup>; MRGPRX4LSL mice develop fully penetrant melanoma without engineered BRAF or NRAS activation or tumor-suppressor loss. Second, MRGPRX4 loss in BRAF V600E mutant A2058 cells reduces pERK1/2, pAKT, and pS6K, showing that MRGPRX4 sustains these signaling outputs even in the presence of activated BRAF. Together, these findings support a model in which MRGPRX4 could provide a distinct oncogenic input.

      Overall assessment:

      The manuscript's central, most novel claim - that lineage-inappropriate expression of a sensory GPCR is sufficient to drive melanoma - is compellingly supported. The secondary mechanistic and translational claims built around this finding are convincing and consistent with the broader literature but are currently supported by correlative rather than causal or functional evidence.<br />

      Recommendations for the authors:

      Reviewing Editor Comments:

      Both reviewers found much novelty and potential for changing thinking about melanoma biology with your discovery of MRGPRX4 as a relatively melanoma-specific G protein-coupled receptor. Particularly in neural-crest-like/invasive states, MRGPRX4 was aberrantly re-expressed in human melanomas. With the Tyr-CreER; MRGPRX4-LSL mouse model, there were compelling data in transcriptomics and proteomics. As one reviewer noted, your work closes a circle from early MAS1 (a related GPCR) oncogene studies to the MRGPR family, consistent with the shared neural-crest origin of melanocytes and sensory neurons.

      There were several minor suggestions and clarifications suggested by the reviewers. Please address them in a revised manuscript, which we will review without sending it back to the reviewers.

      Reviewer #1 (Recommendations for the authors):

      There is a number of grammatical errors and spacing issues that could be sorted out via built-in editing tools.

      We have checked the manuscript and are resubmitting updated version.

      Reviewer #2 (Recommendations for the authors):

      Examine whether Mrgprx4 is detectable (even at low levels) in the BRAF^V600E; Pten^fl/fl and NRAS^Q61K; Ink4a−/− datasets used for integration in Figures 3K-L.

      Levels of MRGPRX4 in BRAF- and NRAS-driven GEMMs cannot be interrogated, as MRGPRX4 is a primate-specific gene and hence not expressed in mice.

      In vivo antagonist efficacy: Given the well-established transgenic model, in vivo testing of compound 31-2 (or a more potent/optimized MRGPRX4 antagonist) on tumor growth or metastatic burden would considerably strengthen the translational claims.

      We appreciate the reviewer's recommendation and agree that in vivo testing of an MRGPRX4 antagonist would meaningfully strengthen the translational relevance of our findings. However, we do not believe compound 31-2 is a viable candidate for in vivo studies. While the reported biochemical IC50 on the company's (MedChemExpress) website is ~100 nM, in our hands, using a cell-based assay, we required a substantially higher concentration (5 µM) to block receptor activity. Additionally, using our GPCR (calcium-based) activation assays, we found that the compound is no longer active after approximately 6 hours in solution, necessitating the addition of freshly prepared compound at least twice daily in our in vitro culture system.

      Compound 31-2 is a tool compound with no available in vivo pharmacokinetic characterization (bioavailability, clearance, half-life, or protein binding), and translating our in vitro dosing requirement to an in vivo regimen would demand achieving sustained micromolar free-drug exposure, likely requiring impractically high and frequent dosing, or specialized delivery methods (e.g., continuous infusion). We therefore consider compound 31-2 unsuitable for in vivo efficacy testing in its current form. Development or identification of a more potent, metabolically stable, and orally bioavailable MRGPRX4 antagonist with an established in vivo PK profile will be necessary before in vivo antitumor efficacy can be meaningfully evaluated.

    1. Author response:

      The following is the authors’ response to the original reviews

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      This manuscript describes a chemical screen for activators of the eIF2 kinase GCN2 (EIF2AK4) in the integrated stress response (ISR). Recently, reported inhibitors of GCN2 and other protein kinases have been shown at certain concentrations to paradoxically activate GCN2. The study uses CHO cells and ISR reporter screens to identify a number of GCN2 activator compounds, including a potent "compound 20." These activators have implications for the development of new therapies for ISR-related diseases. For example, although not directly pursued in this study, these GCN2 activators could be helpful for the treatment of PVOD, which is reported for patients with certain GCN2 loss-of-function mutations. The identified activators are also suggested to engage with the GCN2 directly and can function while devoid of GCN1, a co-activator of GCN2.

      Strengths:

      The manuscript appears to be a largely rigorous study that flows in a logical manner. The topic is interesting and significant.

      Weaknesses:

      Portions of the manuscript are not fully clear. Some experimental presentation and design concerns should be addressed to support the stated conclusions.

      We thank the reviewer for their supportive comments. We agree that portions of the manuscript were not fully clear and that some aspects of the experimental presentation and design required clarification.

      To address this, we have revised the manuscript to make the experimental logic more transparent. In particular, we now explain more clearly the rationale for the screening strategy, including the use of histidinol as a canonical GCN2 activator, latrunculin A as a modulator of PPP1R15A-mediated eIF2α dephosphorylation, and tunicamycin as a PERK-dependent ER-stress control. We also clarify why a submaximal concentration of histidinol was used: this was intended to reveal compounds that enhance ISR signalling when GCN2 is partially activated.

      We have clarified the use of the two ATF4 reporter systems. The ATF4–NanoLuc reporter was used for sensitive primary screening, whereas the ATF4–luc2 reporter was used as a more stringent orthogonal assay to prioritise robust ISR activators. We now state explicitly why some initial hits were not retained after testing in the second reporter line, and why the NanoLuc system was subsequently used again for mechanistic experiments.

      Finally, we have revised the presentation of the orthogonal validation steps to make clearer how they support the stated conclusions. These include assays designed to distinguish GCN2-dependent ISR activation from indirect activation through ER stress, additional analysis of GCN2 dependence, and clearer interpretation of biochemical and docking data.

      We hope that these revisions address the reviewer’s concern that the experimental design and data presentation needed to be made clearer in order to support the conclusions.

      Reviewer #2 (Public review):

      Summary:

      In this manuscript, Zhu, Emanuelli, and colleagues describe a novel pharmacological activator of the Integrated Stress Response kinase GCN2. The work is conclusive and biochemically solid. This work significantly adds to the pharmacological arsenal targeting the ISR and, in particular, GCN2.

      Strengths:

      Strong biochemistry, novel molecular activator of GCN2 (GCN1 independent).

      Weaknesses:

      The rationale for the screen is not exploited in the results (e.g., pathogenic GCN2 mutants), and lots of cell-based read-outs are not endogenous.

      We thank this reviewer for their positive assessment of the work. We address the three major concerns in turn below.

      Major points

      (1) Regarding the justification of the work. Since the authors justify the screen for GCN2 activators with loss-of-function mutants associated with diseases, it would be of interest to evaluate whether the best compounds identified in the study are indeed able to prompt activation of those mutants (or at least of the most prevalent). This approach could actually go in parallel with the docking experiments carried out in the last figure of the manuscript, where mutants could be modelized as well.

      To address this point, we tested whether the lead compounds could activate disease-associated GCN2 variants linked to pulmonary veno-occlusive disease. In contrast to GCN2iB, the new compounds did not activate these variants. We now state this explicitly in the manuscript, thereby clarifying that although the compounds identify a new mode of GCN2 activation, they do not rescue the pathogenic GCN2 variants tested here.

      Results

      “Moreover, in contrast to GCN2iB (17), the current compounds did not activate disease-associated GCN2 variants linked to PVOD [data not shown].”

      (2) The compounds are only tested using « artificial » proximal signaling outputs. It would be interesting to evaluate whether the best identified compounds are capable of prompting endogenous eIF2alpha phosphorylation in cellular models.

      We thank the reviewer for this suggestion. Detecting eIF2α phosphorylation following activation of GCN2 is technically challenging and typically produces weaker signals compared to activation of other ISR kinases, such as PERK (e.g. by thapsigargin). For this reason, many studies rely on downstream reporter assays to monitor GCN2 activity. To address the reviewer’s concern, we have now included an orthogonal readout of ISR activation by assessing global translation using a puromycin incorporation assay. Using this approach, we show that compound 20 significantly reduces translation, and importantly, this effect is attenuated in GCN2-deficient cells, supporting a GCN2-dependent mechanism.

      Results

      “Studies with compound 18 were limited by poor aqueous solubility; therefore, time‑course analyses focused on compounds 20 and 21. To assess ISR activation over an extended period, live‑cell luciferase measurements were performed using CHO cells stably expressing an ATF4::Nanoluc-PEST reporter. Both compounds elicited maximal reporter activation between 6 and 8 h (Figure S1A&B). Compound 20, but not 21, induced a significant GCN2‑dependent reduction in mRNA translation, as measured by puromycin incorporation, with a progressive effect observed up to 7 h (Figure S1C-F).”

      (3) Other GCN2 activators (other than GCN2iB, e.g., HC-7366) were recently identified. In this context, it would be of interest to carry out a small benchmarking study to evaluate how the compounds identified in the current study perform against the previously identified molecules.

      We thank the reviewer for this suggestion. In response, we obtained HC-7366 and assessed its activity alongside our compounds in the CHO ATF4::NanoLuc reporter assay. In this system, compound 20 demonstrated greater potency than HC-7366 (see reviewer figure below). However, we note that HC-7366 showed relatively limited activity in CHO cells in our hands, despite previously reported strong effects in other cellular systems and in vivo models. This context-dependent activity makes direct benchmarking difficult. Accordingly, we have included this comparison in the revised manuscript and discuss this limitation in the Discussion.

      Discussion

      “We also evaluated the reported GCN2 activator HC-7366 in our CHO ATF4::NanoLuc reporter system. In this context, HC-7366 showed limited activity relative to compound 20, despite its reported efficacy in other cellular systems and in vivo (data not shown). This highlights potential context dependence in small‑molecule activation of GCN2 and limits direct cross-study comparison.”

      Author response image 1.

      ISR activation by compound 20 and GC-7366 in CHO cells

      Normalised fold-change in ATF4 signal in CHO ATF4::NanoLuc reporter cells treated for 19 hours with Compound 20 or HC-7366. DMSO was used as vehicle control. (representative experiment, mean ± SEM, n=3 technical replicates).

      Reviewer #3 (Public review):

      Summary:

      In this manuscript, the authors describe the results of a high-throughput screen for small-molecule activators of GCN2. Ultimately, they find 3 promising compounds. One of these three, compound 20 (C20), is of the most interest both for its potency and specificity. The major new finding is that this molecule appears to activate GCN2 independent of GCN1, which suggests that it works by a potentially novel mechanism. Biochemical analysis suggests that each binds in the ATP-binding pocket of GCN2, and that at least in vitro, C20 is a potent agonist. Structural modeling provides insight into how the three compounds might dock in the pocket and generates testable hypotheses as to why C20 perhaps acts through a different mechanism than other molecules.

      We agree that GCN1-independent activation suggests a potentially distinct mechanism of action. While we are currently unable to define the mechanistic basis underlying the GCN1-independence of compound 20, prior work provides some relevant context. Recent studies have shown that the ATP-competitive modulator GCN2iB can activate GCN2 independently of GCN1 under specific conditions, notably in the context of the GCN2 E26A mutant [Carlson, 2023]. This observation raises the possibility that, under certain conditions, engagement of the kinase domain, potentially via the ATP-binding pocket, may bypass the requirement for GCN1. However, in our system, we did not observe GCN1-independent activation with GCN2iB at the concentrations tested. This discrepancy may reflect a narrow or context-dependent window for such activity, or differences between wild-type and mutant GCN2. These findings suggest that GCN1-independent activation of GCN2 may occur under specific conditions or with distinct classes of compounds, although further work will be required to define the underlying mechanism for compound 20. We have added the following to the main text:

      Discussion

      “Recent work suggests that the ATP-competitive modulator GCN2iB can activate GCN2 independently of GCN1 under specific conditions using a GCN2 E26A mutant (9). In our hands, we did not observe GCN1‑independent activation with GCN2iB at the concentrations tested. This discrepancy may reflect a narrow concentration window for GCN1‑independent activation or context‑dependent effects of the E26A mutation. These findings raise the possibility that GCN1‑independent activation of GCN2 may occur under specific conditions or with distinct classes of compounds.”

      Strengths:

      Of the 3 compounds identified by the authors, C20 is the most interesting, not just for its intriguing mechanistic distinction as being GCN1-independent (shown genetically in two distinct cell lines, CHO and 293T in Figure 4, and in contrast to other GCN2 activators) but also for its potency. In in-cellulo assays, compound 21 appears as more of an ISR enhancer than an activator per se, and although compound 18 and compound 21 lead to upregulation of the ISR targets (Figure 2), that degree of upregulation is probably not significantly different from that induced by those compounds in Gcn2-/- cells. For C20, the effect appears stronger (although it is unclear whether the authors performed statistical analysis comparing the two genotypes in Figure 2D). In Figure 3, only C20 activates the ISR robustly in both CHO and 293T. Ultimately, C20 might be a tool for providing mechanistic insight into the details of GCN2 activation and regulation, and could be exploited therapeutically.

      Prompted by this suggestion, we assessed C20 in two additional commonly used cell lines: human colon carcinoma HCT116 cells and African green monkey COS7 cells. C20 showed no activity in these models. In contrast, primary mesothelioma cells (Mesobank T12) exhibited robust PPP1R15A induction in response to the compound. The following text has been added to the manuscript.

      Results

      “We went on to examine downstream cellular consequences of GCN2 activation in multiple models. While compounds did not induce detectable ISR signalling in HCT116 or COS‑7 cells under the conditions tested, induction of PPP1R15A was observed in Mesobank T12 primary mesothelioma cells, indicating context-dependent biological responses… [data not shown].”

      Weaknesses:

      There are some limitations to the existing work. As the authors acknowledge, they do not use any of the compounds in animals; their in vivo efficacy, toxicity, and pharmacokinetics are unknown. But even in the context of the in cellulo experiments, it is puzzling that none of the three compounds, including C20, has any effects in HeLa cells when Neratinib does. It's beyond the scope of this paper to address definitively why that is, but it would at least be reassuring to know that C20 activates the ISR in a wider range of cells, including ideally some primary, non-immortalized cells. In addition, the ISR is a complex, feedback-regulated response whose output varies depending on the time point examined. The in cellulo analysis in this paper is limited to reporter assays at 18 hours and qRT-PCR assays at 4 and 8 hours. A more extensive examination of the behaviour of the relevant ISR mRNAs and proteins (eIF2, ATF4, CHOP, cell viability, etc.) for C20 across a more extensive time course would give the reader a clearer sense of how this molecule affects ISR output.

      We thank the reviewer for this insightful suggestion. To address the need for a more comprehensive assessment of ISR signalling, we have extended our analysis across a broader time course and incorporated additional functional readouts. Using the ATF4-NanoLuc reporter, compounds 20 and 21 exhibit peak ISR activation at approximately 6-8 h in wild-type cells. In parallel, we assessed global mRNA translation using puromycin incorporation and found that compound 20, but not compound 21, induces a progressive reduction in translation over this period, which is dependent on GCN2. While we agree that direct measurement of upstream ISR markers such as eIF2α phosphorylation can be informative, detection of GCN2-mediated eIF2α phosphorylation is technically challenging and often less robust than activation of other ISR kinases (e.g. PERK). For this reason, we have prioritised orthogonal downstream functional readouts, including reporter activity and translational output, to capture ISR pathway engagement. These additional data provide a clearer picture of the kinetics and functional consequences of compound-induced ISR activation and have been incorporated into the revised manuscript.

      Results

      “Studies with compound 18 were limited by poor aqueous solubility; therefore, time‑course analyses focused on compounds 20 and 21. To assess ISR activation over an extended period, live‑cell luciferase measurements were performed using CHO cells stably expressing an ATF4::Nanoluc-PEST reporter. Both compounds elicited maximal reporter activation between 6 and 8 h (Figure S1A&B). Compound 20, but not 21, induced a significant GCN2‑dependent reduction in mRNA translation, as measured by puromycin incorporation, with a progressive effect observed up to 7 h (Figure S1C-F).”

      I also find it a bit strange that the authors describe C20 as "demonstrat(ing) weak inhibition of ... PKR" - the measured IC50 is ~4 μM, which is right around its EC50 for GCN2 activation. This raises the confounding possibility that C20 would simultaneously activate GCN2 while inhibiting PKR. While perhaps inhibition of PKR is not relevant under the conditions when GCN2 would be activated either experimentally or therapeutically, examining in cells the effects of C20 on GCN2 and PKR across a dose range would shed light on whether this cross-reactivity is likely to be of concern.

      We thank the reviewer for highlighting compound 20 as the most interesting lead compound and for recognising its apparent ability to activate GCN2 independently of GCN1. The reviewer identified several limitations relating to cell-type specificity, the temporal behaviour of ISR activation, and possible PKR cross-reactivity.

      In response to the concern about cell-type specificity, we tested compound 20 in additional cellular models. Compound 20 did not induce detectable ISR signalling in HCT116 or COS-7 cells under the conditions tested, consistent with the reviewer’s observation that activity is not universal across cell types. However, we observed induction of PPP1R15A in primary Mesobank T12 mesothelioma cells. We have therefore revised the manuscript to present compound 20 activity as cell-context dependent rather than broadly generalisable across all cell types.

      To address the reviewer’s concern that the ISR output was examined only at limited time points, we extended the time-course analysis for compounds 20 and 21. Using live-cell ATF4::NanoLuc reporter measurements, both compounds showed maximal reporter activation at approximately 6-8 hours. We also measured translational output by puromycin incorporation and found that compound 20, but not compound 21, caused a progressive GCN2-dependent reduction in translation. These data provide a clearer view of the kinetics and functional consequences of compound 20-mediated ISR activation.

      The reviewer also noted that compound 20 inhibits PKR in vitro at concentrations close to those required for GCN2 activation in cells. We agree that this is an important potential liability. Because PKR signalling was not robustly or reproducibly inducible in our CHO-based reporter system, we were unable to perform a reliable cellular dose-response analysis of PKR engagement in the present study. We have therefore revised the Discussion to acknowledge kinase cross-reactivity, including possible PKR inhibition, as an important limitation and an issue for future development of this chemical series.

      Finally, we have moderated our mechanistic interpretation of compound 20. Although the data support direct engagement of GCN2 and suggest a mechanism distinct from canonical GCN1-dependent activation, we now discuss GCN1-independent activation more cautiously and in the context of prior reports that GCN2iB can display GCN1-independent activity under specific experimental conditions.

      Discussion

      “While the functional relevance of PKR inhibition in our cellular systems is uncertain, these observations highlight the potential for kinase cross-reactivity, which will be important to address in future studies.”

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):<br /> (1) The description of the chemical screen for Gcn2 activators is not sufficiently clear and detailed. a) Briefly and early on provide the rationales (modes of action) for using histindinol and latruculin A. Explain further the rationale in Figure 2, outlining the purpose for the combined compound + submaximal dose of histindinol.

      The text has been amended.

      Results

      “Histidinol activates GCN2 by inhibiting histidyl‑tRNA synthetase, leading to the accumulation of uncharged tRNAHis. This uncharged tRNA binds to GCN2, relieving its autoinhibition and activating the kinase (35). Latrunculin A sequesters G‑actin, thereby inhibiting PPP1R15A activity (36, 37). Tunicamycin inhibits protein glycosylation in the endoplasmic reticulum (ER), resulting in activation of PERK (38).”

      “This submaximal concentration was used to allow detection of compounds that enhance ISR signalling when GCN2 is partially activated.”

      b) What is unique about the second CHO: ATF4-luc2 reporter line? Why do only 89 out of the original 130 compounds induce the ISR in this line versus the original CHO: ATF4-Nanoluc cell line? This is confusing for the reader about how compounds were triaged for characterization.

      The ATF4‑Nanoluc and ATF4‑luc2 reporter lines differ only in the luciferase used, but this has important practical consequences. The Nanoluc reporter is substantially more sensitive, so it was used for the primary screen to detect even weak ISR activation. The luc2 reporter has lower sensitivity and a narrower dynamic range, making it a more stringent orthogonal assay. As a result, not all hits from the Nanoluc screen (130 compounds) reproduced in the luc2 line; the 89 compounds retained are those that robustly activate the ISR under these more stringent conditions. This step was therefore used to prioritise stronger, more reproducible activators for downstream characterisation.

      Results

      “While primary screening was performed in ATF4‑Nanoluc lines for maximal sensitivity, hits were subsequently re-tested in a second CHO ATF4::luc2 reporter line as a more stringent orthogonal assay to prioritise robust ISR activators. Of the 130 hits identified in the sensitive Nanoluc screen and passing early toxicity assessment, 89 were confirmed in the luc2 assay, consistent with enrichment for higher-amplitude ISR activators under more stringent detection conditions.”

      c) The study uses a second CHO reporter line in the flow scheme (CHO:ATF4-luc2) and then switches back to an ATF4-Nanoluc line to establish GCN2 dependence. What is the rationale for switching back to the original reporter line?

      The luc2 reporter line was used as a more stringent, orthogonal validation step to prioritise robust ISR activators. For subsequent mechanistic studies, including assessment of GCN2 dependence, we returned to the ATF4‑Nanoluc line because its higher sensitivity and simpler single‑reagent assay format are better suited to multi‑point measurements and comparative analyses. In effect, the luc2 reporter was used for triage, whereas the Nanoluc system was retained for mechanistic characterisation and downstream screening.

      Results

      “In subsequent mechanistic studies, the ATF4‑Nanoluc reporter was again used to take advantage of its higher sensitivity and simpler assay format for multi‑condition comparisons.”

      d) The rationale for the first orthogonal screen described in the results section to identify inducers of ER stress is not clearly explained. The compounds were already determined to be dependent on GCN2 prior to this test, and one would have thought that this criterion would have covered ER stress and alternative eIF2 kinase activators.

      We agree with the reviewer that, in principle, establishing GCN2 dependence should reduce the likelihood of capturing compounds acting through alternative eIF2α kinases. However, we performed this orthogonal ER stress screen to address two practical considerations. First, high‑throughput screening is inherently prone to false positives, as it is typically conducted at a single concentration and time point, and compound libraries may contain degraded or chemically inconsistent material. We therefore used a lower‑throughput, more controlled ER stress assay with freshly sourced compounds and additional readouts (e.g. CHOP and XBP1) to improve confidence in the hits. Second, despite prior evidence of GCN2 dependence, ER stress signalling via PERK converges on the same downstream endpoints: eIF2α phosphorylation and ATF4 induction. We therefore wished to explicitly exclude compounds that activate the ISR indirectly via ER stress. In practice, this proved important, as the orthogonal assay did identify compounds that induced ER stress, which we subsequently excluded from the lead set.

      Results

      “Although hits were prioritised for GCN2 dependence, we performed an additional orthogonal screen to exclude compounds that activate the ISR indirectly via ER stress, which converges on the same downstream outputs.”

      (2) A major point of the manuscript is that there is GCN1 independence for the small molecule activation of GCN2, and this has not yet been reported. One report for this GCN1 independence is reference 9 [Carlson … Wek 2023] (Figure 5). In this report, low doses of GCN2iB that can activate GCN2 (although by the present manuscript at much lower levels than the identified new compounds) induce ATF4 expression in cells expressing an E26A mutant of GCN2 that is suggested to negate GCN1 binding and enhancement of GCN2 activity. Halofuginone induction of ATF4 expression was thwarted by the GCN2 E26A mutant.

      We thank the reviewer for highlighting this important point. We agree that Carlson et al. (2023) suggest that, under certain conditions, GCN2iB can activate GCN2 independently of GCN1 using the E26A mutant. In our experiments, however, we did not observe GCN1‑independent activation with GCN2iB under the conditions tested, i.e. similar low doses. One possible explanation is that the GCN1‑independent activity reported by Carlson et al. occurs only within a narrow concentration range; their observations were made at very low compound concentrations, whereas higher concentrations may engage additional regulatory mechanisms. In our study, we used concentrations optimised for robust ISR activation, which may mask such effects. We also note that the E26A mutation (E18A in yeast), originally identified by two‑hybrid analysis, disrupts the GCN2-GCN1 interaction but may not completely eliminate all modes of functional coupling under all conditions. Taken together, these observations raise the possibility that GCN1‑independent activation represents a context‑dependent mechanism that may be unmasked only under specific experimental conditions or by particular classes of compounds.

      We have revised the Discussion to acknowledge this prior report explicitly and to clarify how our findings relate to it.

      Discussion

      “Recent work suggests that the ATP-competitive modulator GCN2iB can activate GCN2 independently of GCN1 under specific conditions using a GCN2 E26A mutant (9). In our hands, we did not observe GCN1‑independent activation with GCN2iB at the concentrations tested. This discrepancy may reflect a narrow concentration window for GCN1‑independent activation or context‑dependent effects of the E26A mutation. These findings raise the possibility that GCN1‑independent activation of GCN2 may occur under specific conditions or with distinct classes of compounds.”

      (3) The authors state that the ISR was exaggerated in Ppp1r15a KO cells. It would be helpful to include statistical analyses to support this statement.

      Thank you for enabling us to be more precise. New text added:

      Results

      “Activation of the ISR by tunicamycin was exaggerated in the Ppp1r15a<sup>-/-</sup> cells owing to their defective dephosphorylation of eIF2a (wild type vs Ppp1r15a<sup>-/-</sup>, p<0.05).”

      (4) The results state that Chop and Ppp1r15a mRNAs were measured following 4 hours of treatment with compound 18, 20, or 21, but Figure 2D shows treatment from 0 to 8 hours? It appears that the compound still induces these mRNAs in GCN2 KO cells, possibly with delayed kinetics. A lengthened time course study would help determine if this is indeed the case.

      We thank the reviewer for this careful observation. To address the reviewer’s point regarding delayed or GCN2‑independent signalling, we have extended our analysis using compounds 20 and 21, which are more tractable experimentally (solubility). Using the ATF4‑Nanoluc reporter, both compounds show peak ISR activation at ~6–8 h in wild-type cells over an extended time course. In parallel, functional readouts of mRNA translation (puromycin incorporation) demonstrate that compound 20, but not 21, induces a progressive, GCN2‑dependent reduction in translation over this period. These clarify the temporal aspects of signalling by these two compounds.

      Results

      “Studies with compound 18 were limited by poor aqueous solubility; therefore, time‑course analyses focused on compounds 20 and 21. To assess ISR activation over an extended period, live‑cell luciferase measurements were performed using CHO cells stably expressing an ATF4::Nanoluc-PEST reporter. Both compounds elicited maximal reporter activation between 6 and 8 h (Figure S1A&B). Compound 20, but not 21, induced a significant GCN2‑dependent reduction in mRNA translation, as measured by puromycin incorporation, with a progressive effect observed up to 7 h (Figure S1C-F).”

      Legend

      “Supplementary Figure S1. Kinetics of responses to compounds 20 and 21

      (A-B) Wild-type CHO cells stably expressing the ATF4::nanoLuc-PEST reporter were treated with Nano-Glo and either (A) 13mM compound 20 or (B) 13mM compound 21. Median bioluminescence (fold change normalised to DMSO control) ± 95% confidence. Representative experiment (n=4 technical repeats). (C-F) Representative immunoblot of lysates from wild-type or Eif2ak4<sup>-/-</sup> CHO cells treated with 10μM compound 20 or 7.5μM 21 for the indicated times. Immediately before harvesting, cells were treated with 10μg/mL puromycin to label newly synthesised polypeptides. “-“ indicates cells not incubated with puromycin. “U” cells were treated with puromycin but without test compound. “CHX” represents the cycloheximide control (100μg/mL). Molecular size in kDa. (E-F) Quantification of puromycinylated proteins normalised to GAPDH. Mean ± SEM. CHO WT (black) and Eif2ak4<sup>-/-</sup> cells (turquoise. N = 4 independent experiments. Two-way ANOVA with Šídák's multiple comparisons test; ***: p ≤ 0.001.”

      (5) In the section describing the differences between cell lines in the ability of compounds to induce the ISR, this is difficult for the reader to interpret, as no controls are included. How does histidinol (or other canonical inducers of the ISR) behave in the three reporter assays (CHO, 293T, and HeLa)?

      As requested, we now provide ATF4::Nanoluc reporter activation (3mM, 20 hours because of this drug’s slow kinetics)

      Results

      “To benchmark ISR activation in these models, each cell type was treated with 3mM histidinol (Figure S2). Reporter activation was most robust in CHO cells, followed by 293T cells, then HeLa cells.”

      Discussion

      “Moreover, histidinol-induced ISR activation showed a clear hierarchy across cell lines, with CHO cells being the most responsive and HeLa cells the least.”

      Legend

      “Supplementary Figure S2. Cell-type differences in response to histidinol

      Fold-change of ATF4::NanoLuc reporter signal in HEK293T, HeLa and CHO cells transiently transfected with reporter and treated for 20 hours with 3mM histidinol. Fold-change calculated relative to vehicle control. Mean ± SEM).”

      We thank the reviewer for this important question. However, we respectfully disagree that a direct correspondence between the concentrations required for target engagement in the BRET assay and for ISR activation in functional assays should necessarily be expected. BRET (including NanoBRET) is a target engagement assay that measures compound binding to the protein in intact cells, typically by competition with a labelled tracer, and thus reports on apparent intracellular affinity and occupancy rather than downstream biological effect (Robers 2019, PMID 30519940). By contrast, ISR activation is a functional readout that reflects amplification through signalling networks, and can be influenced by multiple additional variables including pathway non-linearity, feedback, and kinase regulation. Consequently, it is well established that potencies derived from target engagement assays do not always align with those measured in functional assays. For example, intracellular kinase profiling studies using NanoBRET have demonstrated systematic potency offsets between binding/engagement measurements and downstream cellular activity, arising from factors such as intracellular ATP competition and pathway context (PMID Capener 2026, PMID 41495225). More generally, target engagement assays provide a quantitative measure of binding, whereas functional assays measure biological outcome, and these readouts need not coincide because they capture distinct aspects of a compound’s mechanism of action. Accordingly, we interpret our BRET data as evidence of direct interaction with GCN2 in cells, rather than as a predictor of the concentration required to activate the ISR. The observation that higher concentrations are required in the BRET assay is therefore not unexpected and does not argue against a requirement for kinase-domain engagement in ISR activation. Instead, it reflects the different mechanistic endpoints captured by the two assay formats.

      We will clarify this point explicitly in the revised manuscript.

      Results

      “The concentrations required to detect target engagement in NanoBRET assays did not directly mirror those required for ISR activation, reflecting the distinction between ligand binding and downstream pathway output.”

      (7) In Figure 5E, the authors suggest that compounds 18 and 20 are non-competitive inhibitors of GCN2 since the Vmax increases with increasing ATP concentration. What is the Km for ATP in the absence or presence of compound 18 or 20? It would be helpful to include progress curves as supplementary data to support the Vmax plots in Fig. 5E. Consider providing more specific units (currently arbitrary units) for the y-axis.

      We thank the reviewer for this insightful comment and agree that our original wording overstated the mechanistic interpretation of these data. In particular, the use of the term “non‑competitive” is not well supported by the current analysis and may be misleading, especially given that our data are consistent with binding within or proximal to the ATP-binding pocket. We have therefore revised the text to remove this designation and instead describe the data more conservatively in terms of changes in apparent Vmax, without assigning a specific inhibition mechanism. With respect to kinetic analysis, we agree that full determination of Km values and inclusion of progress curves would provide a more rigorous mechanistic interpretation. However, given the primary focus of this manuscript on identifying and characterising small‑molecule activators of GCN2 in cells, we believe that a detailed steady‑state kinetic analysis would be beyond the scope of the current study. We have therefore moderated our conclusions accordingly and now present these data as preliminary kinetic observations rather than definitive evidence of inhibition modality.

      Results

      “Compounds 18 and 20 altered the apparent kinetic parameters of GCN2, including an increase in the observed V<sub>max</sub>; however, these data do not allow assignment of a specific inhibition modality.”

      (8) The full-length GCN2 assay presented in Figure 5G appears to be unresponsive to uncharged tRNA, a known regulator of GCN2. The statement that compound 20 induces eIF2 phosphorylation to a greater extent than tRNAs is true for the in vitro assay, but arguably is because the in vitro assays do not recapitulate the in vivo arrangement.

      We thank the reviewer for this comment. We respectfully disagree that the assay is unresponsive to uncharged tRNA. In our hands, GCN2 does exhibit activation in response to tRNA; however, the magnitude of this effect is modest (~4‑fold) compared to the substantially stronger activation observed with compound 20 (~40‑fold). As a result, the tRNA response can appear compressed when both are plotted on the same scale. We agree with the reviewer that the in vitro assay does not fully recapitulate the in vivo regulatory environment, where factors such as GCN1 and ribosome association are known to potentiate GCN2 activation. This limitation likely explains the relatively weaker response to tRNA under our assay conditions and was a key motivation for incorporating cellular assays in our study. Interestingly, the marked difference in activation magnitude between tRNA and compound 20 in vitro raises the possibility that compound-mediated activation may, at least in part, bypass regulatory features that normally constrain GCN2 activity in a GCN1‑dependent manner. While we have not directly tested this hypothesis, we will temper the wording and include this as a speculative point in the Discussion.

      Results

      “Of note, uncharged tRNA produced a modest (~4‑fold) activation of GCN2 under these conditions, whereas compound 20 induced substantially greater (~40‑fold) activation.”

      Discussion

      “The markedly greater activation observed with compound 20 compared with uncharged tRNA in vitro raises the possibility that such compounds may partially bypass regulatory constraints on GCN2 activation, including those normally mediated by GCN1.”

      (9) Using purified GCN2 kinase domain at low ATP concentrations (10 μM), compounds 18 and 20 were shown not to inhibit GCN2 up to concentrations of 3 μM. In previous assays, much higher concentrations of compounds 18 and 20 were used to inhibit GCN2. Why were different concentrations used? This makes this interpretation of this data difficult for the reader to draw conclusions.

      We thank the reviewer for this comment and agree that the use of different concentration ranges across assays may not have been sufficiently clear. The kinase‑domain assay performed at low ATP (10 μM) was specifically designed to assess whether compounds 18 and 20 have a propensity to inhibit GCN2 under conditions that sensitise detection of ATP‑competitive effects and facilitate comparison with related eIF2α kinases. This assay was therefore optimised for detecting inhibition, rather than activation. In contrast, the higher concentrations used in other experiments were selected to robustly measure ISR activation in cellular or full‑length protein contexts, where higher compound exposure is required to observe downstream signalling outputs. These two assay systems therefore address distinct mechanistic questions—targeting inhibition under controlled biochemical conditions versus activation in more complex functional settings—and are not directly comparable in terms of concentration–response relationships. We will revise the manuscript to clarify this distinction and to emphasise that the kinase‑domain assay was not intended to define the activation potency of the compounds.

      Results

      “This assay was performed at low ATP concentrations to sensitise detection of ATP-competitive inhibition and was not optimised to detect compound-mediated activation of GCN2.”

      (10) In silico docking studies support the binding of compound 20 in the ATP-binding pocket of the GCN2 kinase domain. How is this compatible with the stated ATP non-competitive mechanism?

      We agree with the reviewer that our previous description was misleading. The designation of compounds 18 and 20 as “ATP non‑competitive” is not supported by the available data and is inconsistent with the docking results suggesting binding within the ATP‑binding pocket. We have therefore revised the manuscript to remove this terminology and to describe the kinetic behaviour more cautiously, without assigning a specific mode of inhibition.

      (11) The study does not appear to feature biological assays demonstrating the effects of GCN2 activation. For example, does compound 20 reduce translation or growth of cells in a GCN1/GCN2-dependent manner, or do the compounds overcome PVOD mutations akin to the authors' Hum Mol Genet 2024 Aug 18;33(17):1495-1505 article?

      We thank the reviewer for this suggestion. We agree that defining downstream biological consequences of GCN2 activation is an important goal. We did explore this using several cellular systems; however, these effects were context-dependent and not consistently observed across models. Specifically, compounds did not induce a detectable ISR in HCT116 or COS‑7 cells under the conditions tested, despite responsiveness of these systems to canonical activators such as histidinol. In contrast, we did observe induction of PPP1R15A in primary mesothelioma cells, indicating that biological responses can be elicited in certain cellular contexts. We also tested whether these compounds could rescue disease-associated GCN2 variants linked to PVOD, as previously reported for GCN2iB, but did not observe activation of these mutants. These findings suggest that while the compounds robustly activate GCN2 signalling in reporter assays, downstream biological outputs are context-dependent and may require specific cellular conditions or co-factors. Given the variability across systems, we have limited our conclusions to ISR activation and have not generalised broader biological effects. We will clarify this point in the revised manuscript.

      Results

      “We went on to examine downstream cellular consequences of GCN2 activation in multiple models. While compounds did not induce detectable ISR signalling in HCT116 or COS‑7 cells under the conditions tested, induction of PPP1R15A was observed in Mesobank T12 primary mesothelioma cells, indicating context-dependent biological responses. Moreover, in contrast to GCN2iB (17), the current compounds did not activate disease-associated GCN2 variants linked to PVOD [data not shown].”

      (12) For the control of neratinib and other activators linked with ATP binding that are suggested to be dependent on GCN1 in Fig. 4, include reporter induction by drug treatment in Gcn2-/- cells. It would be helpful to be clear in the list of compounds between those suggested to be direct activators versus those that may create stress that leads to GCN2 activation.

      We thank the reviewer for this suggestion. In response, we have performed additional reporter assays in both WT and GCN2<sup>-/-</sup> cells to assess the dependence of drug-induced ISR activation on GCN2. These experiments reveal clear GCN2 dependence for reporter induction upon treatment with sunitinib, NXP800, WEE1-in-4, Debio0123, gefitinib, and erlotinib, as signal is markedly reduced in GCN2⁻/⁻ cells compared to WT.

      In contrast, dovitinib and AZD1775 show less clear dependence, with relatively low reporter signal even in WT cells (notably lower than observed in Fig. 4C), limiting interpretation. Interestingly, dabrafenib induces stronger reporter activity in GCN2<sup>-/-</sup> cells than in WT, indicating that its effects are independent of GCN2 and may reflect activation of alternative stress or signalling pathways.

      Results

      “To further assess the mechanism of compound-induced ISR activation, we evaluated reporter responses in GCN2-deleted cells (Supplementary Figure S3). Several compounds, including sunitinib, NXP800, WEE1-in-4, Debio0123, gefitinib, and erlotinib, showed reduced reporter activity in GCN2-deficient cells, consistent with GCN2-dependent activation. In contrast, dovitinib, AZD1775 and dabrafenib produced weaker or inconclusive responses even in the paired wild-type lines, limiting analysis. These data allow us to distinguish compounds consistent with direct or GCN2-dependent activation from those more likely to induce ISR indirectly through cellular stress upstream of GCN2. These findings support a distinction between compounds that activate the ISR through GCN2-dependent mechanisms and those that likely act indirectly via alternative stress pathways.”

      Legend

      “Supplementary Figure S3. GCN2-dependence of ISR activation by putative GCN2 agonists

      Normalised fold-change in ATF4 signal in CHO WT (purple) and Gcn2-/- (blue) ATF4::NanoLuc reporter cells treated for 19 hours with a panel of ATP-competitive kinase inhibitors reported to activate GCN2 (at 1 and 3µM, sunitinib used at 3 and 10µM, AZD1175 used at 0.3 and 1µM, gefitinib and erlotinib used at 3 and 10µM). DMSO was used as vehicle control. (n=3; mean ± SEM).”

      Minor Comments:

      (1) In the introduction, the authors state that "Several type 1 and 1.5 kinase inhibitors can activate GCN2 at low concentrations while inhibiting at higher concentrations". What is the evidence that type I inhibitors can activate GCN2?

      Thank you for this query. We believe our initial phrasing was open to misinterpretation. The new wording is

      Introduction

      “Several kinase inhibitors classified as type 1 or type 1.5 with respect to their canonical targets can activate GCN2 at low concentrations while inhibiting it at higher concentrations; however, their binding mode to GCN2 remains undefined.”

      (2) A CHO:ATF4-Nanoluc translation reporter screen was used to screen 123K compounds and divide them into a pool of inhibitors and a pool of activators. The criteria used to make this distinction are not sufficiently described in the manuscript, and screen results are not supplied as supplementary data.

      We thank the reviewer for highlighting the need for greater clarity regarding the screening criteria and reproducibility. Compounds from the primary screen (BioAscent library of 123,222 drug-like compounds performed by the ALBORADA Drug Discovery Institute) were classified based on Z-score thresholds, with activators defined as those with Z-score > 3. To assess robustness, the primary screen data were re-analysed independently. In an initial analysis of 121,000 compounds (excluding plates failing quality control), 6,521 compounds met the activator threshold. Of these, 6,461 overlapped with the original hit list. The small number of discrepancies included: (i) compounds absent from the analysed dataset (e.g. originating from failed plates), and (ii) compounds with Z-scores close to the threshold (typically between −3 and −3.02), consistent with minor analytical variation (e.g. rounding). Overall, these analyses show a high degree of concordance in hit identification, with differences restricted to borderline cases near the selection threshold. We have clarified these criteria below.

      Results

      “Compounds were classified based on Z-score thresholds derived from the primary screen, with activators defined as those with Z-score > 3. An initial analysis of 121,000 compounds, excluding plates failing quality control, identified 6,521 activators, of which 6,461 overlapped with the subset selected for follow-up screening. Minor discrepancies were restricted to compounds absent from the analysed dataset (e.g. originating from failed plates) or those with Z-scores close to the threshold (3 to 3.02), consistent with limited analytical variation. Using this approach, we assembled a subset of 6,461 compounds enriched for potential ISR activators and screened these in 384-well format at 10 µM for 16 hours.”

      Reviewer #3 (Recommendations for the authors):

      (1) The legend to Figure 4 should read "Compound 20 displays GCN1 independence", not "dependence".

      Thank you for spotting this error. We have made the correction.

      (2) The text describes Figure 2D as examining 4h, but it also examines 8h.

      We have amended the text to:

      “After validating their effects using the assays described above, we next confirmed activation of the ISR by these compounds at the transcriptional level at 4 and 8 hours.”

      (3) Unless I'm misreading Table S1, compound Z134826202 is listed as activating the ISR, but the authors describe it in the text as inactive.

      Thank you. We have corrected this error.

    1. Author response:

      The following is the authors’ response to the previous reviews.

      eLife Assessment:

      This study provides valuable insights into the role of thalamic nuclei in associative threat and extinction learning, underpinned by a large dataset and rigorous, multipronged analyses. The evidence provided is solid, supporting the main conclusions. Minor analytical refinements notwithstanding, the manuscript will be of broad interest to researchers in learning and memory, fear, thalamic circuitry, and related mental health conditions.

      We sincerely thank the editors and the reviewer for their careful evaluation of the revised manuscript and for their constructive comments. We greatly appreciate the time and effort invested in reviewing our work, and we have carefully considered each suggestion to further improve the clarity, presentation, and interpretation of the manuscript.

      Author’s note:

      We note that several comments refer to figure numbers and manuscript text from an earlier version of the manuscript (e.g., Figure 7 in the earlier version corresponds to Figure 8 in the current revised manuscript). For clarity, our responses below refer to the corresponding figures and sections in the current revised manuscript while addressing each comment individually.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      Badarnee and colleagues analyse fMRI data collected during an associative threat-learning task. They find evidence for parallel processes mediated by the mediodorsal, LGn and pulvinar nuclei of the thalamus. The evidence for these conclusions is promising, but limited by a lack of clarity regarding the preprocessing and statistical methods.

      We thank the reviewer for these encouraging comments and for recognizing the novelty of our approach and its potential contribution to advancing our understanding of thalamocortical interactions during associative threat learning. We also appreciate the reviewer’s constructive suggestions regarding the methodological description, which have helped us improve the clarity of the manuscript.

      Strengths:

      The approach is inventive and novel, providing information about thalamocortical interactions that are scant in the current literature.

      Weaknesses:

      (1) There are not sufficient details present to allow for the direct interrogation of the methods used in the study.

      Thank you for raising this point. As described in our previous revision, we substantially expanded the Experimental Procedure section by adding three dedicated subsections describing the fear learning procedure, shock calibration, and participant instructions. These additions included details regarding the stimuli, experimental context, stimulus and shock durations, average inter-trial interval, pseudorandomized stimulus presentation, and the procedure used to determine each participant’s shock intensity.

      In the current revision, we have further clarified the Methods by specifying electrical stimulator that we used and specified the usage of the gel and placement of the electrodes. We believe these additions provide sufficient methodological detail to allow readers to understand and replicate the experimental procedure (page 40):

      “Electrical stimulation was delivered using a BIOPAC stimulation system with BIOPAC electrodes and conductive gel. The electrodes were attached to the palm of the participant's right hand and positioned in close proximity without making contact with one another. The electric stimulation began…”

      (2) The figures do not contain sufficiently granular details, making it challenging to determine whether the observed effects were robust to individual differences.

      Thank you for this suggestion. To better illustrate the underlying data distribution and between-participant variability, we revised Fig. 1 and 4-6 by adding individual participant data points for the block-level analyses and kernel density estimate (KDE) distributions for the trial-level analyses. These additions allow readers to better assess the distribution of the data and the extent to which the reported effects are consistent across participants while maintaining figure readability. An example of the revised Fig. 1.

      Comments on revisions:

      I continue to recommend the plotting of individual data points. While there may be individual variance, it is important to quantify this in publication so that future studies can appreciate the uncertainty surrounding test statistics.

      Thank you for this recommendation. As described in our response to Weakness 2 above, we revised the figures to better illustrate the underlying data distribution and between-participant variability. Specifically, we added individual participant data points for the block-level analyses and kernel density estimate (KDE) distributions for the trial-level analyses. We believe these revisions improve the transparency of the underlying data while maintaining figure readability. An example of a revised figure is included above.

      Reviewer #2 (Public review):

      Summary:

      The authors quantify human fMRI BOLD responses in pulvinar and mediodorsal thalamic nuclei during a fear conditioning and extinction task across two days, in a large sample size (hundreds of participants). They show that the BOLD responses in these areas differentiate the conditioned (CS+) and safety (CS-) stimulus. Additionally this changes with repeated trials which could be a neural correlate of fear learning. They show that the anterior pulvinar is most correlated with the MD, and that this is not due to anatomical proximity. They perform graph analysis on the pulvinar sub nuclei which suggests that the medial pulvinar is a hub between the sensory (lateral/inferior) and associative (anterior) pulvinar. They show different patterns of thalamic activity across conditioning, extinction, recall, and renewal.

      We thank the reviewer for this thoughtful summary of our work and for recognizing the scope of the study and the value of the findings. We appreciate the reviewer’s careful evaluation and constructive feedback, which helped improve the clarity and interpretation of the manuscript throughout the revision process. Below, we respond to each of the points raised under the Weaknesses and Comments on revisions sections and describe the corresponding revisions made to the manuscript.

      Strengths:

      The data has a large sample size (n=293 in some measures, n=412 in others). This is a validated human fear conditioning/extinction task that Dr Milad's group has been working with for several years. Few labs have investigated the thalamus activity during fear conditioning and extinction, particularly with a large sample size. There is an independent replication of the pulvinar network structure (Fig. 3), which suggests that the processing in the more sensory-related inferior and lateral pulvinar is relayed to the anterior pulvinar (and possibly thereby to more action-related prefrontal areas) via an intermediate step in the medial pulvinar - potentially a novel discovery but that needs more validation.

      Weaknesses:

      (1) The authors cannot make causal claims about their results based on correlational neuroimaging evidence. Causal claims should be pared back. E.g. Sentence 1 in results "The anterior pulvinar and MD contribute to early associative threat learning, as evidenced by increased functional activation in response to CS+ compared to CS- at the block level (Fig. 1b-c)." needs to be reworded to something like 'the anterior pulvinar and MD have increased functional activation... This suggests that these areas may contribute to early associate threat learning"

      We agree with the reviewer that causal claims cannot be made based on correlational neuroimaging evidence. Accordingly, we carefully revised the manuscript throughout to avoid causal language and instead use wording that reflects statistical associations and interpretations. Representative examples of these revisions are provided below.

      Representative examples of these revisions are shown below:

      Page 7: “At the block level, both the anterior pulvinar and MD showed increased activation to CS+ vs. CS− (anterior pulvinar: t<sub>(292)</sub> = 4.41, p = 0.00001, d = 0.25; MD: t<sub>(292)</sub> = 6.41, p = 5.83x10<sup>-10</sup>, d = 0.37; Fig. 1b–c), suggesting a possible involvement of these regions in early associative threat learning.”

      Page 13: “A data-driven approach suggests a hierarchical computational organization of pulvinar divisions during associative threat learning.”

      Page 13: “we integrated findings from complementary analyses to propose a computational framework describing the functional relationships among pulvinar divisions during associative threat learning.”

      Page 13-14: “The network plot identified a statistical association between the lateral and anterior pulvinar, together with pathways linking the lateral and inferior pulvinar to the anterior pulvinar through the medial pulvinar (Fig. 3b).”

      Page 14: “The medial pulvinar statistically mediates the functional relationships within the pulvinar network and is associated with elevated centrality values. Together, these findings are consistent with a possible hub-like functional role of the medial pulvinar, consistent with higher-order integration of CS+ information, relative to the more sensory-related functional profiles in the inferior and lateral pulvinar. This possible hierarchical organization is consistent with previous evidence showing that the inferior and lateral pulvinar are associated with processing basic sensory information (Berman and Wurtz, 2010, 2008; Cortes et al., 2024), while the medial pulvinar is implicated in higher-order processing, including attention and working memory (Homman-Ludiye and Bourne, 2019).”

      Page 15: “This data-driven analyses provide a possible new perspective on the functional specialization of pulvinar divisions during associative threat learning. Based on these observations, we hypothesized a computational model in which activation in the medial pulvinar statistically mediates the functional relationships between the inferior and lateral pulvinar and the anterior pulvinar (Fig. 3e). To evaluate this hypothesis, we performed a mediation analysis and assessed the robustness of the model using k-fold cross-validation.”

      Page 25: “The vmPFC connectivity may reflect involvement of prefrontal processes related to evaluation and regulation of threat-related information.”

      Page 27: “The medial pulvinar may statistically mediate the functional relationships between the inferior and lateral divisions and the anterior pulvinar, consistent with a hierarchical computational model.”

      Page 29: “Together, these findings are consistent with the possibility that the anterior pulvinar and MD contribute in parallel to associative threat learning, extending the two-system.”

      Page 32: “Using statistical mediation analysis, we found that activation in the medial pulvinar statistically mediated the relationship between activation in the inferior/lateral pulvinar and activation in the anterior pulvinar. This statistical mediation is consistent with, but does not establish, a hierarchical computational organization.”

      (2) Fig .1 The fact that the difference in BOLD activity between CS+ and CS- goes away on the third trial is not addressed. This is a very large effect in the data.

      Thank you for raising this important point. We have addressed this issue in both the Discussion and the Limitations sections, as follows:

      Discussion (page 31):

      “The attenuated CS+ vs. CS− differentiation on the third trial specifically in the pulvinar may reflect a decreased requirement for differential thalamic engagement once the initial association has been acquired. Notably, because the MD sustained the BOLD response to the CS+ in the third trial which may indicate involvement of this nucleus in continued processing or maintenance of the learned association. This aligns with the well-established MD-PFC circuit involved in cognitive processes (Wolff and Halassa, 2024). Additionally, in a previous study using a similar paradigm, we observed sustained CS+ vs. CS− differentiation on the third trial in the nucleus reuniens, as well (Tuna et al., 2025). These findings suggest that trial-dependent learning dynamics may vary across thalamic nuclei rather than reflecting a uniform thalamic learning signal. Together, while our paradigm does not inherently distinguish between different stages of learning, such as early acquisition and stabilization, our findings are consistent with stronger associative learning-related engagement during the first two trials, with a reduced differential response by the third trial that may reflect the involvement of different neural processes.”

      Limitations (page 36):

      “The reduced CS+ vs. CS− differentiation observed in the pulvinar subdivisions during the third trial may reflect a transition from the rapid associative learning processes engaged during the first two trials to a different stage of threat processing. However, the present experimental design does not allow us to determine the specific psychological or neural mechanisms underlying this change. Importantly, this attenuation was not observed uniformly across thalamic nuclei, suggesting that it does not reflect a general thalamic response but may instead indicate nucleus-specific functional dynamics. Future studies specifically designed to dissociate different stages of threat learning will be required to determine the functional significance of this trial-dependent effect.”

      (3) Fig. 3 Could the observed network structure be due to anatomical proximity? Perhaps the authors should do an analogous analysis to what they did in Fig. 2 for this intra-pulvinar analysis. This analysis doesn't take into account the indirect connections through corticothalamic and thalamocortical connections with visual cortex and the pulvinar. There is an implicit assumption that there are interconnections between the pulvinar sub nuclei, but there are few strong excitatory projections between these sub nuclei to my knowledge. If visual areas are included in the graph, it would make things more complex, but would probably dramatically change the story. In this way, the message is somewhat constructed or arbitrary.

      We thank the reviewer for this thoughtful suggestion. We performed an analysis analogous to that presented in Figure 2. Specifically, we computed partial correlations between pulvinar divisions while controlling for activation in the other thalamic nuclei included in the study (LGN and MD). The relationships between pulvinar divisions remained significant after accounting for shared variance with these nuclei (Supplementary Figure 4), suggesting that the observed associations are not solely explained by activation in neighboring thalamic regions. This analysis is particularly relevant for the LGN because of its close anatomical proximity to the pulvinar and its central role within the visual thalamic system.

      Additionally, we statistically compared the strength of the partial correlations among all pairs of pulvinar divisions (Author response table 1). These analyses demonstrated substantial heterogeneity in the correlation strengths, with several pairwise differences remaining significant after FDR correction, indicating that the functional relationships among pulvinar divisions are heterogeneous rather than uniformly correlated, making a simple anatomical-proximity explanation less likely.

      Author response table 1.

      Pairwise comparisons demonstrate heterogeneous functional relationships among pulvinar subdivisions after controlling for MD and LGN activation.

      Note. All values are partial correlations controlling for MD and LGN activation (N = 293). Differences between correlations were tested using Steiger’s test for dependent correlations measured in the same participants. The sample size entered into the test was 293 - 2 = 291 as two variables (MD and LGN) were partialled out. The test itself then uses 291 - 3 = 288, the standard adjustment applied whenever correlations are converted to Fisher z scores. Steiger provides two versions of the same equation: one for comparisons in which the two correlations share a subdivision, and one for comparisons in which they share none (marked †). Analyses were conducted using the cocor package in R.

      The p-values for the 15 comparisons were corrected using the Benjamini-Hochberg false discovery rate (FDR) procedure; 9 of 15 comparisons remained significant after correction. Correlations ranged from 0.182 to 0.718. PuA = anterior pulvinar; PuI = inferior pulvinar; PuM = medial pulvinar; PuL = lateral pulvinar.

      The two correlations being compared share no subdivision.

      Finally, we agree that pulvinar function is embedded within broader corticothalamic and thalamocortical circuits involving visual cortical regions. However, a comprehensive characterization of pulvinar-visual cortical interactions at the level of specific pulvinar divisions was beyond the scope of the current study. To acknowledge this limitation and avoid implying that the observed relationships represent isolated direct interactions among pulvinar divisions, we revised the conceptual model in Fig. 8 by adding bidirectional dashed gray arrows between the pulvinar divisions and visual cortex (see Fig 8). Additionally, we clarified this point in the Figure notes and the study limitations:

      Limitations (page 36):

      “The observed relationships among pulvinar divisions during conditioning are purely functional and do not distinguish direct inter-nuclear interactions from indirect coupling mediated by corticothalamic and thalamocortical pathways, including visual cortical regions. Thus, the proposed functional pulvinar model may reflect indirect corticothalamic and thalamocortical loops, currently undocumented internuclear interactions, or a combination of these mechanisms.”

      (4) In the results section describing Fig. 4-7, there are no statistics supporting the claims made. There needs to be a set of graphs comparing the results across the study sessions and days, with statistical comparisons between the different experiments to confirm differences.

      We thank the reviewer for this thoughtful comment. As stated in the scope of the study (page 6 in the manuscript), our objective was to characterize thalamic activation and connectivity within each learning phase separately. Accordingly, our statistical analyses were designed to test CS+ vs. CS− differentiation within each phase rather than to directly compare activation or connectivity across phases (e.g., conditioning, extinction, extinction recall, and threat renewal).

      This phase-specific approach was selected because each learning phase probes a distinct psychological process with different experimental conditions. Therefore, direct comparisons of activation or connectivity between phases would address a different research question than the one investigated in the present study were not part of our predefined hypotheses or statistical design.

      To address the reviewer’s concern, we carefully revised the Results and Discussion to make this analytical framework explicit and to avoid wording that could be interpreted as implying direct statistical comparisons between learning phases. Representative examples of revisions made throughout the manuscript to clarify that the statistical analyses and interpretations are phase-specific (CS+ vs. CS− within each phase) and do not involve direct statistical comparisons across learning phases.

      Representative examples of these revisions are shown below:

      Page 17: “Pulvinar divisions and MD show engagement during extinction learning and context-dependent threat memory processing.”

      Page 21: “The threat renewal phase, in which participants were exposed to contextual cues similar to those used during threat conditioning, was associated with.”

      Page 23: “At the block level, activation was greater for CS+ than CS− within each phase separately: conditioning…”

      Page 23: “Collectively, these findings suggest that the LGN exhibited early trial-dependent responses within each learning phase separately, consistent with its proposed role in feedforward visual processing.”

      Page 28: “Figure 8b title: Conceptual model of thalamic-dependent ‘toggle switching’ between safe and threat memory retrieval across contextual cues”

      “Legend: (b) Conceptual model illustrating a possible thalamic-dependent “toggle switch” underlying context-dependent safety and threat memory expression. The observed MDdACC and anterior pulvinar-vmPFC connectivity patterns are consistent with possible preferential engagement of prefrontal circuits during extinction recall and threat renewal, respectively. This framework represents a theoretical integration of the present findings rather than evidence of causal neural mechanisms. It is based on the findings observed within each phase separately and should not be interpreted as a direct comparison between phases.”

      Page 25: “Interestingly, within each phase separately, the findings suggest that thalamic connectivity patterns vary with contextual conditions during extinction recall and threat renewal. Specifically, the MD and anterior pulvinar showed distinct CS+E vs. CS− connectivity patterns during these phases, respectively.”

      (5) FIg. 7 does not include the major corticothalamic and thalamocortical projections from early, mid-level, and higher visual cortex to the different pulvinar nuclei. I doubt that there are strong direct projections between the pulvinar nuclei, rather the functional connections are probably mediated through interconnections with cortical visual areas.

      Thank you for pointing out this important point. As described in our response to Weakness 3 above, we agree that pulvinar function is embedded within broader corticothalamic and thalamocortical circuits involving visual cortical regions. To better acknowledge this, we revised the conceptual model by adding bidirectional dashed gray arrows between the pulvinar and visual cortex and retained a note in the figure legend clarifying that the schematic is not intended to represent a comprehensive anatomical connectivity map. We also emphasize in the manuscript that the proposed intrapulvinar relationships should be interpreted as a functional/computational model based on statistical dependencies rather than evidence of direct monosynaptic anatomical connections. An updated version of the figure is provided. See Fig 8.

      (6) Stylistic: There are a lot of hypotheses and interpretations presented in this primary literature paper which may be better suited for a review or perspective piece.

      Thank you for this comment. Our intention here is to integrate the empirical findings within an existing conceptual framework rather than present isolated observations. We believe that placing our results in the context of current models helps highlight their potential implications while remaining grounded in the experimental data. Nevertheless, we reviewed the Discussion again and ensured that speculative statements are clearly identified as hypotheses or possible interpretations and are appropriately qualified throughout the manuscript.

      (7) In the discussion there is an assumption that the fMRI BOLD responses to CS+ and CS- need to be different to indicate that an area is processing these distinctly, but the BOLD signal can only detect large scale changes in overall activity. It's easy to imagine that an area could be involved in processing these two stimuli distinctly without showing an overall difference in the gross amount of activity.

      Thank you for raising this important limitation. We agree that the absence of differential BOLD responses does not necessarily imply the absence of stimulus-specific neural processing. We explicitly acknowledged this limitation in the manuscript (page 35):

      “Although our findings suggest distinct patterns of thalamic involvement during threat learning, fMRI cannot fully capture the complexity of thalamic organization. Pulvinar divisions, MD, and LGN each contain diverse neuronal subtypes and finer anatomical subdivisions that may serve distinct functions. Importantly, the absence of CS+ vs. CS− differences in BOLD activation should not be interpreted as a lack of stimulus-specific processing, as such distinctions may occur without detectable changes in overall BOLD activation…”

      We reviewed this section again and believe it appropriately addresses the limitation raised by the reviewer.

      (8) There is strong evidence that the BOLD responses to the threat-related and safety-related stimuli are different, modest evidence for their claims of learning/plasticity in these pathways, and circumstantial evidence supporting their hypothesized graph network models. Overall most of the claims made in the discussion are better considered possible interpretations rather than proven findings - this is not a criticism, as these experiments and subject matter are extremely complex.

      We thank the reviewer for this thoughtful perspective. We agree that our findings provide varying levels of evidence across different aspects of the study and that the proposed network models should be interpreted as hypotheses informed by our empirical observations rather than definitive mechanistic conclusions. Accordingly, throughout the current revisions, we have carefully revised the Results and Discussion sections to distinguish empirical findings from interpretations by using more cautious language and explicitly acknowledging the limitations of our experimental approach. All revisions are in the manuscript, and representative examples of the changes can be found above.

      (9) This study continues to validate the power and utility of this in human fear conditioning/extinction paradigm, and extends this paradigm to investigating fear learning beyond the traditional limbic system pathways. It's possible that their models for the pulvinar nuclei interconnections could guide future neuromodulation or DBS studies that could provide more causal evidence for their hypotheses.

      We thank the reviewer for these encouraging comments and for recognizing the potential utility of this paradigm and the possible implications of our findings for future mechanistic and neuromodulation studies.

      Comments on revisions:

      The reviewers addressed my major concerns appropriately in the modified manuscript. As long as the MRI analysis concerns of Reviewer 3 are satisfied (MRI analysis is not my expertise), I am satisfied with the modified manuscript.

      We sincerely thank the reviewer for the positive assessment of our revised manuscript and for recognizing that the major concerns were appropriately addressed. We appreciate the reviewer's constructive feedback throughout the review process, which has helped improve the quality and clarity of the manuscript.

      Reviewer #3 (Public review):

      Summary:

      The present work was aimed at investigating the specific contributions of thalamic nuclei to associative threat learning and extinction. Using fMRI, it examined activation patterns across pulvinar divisions, the lateral geniculate nucleus (LGN), and the mediodorsal thalamus (MD) during threat acquisition, extinction, and recall. It goals was to uncover whether distinct thalamic systems support different modes of learning-automatic survival mechanisms versus more deliberate processes-and to propose a hierarchical pulvinar model of fear conditioning. The manuscript also tried to refine current neuroanatomical models of threat learning and memory, highlighting the role of thalamic nuclei in it.

      We thank the reviewer for this accurate summary of the aims and scope of our study. We also appreciate the thoughtful and constructive feedback provided throughout the review process, which has helped us improve the methodological description, interpretation of the findings, and overall clarity of the manuscript. Below, we respond to each of the points raised under the Weaknesses and Recommendations sections.

      Strengths:

      (1) Valuable theoretical elaboration and modeling regarding the differential role of pulvinar subdivisions on feedforward (inferior, lateral) and higher-order integration (anterior), and their functional interplay with other relevant subcortical and cortical structures in associative threat and extinction learning.

      (2) Large sample sizes and multipronged analytical approaches were used for hypothesis testing.

      (3) Exhaustive literature review in the field of associative threat, as well as regarding the role of thalamic nuclei and other brain structures in it.

      Weaknesses:

      (1) The manuscript has improved methodologically and analytically after the review. Several weaknesses remain, in my opinion, but still findings are valuable and the evidence can be considered as convincing.

      (a) fMRI data have low resolution (3 cubic mm), which certainly limits the examination of small nuclei such as the ones investigated here, and especially the examination of the LGN and inferior pulvinar.

      Thank you! We have acknowledged this limitation in the manuscript (page 35):

      “Pulvinar divisions, MD, and LGN each contain diverse neuronal subtypes and finer anatomical subdivisions that may serve distinct functions. Importantly, the absence of CS+ versus CS− differences in BOLD activation should not be interpreted as a lack of stimulus-specific processing, as such distinctions may occur without detectable changes in overall BOLD activation. Future advances in higher-resolution imaging and human brain atlases may further improve anatomical and functional precision.”

      (b) fMRI was normalized to standard space. Analyzing the data in individual-subject space would have given you the options of avoiding altering every participant's brain and of using more precise atlases than the normalized AAL for ROI selection.

      We thank the reviewer for this thoughtful suggestion. Analyses performed in native subject space and standardized MNI space each have methodological advantages. In the present study, we adopted a standardized MNI-space pipeline because it provides consistent anatomical localization and ROI definition across participants, facilitating group-level analyses and comparisons across individuals. We have added this consideration to the Limitations section (page 35).

      “The present analyses were performed in standardized MNI space to enable consistent group-level analyses and ROI definition across participants. Although this is a widely accepted approach in human neuroimaging, future studies may examine the generalizability of the present findings using complementary approaches, including analyses performed in native subject space.”

      (c) Motion during scanning was poorly controlled. Including the motion parameters as covariates of no interest in the GLM/analysis does not fully guarantee that motion is not influencing the results, and that motion is not differentially influencing some experimental conditions more than others.

      We thank the reviewer for highlighting the importance of controlling for head motion in fMRI analyses. We agree and acknowledge that no preprocessing strategy can completely eliminate all potential residual motion-related effects in fMRI data.

      For the activation analyses, the data were preprocessed using the standard fMRIPrep (v20.0.2) pipeline, which included motion correction through rigid-body realignment prior to statistical modeling. The first-level SPM analyses included the six estimated head-motion parameters (three translations and three rotations) as nuisance regressors. White matter and cerebrospinal fluid signals were also included as nuisance regressors to reduce non-neuronal sources of variance.

      For the functional connectivity analyses, we applied CONN’s denoising pipeline, which included regression of motion parameters, regression of identified outlier scans (scrubbing), component-based physiological noise correction (CompCor), and temporal filtering prior to generalized psychophysiological interaction (gPPI) analyses. The combination of motion correction, nuisance regression, and additional denoising procedures, provides a multistep approach to reducing potential motion-related and non-neuronal confounds in the reported findings. We have further clarified these processes in the manuscript (pages 44-45 in the manuscript):

      “Functional connectivity was computed using the CONN toolbox (version 22.a) for MATLAB (NietoCastanon and Whitfield-Gabrieli, 2022; Whitfield-Gabrieli and Nieto-Castanon, 2012). Anatomical images were segmented into gray matter, white matter, and CSF. Functional images were preprocessed following CONN’s default pipeline, including realignment, slice-timing correction, and coregistration. Functional images were then denoised using a component-based noise correction approach (CompCor), including regression of estimated motion parameters, regression of identified outlier scans using artifact detection procedures (scrubbing), and regression of white matter and CSF signals. The denoised BOLD time series were subsequently band-pass filtered between 0.008 and 0.09 Hz.

      Following these denoising procedures – including regression of motion parameters, artifact-related outlier scans (scrubbing), physiological noise correction (CompCor), and temporal filtering – condition-dependent connectivity effects were inferred from subject-level generalized psychophysiological interaction (gPPI) contrast estimates rather than from raw time-series correlations…”

      Recommendations for the authors:

      Reviewer #3 (Recommendations for the authors):

      (1) Shock methods: how long was the shock? Which electrical stimulator was used? Where were the shock electrodes placed? Was gel used?

      Thank you for pointing this out. The duration of the electrical stimulation was already specified in the manuscript. In the current revision, we have further clarified the shock delivery procedure by adding details regarding the stimulation system, electrodes, use of conductive gel, and electrode placement. These details have now been added to the Experimental Procedures section (page 40):

      “…Electrical stimulation was delivered using a BIOPAC stimulation system with BIOPAC electrodes and conductive gel. The electrodes were attached to the palm of the participant's right hand and positioned in close proximity without making contact with one another. The stimulation began…”

      (2) Fig. 3G: needs details about the independent sample. Was this cohort held out for cross-validation? etc.

      Thank you for raising this point. We added this information to Fig. 3 notes and to the results section.

      Fig. 3 notes:

      “(g) Replication of the mediation model in an independent sample. This independent cohort (N = 114) was collected as part of a separate research project that included the same Day 1 fear-conditioning paradigm used in the present study. The cohort was used to assess whether the mediation findings could be replicated independently.”

      Results (page 15):

      “...we applied the mediation analysis to an independent cohort (N = 114) collected as part of a separate research project using the same Day 1 fear-conditioning paradigm. The mediation findings were largely replicated in this independent cohort (Fig. 3f-3g).”

    1. Author response:

      The following is the authors’ response to the original reviews.

      eLife Assessment:

      This important study provides solid novel evidence for a role of ripples in the hippocampus in visual short-term memory. The work is strong in employing state-of-the-art intracranial electrophysiology in epilepsy patients with multivariate pattern classifiers in the context of an elegant experiment, but several aspects of the theoretical framing, mechanistic interpretation, and analysis strategy are incomplete.

      We thank the editors and reviewers for their positive evaluation of our study and for their constructive comments. In this revision, we have substantially revised the manuscript in the following three aspects:

      First, we have revised the Introduction to better motivate our central hypothesis and expanded our Discussion based on the additional analyses that were performed during this revision, to better interpret our results and highlight our main theoretical contribution to memory and the dynamic coding framework.

      Second, we have strengthened the rigor of our findings by performing several control analyses, including ripple validation, Region × Time × Memory interaction tests, and further characterization of temporal dynamics for coupled hippocampal-LTL ripples and coupled ripple-locked memory reactivation over the maintenance period.

      Third, we have clarified key experimental and analytical details in the Methods and have better illustrated the results following reviewers’ suggestions.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      Cai et al. investigated the role of ripples in the hippocampus and coupled between the hippocampus and the neocortex in visual short-term memory (VSTM) using a similar lures match-to-sample task. The main findings are that hippocampal, but not neocortical ripples, ramp up during the maintenance period, peaking shortly before the memory response is given. This ramping-up effect was stronger for correct compared to incorrect trials. Furthermore, the authors show that stimulus category could be better decoded during coupled hippocampo-neocortical ripples compared to uncoupled ripples. These results provide compelling novel evidence for a role of ripples in supporting human visual short-term memory.

      Strengths:

      (1) State-of-the-art intracranial EEG in 13 patients during a well-designed visual short-term memory task, with simultaneous hippocampal and neocortical recordings.

      (2) Thorough analysis pipeline with validation to detect ripple events, and distinguish them from spurious ripple activity (i.e., as induced by IEDs).

      (3) Use of multivariate classifiers to resolve the neural representation of the stimuli.

      Weaknesses:

      It is difficult to find clear weaknesses in this paper, as the analyses are thorough, the results are clear, and the writing is excellent. However, some more sanity checks on the validity of ripples could have been conducted (i.e., making sure that ripple events have multiple peaks in the unfiltered raw signal at the ripple frequency). Also, the time window for coupled ripples appears to be a bit long, which makes it questionable to what degree these ripples are coupled (i.e., the time window is ~5 times longer than the duration of a ripple event). Lastly, the ramping-up effect could have been more clearly depicted in the figures, but that's a fairly minor point.

      We sincerely thank the reviewer for their positive assessment and constructive suggestions to further improve our manuscript.

      First, following the reviewer’s suggestion, we performed a validity check on the detected ripples using the unfiltered raw signal. For each detected ripple, we identified the local voltage peaks within the event duration in the raw data and calculated the corresponding Inter-Peak Intervals (IPIs). To assess the consistency of these oscillatory structures across the dataset, we generated individual IPI histograms for each of the 13 subjects. Across all participants, an average of 89.84 ± 3.31% of the calculated IPIs fell within the expected 70-180 Hz ripple frequency band. This concentrated distribution of IPIs supports the reviewer’s claim that true ripple events manifest as multi-peak oscillatory waveforms in the raw trace whose IPIs should roughly correspond to the targeted ripple frequency range. We have incorporated these findings into Results (Page 6) and shown them as Supplementary Figure S1a.

      Second, regarding the temporal windows used for quantifying coupled ripples, we apologize that our terminology conflated two distinct analyses and have explicitly clarified this distinction in the revised manuscript: (1) for the analysis in Figure 4b (i.e., Lateral Temporal Lobe (LTL) Ripple Rate Locked to HPC ripple peak), we initial computed the LTL ripple rate within a broad time window (i.e., [-0.5 s, 0.5 s]) centered on Hippocampal (HPC) ripple peaks (Dickey et al., 2022). This broad window was employed to examine the lead-lag or directionality between ripples of these two regions. We agree that labeling this as “coupled ripples” in the original text is misleading. In the revised manuscript, we have changed the y-axis label of Figure 4b into “Normalized LTL ripple rate (z-score)”. (2) For the coupled ripple and the coupled ripple locked decoding analyses (Figure 4c and Figure 5), “coupled ripples” were defined as LTL ripples that temporally overlapped with or occurred within ± 50 ms of an HPC ripple peak following previous research (Vaz et al., 2019). We compared the coupled ripple rates between VSTM remembered versus forgotten trials. The results revealed significantly higher coupled ripple rates in remembered trials compared to forgotten trials during maintenance (t(12) = 2.897, p<sub>FDR</sub> = 0.040; Fig. 4c). We have revised the corresponding text in both the Results and Methods sections (Pages 9-10 and Page 24) to clearly separate these two analyses and ensure that the term “coupled ripples” is reserved exclusively for LTL ripple events within the ± 50 ms of the HPC ripple peak.

      Third, we have revised Figure 2b to provide a clearer and more intuitive depiction of the hippocampal ripple ramping-up effect.

      Reviewer #2 (Public review):

      Summary:

      Liu et al. record intracranial EEG from the hippocampus and lateral temporal lobe in thirteen neurosurgical patients while they perform a delayed match-to-sample visual short-term memory task. The central question is whether hippocampal sharp-wave ripples (brief high-frequency oscillations well established in the long-term memory consolidation literature) also contribute to the active maintenance of visual representations over a short delay. The authors report three main findings: hippocampal ripple rates progressively ramp up across the 7-second maintenance period, hippocampal ripples temporally co-occur with ripples in the lateral temporal lobe, and these coupled events coincide with above-chance category-level decoding of the memorized stimulus in the lateral temporal lobe. The findings are interpreted within the dynamic coding framework of working memory, which predicts discrete reactivation bursts rather than sustained firing during maintenance. The question is timely, and the use of intracranial recordings affords a level of temporal and spatial resolution unavailable to non-invasive methods.

      Strengths:

      The study addresses a genuinely important and underexplored question: whether a neural mechanism best characterized in the context of offline memory consolidation is also engaged during active online maintenance. The use of intracranial recordings in humans is well suited to this question, providing the millisecond temporal resolution and regional specificity needed to detect transient high-frequency events. The dissociation from long-term memory, tested by splitting remembered trials according to whether the item was later recalled in a cued-recall test, directly addresses what would otherwise be a significant confound, and the finding that ripple dynamics during maintenance are unrelated to subsequent long-term memory performance adds specificity to the interpretation. The coupled ripple analysis is methodologically grounded, and the finding that coupled but not isolated ripples coincide with elevated memory decoding is mechanistically informative. The multivariate decoding approach applied to lateral temporal lobe spectral power provides a meaningful index of memory reactivation that goes beyond simple univariate rate measures. The control analysis and the alternative ripple detection method provide useful robustness checks. The public availability of preprocessed data and analysis code on OSF is commendable.

      We are grateful that the reviewer highlighted the importance and novelty of our findings. Below, we address the specific considerations and weaknesses raised by the reviewer.

      Weaknesses:

      (1) Theoretical motivation for examining ripples in visual short-term memory.

      A fundamental question that the paper does not adequately address is why hippocampal ripples, a mechanism strongly associated with offline memory consolidation during sleep, where they coordinate the transfer of hippocampal representations to cortex through temporally compressed replay, should be recruited for the online maintenance of visual information over a seconds-long delay. The Introduction acknowledges this gap but does not close it. The dynamic coding framework is used to motivate the ramping-up prediction, but this framework is agnostic about the specific neural mechanism responsible for reactivation bursts. In particular, the literature cited by the authors predicts high-frequency population activity or gamma bursts, but not specifically hippocampal ripples. The reasoning that "ripples share key properties with postulated reactivation bursts" risks being circular: it amounts to saying that ripples could be the relevant mechanism because the relevant mechanism has properties that ripples also have. A stronger theoretical motivation would require either evidence that the replay or reactivation computations that ripples support during offline states are also engaged during active short-term maintenance, or a mechanistic account of how the circuit processes underlying ripple generation are recruited differently across these two contexts.

      We thank the reviewer for raising this important point. We agree that the theoretical motivation for examining hippocampal ripples in visual short-term memory (VSTM) needs to be stated more explicitly. In the revision, we have reorganized the Introduction with the following structure (for the comprehensive revised Introduction, please see Pages 3-4):

      First, we review evidence that the hippocampus is involved in VSTM, including both lesion studies and neural representational studies. These findings converge to suggest that the hippocampus contributes to maintaining visual information over short delays.

      Second, we introduce hippocampal ripples as a key candidate mechanism based on the following lines of evidence: (1) While hippocampal (HPC) ripples have been traditionally linked to offline processing of long-term memory (LTM), more recent evidence indicates that they also contribute to online memory processing, including LTM encoding, retrieval, and most critically, the short-term maintenance period. (2) HPC ripples and their coordinated neocortical memory reactivation have been frequently observed during LTM consolidation and retrieval. Given that VSTM and LTM have been proposed to share neural mechanisms, it is reasonable to hypothesize that the hippocampal ripples and their coordinated memory reactivation contribute to VSTM maintenance. In this revision, this part has been revised as follows:

      “A key candidate mechanism is the hippocampal ripple, a brief high-frequency (~80-170 Hz) oscillation that reflects synchronized activity of neuronal ensembles in the hippocampus (Buzsáki, 2015; Iwata et al., 2024; Norman et al., 2019). Traditionally, hippocampal sharp-wave ripples have been recognized for their role in offline memory consolidation during sleep and quiet awake rest, during which they are temporally coordinated with neocortical memory replay/reactivation via hippocampal-neocortical communication (Eschenko et al., 2008; Schreiner et al., 2024; Zhang et al., 2024, 2018). Recent studies, however, indicate that ripples also actively support online memory processing. In human long-term memory (LTM) studies, ripple rates during encoding and pre-retrieval intervals predict subsequent LTM performance, and temporally coordinate the reinstatement of neocortical representations during successful retrieval (Kunz et al., 2024; Norman et al., 2019; Sakon and Kahana, 2022; Vaz et al., 2019; Zhang et al., 2024). Beyond LTM, rodent studies have revealed that selectively disrupting hippocampal ripples during awake learning periods impaired the working memory-dependent spatial navigation performance (Jadhav et al., 2012; Zhang et al., 2021), pointing to a vital role for ripples in sustaining online short-term memory representations. Moreover, VSTM and LTM could recruit overlapping hippocampal-neocortical networks (Cowan, 2019; Ranganath and Blumenfeld, 2005), especially when the VSTM task is demanding or engaging feature binding (Hannula et al., 2006; Jeneson et al., 2012; Jeneson and Squire, 2012; Pertzov et al., 2013). These findings together raise a fundamental question: Do hippocampal ripples, long implicated in LTM formation and offline consolidation, also actively support human VSTM maintenance?”

      Third, following the reviewer’s suggestion, we state that hippocampal ripples share key properties postulated for bursts; we hypothesized that hippocampal ripple rates would exhibit a progressive temporal ramping pattern as postulated for bursts across the VSTM maintenance interval in accordance with the dynamic coding framework.

      Finally, we emphasize the importance of HPC-neocortical communications in memory processing and propose a potentially coupled ripple mechanism for the interactions between the HPC and the lateral temporal lobe (LTL).

      This concern is compounded by what the authors present as one of their main controls. The finding that ripple dynamics during maintenance are not associated with subsequent long-term memory performance is treated as a reassurance that the observed effects are specific to short-term memory. But if ripples are canonically a long-term memory consolidation mechanism, the observation that they are engaged by a short-term memory task while appearing disengaged from concurrent long-term memory encoding is itself a finding that demands explanation. Resolving this tension is important for the paper's contribution to be correctly interpreted by the field.

      We thank the reviewer for raising this important concern. In this revision, we clarify that this null effect should not be simply interpreted as evidence that ripples are generally disengaged from LTM, nor as contradicting previous findings on ripple contributions to LTM. Rather, our results indicate that the ramping-up hippocampal ripples were primarily attributed to online maintenance of VSTM. However, this online maintenance may not be the determining factor for subsequent LTM performance.

      This interpretation is based on the evidence that hippocampal ripples contributing to LTM are most evident during offline consolidation windows, including sleep and post-encoding awake rest, rather than during online task execution. For instance, event-contingent suppression of post-learning sleep ripples impairs subsequent spatial memory in rodents (Girardeau et al., 2009). Consistently, in humans, ripple-coupled replay during NREM sleep has been shown to predict later memory success more reliably than replay measured across wakefulness (Zhang et al., 2018); more recent work further suggests that, post-encoding awake-rest ripple activity, rather than encoding-period ripple activity, is associated with subsequent memory performance (Zhang et al., 2024).

      Moreover, the cued-recall long-term memory test in the current study was performed after both an interference task and a 1-4 minute rest period. Therefore, the LTM performance likely depends on multiple processes beyond VSTM maintenance, such as resistance to interference, awake rest-related replay or fast consolidation, and retrieval success. Thus, it is possible that ripple activity during the VSTM delay alone may not be sufficient to predict later LTM performance. In this revision, we have also added more details for the LTM task in Methods (Page 19) and the interpretation of our results in Discussion (Page 17):

      “Following the completion of each VSTM run, participants performed a 1-minute mathematical countback task, followed by a brief rest period (1-4 min) before the LTM cued-recall test. During each LTM test run, 14 learned, unique cue-picture pairs were tested in a randomized order, with each pair tested only once. There are, on average, 88.31 ± 19.28 trials per participant. For each trial, participants first performed a self-paced, binary keypress to indicate subjective retrieval success (“remember” vs. “don’t remember”). Upon a subjective “remember” response, an objective category verification prompt was presented for a maximum of 3 s, requiring a 4-alternative forced-choice response to identify the semantic category of the associated target picture (animals, electronics, fruits, or furniture). Trials were operationally classified as LTM “remembered” trials only if the subjective recall was accompanied by a correct objective category verification. Trials receiving a “don’t remember” response or an incorrect category report were classified as LTM “forgotten” trials.” (Page 19)

      “Notably, the absence of the hippocampal ramping-up effect during maintenance in predicting LTM does not conflict with the established role of hippocampal ripples in long-term memory. Converging evidence suggests that ripple contributions to LTM are most evident during offline consolidation windows, including sleep and post-encoding rest, rather than during online task execution. In rodents, suppressing post-learning sleep ripples impairs subsequent memory (Girardeau et al., 2009). In humans, ripple-coupled replay during NREM sleep predicts later memory success (Zhang et al., 2018), and post-encoding awake-rest ripple activity, rather than encoding-period activity, is associated with subsequent memory performance (Zhang et al., 2024). Thus, the lack of association between VSTM-delay ripples and later cued recall raises a possibility: ramping-up ripple dynamics during active maintenance may support online VSTM, whereas LTM formation may depend more on ripple events occurring during post-encoding time windows. Our study cannot rule out the possibility that any relationship between VSTM delay-period ripples and later LTM was obscured by intervening processes between maintenance and recall, including interference resistance, offline consolidation during rest, and retrieval-related factors. Future studies incorporating parametric manipulations, such as varying memory load, delay duration, or lure similarity, will be essential to directly test whether hippocampal ripple activity selectively scales with VSTM demands, thereby providing stronger evidence for its specific role in online maintenance versus LTM-related processes.” (Pages 17-18)

      (2) Ripple detection and specificity.

      Even granting that ripples could in principle contribute to short-term memory maintenance, the study does not establish that the detected events are physiological sharp-wave ripples rather than broadband high-frequency activity. The detection band (70-180 Hz) substantially overlaps with the high-gamma range, which is a well-established proxy for local neural population activity and coding, and is broader than the 80-120 Hz band used by several of the cited papers, including Vaz et al. (2019), Ngo et al. (2020), Chen et al. (2021), Staresina et al. (2023), and Kunz et al. (2024). Without demonstrating that detected events have the hallmark features of physiological sharp-wave ripples, a clear narrowband spectral peak, and characteristic waveform morphology, it is difficult to conclude that the observed effects reflect a ripple-specific mechanism rather than a more general high-frequency population activity phenomenon. The reported mean rate of 0.29 Hz is somewhat higher than rates reported in some recent work, such as Chen et al. (2021, ref 74) and Kunz et al. (2024, ref 15). It is worth noting that van Schalkwijk and Helfrich (2026, Nature Communications) demonstrated that a large proportion of awake ripple detections in the human medial temporal lobe reflect false positives arising from aperiodic 1/f noise, with task-related modulations of this noise floor producing spurious detections. The authors present an 80-120 Hz control analysis as a robustness check, but this inverts the appropriate logic: if 80-120 Hz is the more validated band, as the cited literature suggests, it should serve as the primary analysis rather than a supplementary one.

      We thank the reviewer for raising these important concerns and agree with the reviewer that validating ripples is paramount. To address these concerns, we have performed two major validation analyses.

      First, to confirm that the detected events reflect genuine, multi-peak ripples, we conducted a validity check on the unfiltered raw data. As suggested by Reviewer 1, if genuine ripples are present in the raw data, the inter-peak interval (IPI) should roughly correspond to the ripple frequency. Our results show that across all participants, an average of 89.84 ± 3.31% of the calculated IPIs using unfiltered raw data fell within the expected 70-180 Hz ripple frequency band, confirming the physiological nature of ripples (see also our response to Reviewer 1 on Pages 2-3 of this response letter). We have added these results in the revised Results section (Page 6) and Supplementary Figure S1b.

      Moreover, to the best of our knowledge, there is no universal consensus on the exact frequency band for human ripple detection. Although some human iEEG studies use narrower bands, such as 80-120Hz (as noted by the reviewer) or 80-150 Hz (Liu et al., 2022), our use of a broader band, 70-180 Hz, follows established human iEEG protocols (Norman et al., 2021, Neuron) and this broader band of ripples has also been adopted in substantial number of recent human iEEG studies (e.g., He et al., 2026, Nature Neuroscience; Iwata et al., 2024, Nature Communications; Xiao et al., 2025, Neuron). Importantly, as the reviewer noted, our control analyses using alternative detection criteria, including an 80-120 Hz band and different duration thresholds, yielded the same pattern of results. Thus, our main conclusions were not dependent on the specific ripple-band definition or duration threshold used for event detection.

      Second, we agree that ruling out the possibility that the observed ripple-rate ramping and the memory performance differences reflect fluctuations in the aperiodic 1/f background is critical. We quantified the aperiodic slope throughout the maintenance period using the method described by van Schalkwijk and Helfrich, (2026), following the reviewer’s suggestion. We modeled the ramping-up effect of the aperiodic slope, and the results revealed that the aperiodic slope showed no significant change over time (p > 0.600, see Author response image 1) and did not differ between remembered and forgotten trials (p = 0.544). These results indicate that background 1/f dynamics cannot account for either the temporal ramping of the hippocampal ripple rate or the ramping-up difference between remembered vs. forgotten trials.

      Author response image 1.

      No significant ramping-up effect of aperiodic activity during VSTM maintenance.

      (3) Internal inconsistency with the dynamic coding framework.

      The authors invoke the dynamic coding framework, which predicts that reactivation bursts should ramp up toward the end of the retention interval in the region where memory representations are actively maintained. The hippocampal ramping-up result is presented as confirming this prediction. However, the lateral temporal lobe, the region where above-chance category decoding is found and memory reactivation is attributed, shows no corresponding ramping-up. The authors acknowledge this asymmetry but do not offer a mechanistically satisfying explanation, and the suggestion that the effect might exist in unsampled subregions cannot be evaluated with the current data. This leaves the framework's core prediction unconfirmed in the region that is claimed to maintain the representations.

      We thank the reviewer for raising this important point.

      Regarding the absence of an overall LTL ripple ramping-up, following the reviewer’s suggestion (see also the next relevant comment #4), we performed an additional analysis separating LTL ripples that were temporally coupled with hippocampal ripples from LTL ripples that occurred independently (uncoupled) among remembered trials. We found a non-significant, positive numerical trend for LTL ripples that coupled to HPC ripples (β = 0.032, p = 0.126), whereas uncoupled LTL ripples showed a significant decrease over the maintenance period (β = -0.014, p = 0.026), with the interaction effect showing a non-significant trend of greater ramping-up for coupled versus uncoupled LTL ripples (β = 0.031, p = 0.088, see Supplementary Figure S10). These results suggest that although overall LTL ripple activity did not show a significant ramping-up, the subset of LTL ripples temporally coupled with hippocampal ripples exhibited a trend consistent with the hippocampal ramping pattern. In addition, the absence of the overall LTL ripple ramping-up may also be shaped by broader cortical inputs rather than by the HPC alone. For instance, prior work suggests that LTL activity can be strongly influenced by inputs from other cortical areas, including prefrontal and parietal regions (Axmacher et al., 2008; Hirabayashi et al., 2024; Xu, 2023). Such circuit-level differences may also give rise to distinct temporal dynamics in the LTL from those in the HPC.

      In this revision, we have carefully discussed the null effect for the LTL ripples and the potential mechanisms underlying the asymmetry between hippocampus and LTL (Page 15):

      “Despite the observed HPC-LTL coupled ripples and the role of LTL in representing VSTM content, we found the LTL ripple rates did not ramp over the maintenance. This absence of ripple ramping-up in the LTL channels cannot be attributed to greater ripple heterogeneity since controlling the ripple-rate variability did not affect the results (Fig. S5). There are at least two possibilities: First, hippocampal ripple coupling selectively influence a subset of LTL ripple events, given the coupled ripples showing a ramping-up trend, while uncoupled ripple decreasing overing the maintenance period (see Fig. S10); Second, LTL ripple dynamics are shaped by broader cortical inputs beyond hippocampal coupling alone, as prior work indicates that LTL activity can be strongly influenced by prefrontal and parietal inputs (Axmacher et al., 2008; Hirabayashi et al., 2024; Xu, 2023). Moreover, the absence of LTL ramping-up does not necessarily contradict the dynamic coding framework, as the region maintaining decodable content and the region exhibiting ramping dynamics may differ yet interact to support VSTM maintenance. Due to electrode coverage limitations, we cannot evaluate other key cortical areas, such as the frontal or parietal cortex, where VSTM information is traditionally maintained (Bettencourt and Xu, 2016; Kamiński et al., 2017). To further test these possibilities, future studies with broader cortical sampling and higher ripple counts will be necessary.”

      (4) Coupled ripples, directionality of hippocampal-lateral temporal coupling, and the ramping-up paradox. The conclusion that coupled hippocampal-lateral temporal ripples coordinate memory reactivation creates a logical tension that the paper does not resolve. If hippocampal ripples drive lateral temporal reactivation only when co-occurring with lateral temporal ripples, and hippocampal ripples ramp up in a memory-predictive fashion, then the absence of lateral temporal ripple ramping up implies that the hippocampal ramping-up is not primarily expressed through the coupled ripple mechanism, undermining the coherence of the two main findings.

      The coupled ripple analysis further quantifies only temporal co-occurrence and provides no evidence about the direction of influence. Without demonstrating that hippocampal ripples systematically precede lateral temporal ripples (i.e., the expected signature of hippocampus-to-cortex information flow), the central claim that hippocampal ripples drive lateral temporal reactivation remains an interpretive assumption. Directly testing whether lateral temporal ripples specifically coupled to hippocampal ripples show a ramping temporal profile during maintenance (even if overall lateral temporal ripple rates do not) is necessary to establish whether the lateral temporal lobe engages in hippocampally-gated reactivation bursts in the manner the framework predicts. Additionally, reporting the distribution of peak lags between hippocampal and lateral temporal ripple peaks, and testing whether hippocampal ripples systematically precede lateral temporal ripples, is similarly necessary to support the directional interpretation.

      We thank the reviewer for these constructive comments. Regarding the “ramping-up paradox”, please see our detailed response to your comment #3 above.

      Regarding the directionality of coupling, we computed the peak-to-peak lag between coupled LTL and HPC ripple events (defined as co-occurrence within ± 50 ms). For remembered trials, no significant difference between LTL and HPC ripple peaks for the coupled ripples in any task stage (ps<sub>FDR</sub> > 0.069, see figure 2). We have included this analysis in the updated Results (Page 10).

      For the interpretation of the absence of temporal lag between HPC and LTL ripples during the maintenance period, recent evidence has shown that ripples in different brain areas often co-occur with near-zero phase lag, providing a temporally precise mechanism for efficient inter-regional communication (Verzhbinsky et al., 2024). Such synchronous coupled ripples may reflect a shared or rapidly reciprocal interaction between hippocampus and neocortex, rather than a unidirectional drive. We have revised the Discussion to avoid any claim that hippocampal ripples “drive” lateral temporal reactivation, and leave it as an open question for future studies using neural modulation or other causal approaches (Page 14):

      “However, our ripple peak lag analysis revealed little evidence regarding the directionality of coupled ripples during the maintenance period. Recent evidence shows that ripples in different brain areas often co-occur with near-zero phase lag, providing a temporally precise mechanism for efficient inter-regional communication (Verzhbinsky et al., 2024). Such synchronous coupled ripples may reflect a shared or rapidly reciprocal activation between hippocampus and neocortex, rather than a unidirectional drive. Although the absence of significant directionality does not necessarily undermine the functional relevance of coupled ripples, it leaves the open question of whether hippocampal ripples actively gate cortical reactivation or merely co-occur with it. Future studies with directed connectivity manipulations or measures will be necessary to resolve this issue.”

      Author response image 2.

      The peak time lag between HPC and LTL ripples for the coupled ripples among remembered trials. Time 0 indicates the hippocampal ripple peak time. Each dot represents the mean peak time for each channel. For each epoch, the central solid horizontal line represents the group-level mean peak lag estimated from the linear mixed-effects model (LMM), flanked by the upper and lower horizontal lines indicating the corresponding 95% confidence intervals.

      (5) Trial-level analysis clarity.

      The paper reports that ripples occurred in 54%, 79%, and 27% of trials during encoding, maintenance, and retrieval, respectively, but does not state whether subsequent analyses were conducted on trials thresholded by ripple occurrence. Given that occurrence rates vary substantially across stages and conditions, this inclusion criterion has implications for interpreting rate differences and should be stated explicitly.

      We apologize for the lack of clarity regarding trial inclusion across our analyses. In the revised manuscript, we have now explicitly reported the trial inclusion for each analysis in the Methods. Specifically, for the analysis of stage-averaged ripple rates (Figure 2c & e) and the ripple ramping-up analysis (Figure 3), all trials were included. This inclusion of all trials was necessary for the contrasts to maintain a consistent trial number and baseline across all stages (Pages 6 and 8). However, for the coupled ripple, the analyses were restricted exclusively to trials in which the ripples occurred (Page 9).

      To confirm that the inclusion of all trials did not skew our temporal ramping results, we performed a control analysis restricted exclusively to trials in which at least one hippocampal ripple was detected during the 7-second maintenance period. The ramping-up effect remained, demonstrating that the observed temporal profile is robust and independent of the trial-inclusion threshold (see Author response image 3).

      Author response image 3.

      Hippocampal ripple ramping-up analysis among trials with ripples. ***: pFDR < 0.001.

      (6) Statistical model specification.

      The methods describe the ramping-up analysis using both a "logistic" link function and a "Poisson link function" in different places, with the dependent variable described inconsistently as ripple occurrence and ripple count. These are not equivalent, and the distinction matters for interpreting the reported coefficients. Additionally, the regional dissociation in Figure 3 appears to be assessed by fitting separate models to each region and comparing results informally. This does not constitute a direct test of whether slopes differ between regions and risks the well-known error of inferring a difference based on one p-value being significant while another is not. A direct region × time interaction test would more cleanly support the claimed dissociation.

      We apologize for the incorrect and inconsistent terminology. To clarify, in both the ramping-up analysis for all trials and the interaction effect between ramping-up and VSTM performance, we used the Generalized Linear Mixed Model (GLMM) with the Poisson link function. We have now corrected these descriptions in this revision (Page 8).

      In addition, following the reviewer’s suggestion, we implemented a direct statistical test of whether ramping-up differs between HPC and LTL by the following GLMM model:

      Ripple rate ~ 1 + time × memory × region + (1 + time | participant) + (1 + participant | trial)

      The results revealed a significant three-way interaction between time, region, and memory accuracy (β = 0.053, p = 0.044), supporting the dissociation of the ripple temporal patterns between HPC and LTL. We have now integrated this result into the revised manuscript (Page 9) and describe the models in the Methods (Page 24).

      Reviewer #3 (Public review):

      Summary:

      Liu, He, et al. present results suggesting hippocampal ripples support short-term working memory. The basic finding that hippocampal ripples increase during a 7s working memory maintenance period is intriguing and previously not shown as far as I know, but a lack of control analyses within the task, across brain regions, or as compared to alternative oscillatory signals makes the overall evidence weak. The author needs to more thoroughly evidence this signal via several analyses (suggested below) to strengthen their finding. The paper moves on to a hippocampal-cortical ripple coupling analysis that needs further methodological details and corrected statistics to make a meaningful contribution. As is, the ripple coupling results don't seem to necessarily relate to the hippocampal ripples found in the maintenance period, making the manuscript somewhat incoherent and of low impact in its current form.

      We thank the reviewer for recognizing the novelty and potential importance of our findings. We also appreciate the constructive suggestions to further improve our manuscript, and please see our detailed responses below.

      Major issues:

      (1) The framing sets up "visual short term memory" (VSTM) and "long term memory" (LTM) as two different things. A long line of research with humans possessing MTL/hippocampus damage shows the hippocampal memory system contributes to working memory only when the task is difficult enough to warrant its recruitment (see Hannula et al. 2006 J. of Neuroscience, Pertzov et al. 2013 Brain, or particularly Jeneson et al. 2012 Learning & Memory and J. of Neuroscience). This theory therefore, suggests that the hippocampus contributes to working memory via LTM mechanisms, as opposed to it possessing two different roles (VSTM and LTM). While the authors might disagree with this framing, at a minimum, they should describe this line of work. As is, it's difficult to know how their task fits into this literature since it's a cross between a pattern separation probe (identify repeats from lures), working memory (7 s delays), and subsequent cued associate recognition. Addressing why they used this combination of task features would help frame its place in the literature.

      We thank the reviewer for raising this important conceptual issue.

      First of all, we want to clarify that the core objective of our study was not to argue for a dichotomy between VSTM and LTM systems. Rather, we sought to address a fundamental mechanistic question: whether and how hippocampal ripples, which are canonically established in coordinating memory reactivation during offline LTM consolidation, are recruited to support active, online VSTM maintenance.

      In the revision, we have reorganized the Introduction with the following structure (for the comprehensive revised Introduction, please see Pages 3-4):

      (1) We review evidence that the hippocampus is involved in VSTM, including both lesion studies and neural representational studies. These findings converge to suggest that the hippocampus contributes to maintaining visual information over short delays.

      (2) We introduce hippocampal ripples as a key candidate mechanism based on the following lines of evidence: (a) While hippocampal (HPC) ripples have been traditionally linked to offline processing of long-term memory (LTM), more recent evidence indicates that they also contribute to online memory processing, including encoding, maintenance, and most critically, the short-term maintenance period. (b) HPC ripples and their coordinated neocortical memory reactivation have been frequently observed during LTM consolidation and retrieval. Given that VSTM and LTM have been proposed to share neural mechanisms, it is reasonable to hypothesize that the hippocampal ripples and their coordinated memory reactivation contribute to VSTM maintenance. In this revision, this part has been revised as follows:

      “A key candidate mechanism is the hippocampal ripple, a brief high-frequency (~80-170 Hz) oscillation that reflects synchronized activity of neuronal ensembles in the hippocampus (Buzsáki, 2015; Iwata et al., 2024; Norman et al., 2019). Traditionally, hippocampal sharp-wave ripples have been recognized for their role in offline memory consolidation during sleep and quiet awake rest, during which they are temporally coordinated with neocortical memory replay/reactivation via hippocampal-neocortical communication (Eschenko et al., 2008; Schreiner et al., 2024; Zhang et al., 2024, 2018). Recent studies, however, indicate that ripples also actively support online memory processing. In human long-term memory (LTM) studies, ripple rates during encoding and pre-retrieval intervals predict subsequent LTM performance, and temporally coordinate the reinstatement of neocortical representations during successful retrieval (Kunz et al., 2024; Norman et al., 2019; Sakon and Kahana, 2022; Vaz et al., 2019; Zhang et al., 2024). Beyond LTM, rodent studies have revealed that selectively disrupting hippocampal ripples during awake learning periods impaired the working memory-dependent spatial navigation performance (Jadhav et al., 2012; Zhang et al., 2021), pointing to a vital role for ripples in sustaining online short-term memory representations. Moreover, VSTM and LTM could recruit overlapping hippocampal-neocortical networks (Cowan, 2019; Ranganath and Blumenfeld, 2005), especially when the VSTM task is demanding or engaging feature binding (Hannula et al., 2006; Jeneson et al., 2012; Jeneson and Squire, 2012; Pertzov et al., 2013). These findings together raise a fundamental question: Do hippocampal ripples, long implicated in LTM formation and offline consolidation, also actively support human VSTM maintenance?”

      (3) Following the reviewer’s suggestion, we state that hippocampal ripples share key properties postulated for bursts; we hypothesized that hippocampal ripple rates would exhibit a progressive temporal ramping pattern as postulated for bursts across the VSTM maintenance interval in accordance with the dynamic coding framework.

      (4) We emphasize the importance of HPC-neocortical communications in memory processing and propose a potentially coupled ripple mechanism for the interactions between the HPC and the lateral temporal lobe (LTL).

      Regarding the combination of task features, the task was originally designed to examine the dynamic neural representations supporting the maintenance of complex visual information and how these representations may relate to subsequent long-term memory (Liu et al., 2021, 2020). A classical delayed match-to-sample (DMS) paradigm was employed to examine the VSTM. During the VSTM test, highly similar lures were used as half of the probes in the cued-recognition task to increase the task demand for visual features binding within a picture, a condition under which hippocampal involvement in short-delay memory is expected based on prior work (Pertzov et al., 2013). The cue word in the DMS task was designed for a subsequent long-term memory (LTM) cued-recall test. This LTM test allowed us to further examine whether ripple dynamics during the VSTM delay were also related to later LTM performance. To clarify, we have expanded the Methods section to describe the LTM test in greater detail, which reads (Page 19):

      “Following the completion of each VSTM run, participants performed a 1-minute mathematical countback task, followed by a brief rest period (1-4 min) before the LTM cued-recall test. During each LTM test run, 14 learned, unique cue-picture pairs were tested in a randomized order, with each pair tested only once. There are, on average, 88.31 ± 19.28 trials per participant. For each trial, participants first performed a self-paced, binary keypress to indicate subjective retrieval success (“remember” vs. “don’t remember”). Upon a subjective “remember” response, an objective category verification prompt was presented for a maximum of 3 s, requiring a 4-alternative forced-choice response to identify the semantic category of the associated target picture (animals, electronics, fruits, or furniture). Trials were operationally classified as LTM “remembered” trials only if the subjective recall was accompanied by a correct objective category verification. Trials receiving a “don’t remember” response or an incorrect category report were classified as LTM “forgotten” trials.”

      We have also revised the Discussion to better situate our findings that the HPC ripple ramping-up profile primarily supported online VSTM maintenance rather than LTM-related processes. Based on these findings, we interpret such ripple activity as supporting online maintenance under high demands on visual features binding and target-lure discrimination, rather than word-pair associative LTM. This interpretation is also corroborated by studies showing hippocampal involvement in comparable VSTM tasks without associative-memory requirements or without subsequent LTM tests (Daume et al., 2024; Verzhbinsky et al., 2025). Furthermore, we clarify that the absence of a relationship between delay-period ripple dynamics and subsequent LTM performance should not be interpreted as evidence that ripples are unrelated to LTM. Instead, the ramping-up hippocampal ripple rates support active maintenance, whereas successful LTM formation may depend more strongly on ripple-mediated replay during subsequent offline periods (Deceuninck and Kloosterman, 2024; Girardeau et al., 2009; Zhang et al., 2024, 2018). In addition, our task design may have further weakened any direct relationship between VSTM-delay ripples and later cued recall, because LTM performance likely depended on multiple intervening processes, including resistance to interference, post-encoding rest-related reactivation, and retrieval success at test (see details in response to comment #1 for Review #2). Finally, we explicitly acknowledge as a limitation that our task does not isolate “pure” VSTM from LTM-related mechanisms, and future studies using tasks that orthogonally manipulate VSTM-related factors will be needed to more directly dissociate the contributions of hippocampal ripples to VSTM from those supporting LTM. The revised Discussion has been reorganized and expanded as follows (Pages 16-18):

      “In addition, our task involves cue-picture associations, which makes it challenging to fully disentangle VSTM from LTM-related processes. Nevertheless, our findings showed that both the ramping-up hippocampal ripple rates and the HPC-LTL coupled ripples during maintenance were prominently associated with VSTM accuracy but not with subsequent LTM accuracy. These findings suggest that the ripple dynamics we observed primarily support the short-term maintenance of complex visual features and their binding within the pictures themselves rather than the formation of long-term memory for cue-picture pairs, which has been shown in previous research (Pacheco Estefan et al., 2019). This interpretation is strengthened by recent studies showing that hippocampal ripples and hippocampal neuronal firing support VSTM of complex naturalistic pictures in the absence of subsequent LTM tests or cue-picture associations (Daume et al., 2024; Verzhbinsky et al., 2025).” (Page 16)

      “Notably, the absence of the hippocampal ramping-up effect during maintenance in predicting LTM does not conflict with the established role of hippocampal ripples in long-term memory. Converging evidence suggests that ripple contributions to LTM are most evident during offline consolidation windows, including sleep and post-encoding rest, rather than during online task execution. In rodents, suppressing post-learning sleep ripples impairs subsequent memory (Girardeau et al., 2009). In humans, ripple-coupled replay during NREM sleep predicts later memory success (Zhang et al., 2018), and post-encoding awake-rest ripple activity, rather than encoding-period activity, is associated with subsequent memory performance (Zhang et al., 2024). Thus, the lack of association between VSTM-delay ripples and later cued recall raises a possibility: ramping-up ripple dynamics during active maintenance may support online VSTM, whereas LTM formation may depend more on ripple events occurring during post-encoding time windows. Our study cannot rule out the possibility that any relationship between VSTM delay-period ripples and later LTM was obscured by intervening processes between maintenance and recall, including interference resistance, offline consolidation during rest, and retrieval-related factors. Future studies incorporating parametric manipulations, such as varying memory load, delay duration, or lure similarity, will be essential to directly test whether hippocampal ripple activity selectively scales with VSTM demands, thereby providing stronger evidence for its specific role in online maintenance versus LTM-related processes.” (Pages 17-18)

      (2) The basic idea of looking for hippocampal ripples as a marker for working memory maintenance is new, with no prior literature (that I know of in rodents or in the handful of human intracranial ripple papers) to build on. That said, I suspect hippocampal ripples act as a proxy for hippocampal activation, providing a possible explanation for the hippocampal ripple increase shown during the Maintenance period. The effect they show is well supported by the mixed effects modeling (MEM), making it a potentially meaningful finding, but considering the novelty, it's rather important that control analyses rule out alternative possibilities. I suggest two important ones and a third related to the lack of parametric manipulations in the next paragraph. First, the authors frame the paper by suggesting hippocampal ripples share features with beta/gamma burst theories of working memory maintenance. In that case, the obvious question is why use a ripple detector instead of measuring gamma (or beta) activity as in this previous work? Some work has suggested hippocampal ripples act differently than high-frequency activity (see Sakon et al. 2024 J. of Neuroscience), so an analysis contrasting ripples and gamma seems rather important. Second, and relatedly, the authors only compare the hippocampus and lateral temporal cortex (LTC), likely because these tend to be sites with strong coverage in epilepsy cases. That's ok, but typically there is also reasonable coverage in other MTL areas like entorhinal cortex and amygdala, which would serve as important controls to show what they're measuring likely relates to sharp-wave ripples (a hippocampal phenomenon) and not something more generic like gamma or HFA (as shown in Sakon et al. 2024, Howard et al. 2003 Cerebral Cortex, Axmacher et al. 2007 reference 26, Meltzer et al. 2008 Cerebral Cortex, etc.).

      We thank the reviewer for raising these constructive comments.

      First, we agree with the reviewer that validating ripples is paramount. We thus performed an additional validity check on the unfiltered raw signal, as suggested by Reviewer 1. Specifically, if the detected events reflect genuine multi-peak ripple oscillations, the inter-peak intervals in the raw signal should roughly correspond to the ripple-frequency range. Across participants, an average of 89.84 ± 3.31% of the inter-peak intervals fell within the expected 70-180 Hz ripple band, supporting the physiological validity of the detected events (see also Response to Reviewer 1 of this response letter on Pages 2-3). Besides, following the reviewer’s suggestion, we added a control analysis examining continuous high-frequency activity in the same 70-180 Hz range and applied the same ramping-up analysis during the VSTM maintenance period. The results revealed that while we observed a significant ramping-up effect of hippocampal ripples (β = 0.012, p < 0.001), a non-significant trend was observed for ripple-band HFA during maintenance (β = 0.002, p = 0.074). Nevertheless, the ramping slopes did not significantly differ between ripple events and HFA (p = 0.662). We have now incorporated these results into our revised Results as follows (Pages 6 and 8):

      “To validate our ripple detection procedures, we performed peak detection in the unfiltered raw iEEG data and found that 89.84 ± 3.31% of inter-peak intervals (IPIs) within the 70-180 Hz ripple frequency band, confirming that the detected ripple events exhibited multi-peak oscillatory waveforms (Buzsáki et al., 1992) (see Fig. S1)” (Page 6)

      “A similar analysis of the broadband high-frequency activity (HFA) (70-180 Hz) during maintenance revealed a non-significant ramping-up trend (p = 0.074), and the ramping slopes did not significantly differ between ripple events and HFA (p = 0.662).” (Page 8)

      Regarding the reviewer’s suggestion to include other MTL regions, such as the entorhinal cortex and amygdala, as anatomical controls, we agree that this would be a valuable analysis for determining whether the observed effect is specific to the hippocampus or reflects a more general effect for MTL. Unfortunately, the current dataset may not provide sufficient electrode coverage in these regions for reliable results. Specifically, we had only 20 electrodes in the amygdala (AMY, less than one third of the hippocampal electrodes), 6 electrodes in the parahippocampal cortex (PHC), and 2 electrodes in the entorhinal cortex (ERC, see more details in Author response table 1).

      Author response table 1.

      Together, our additional analysis validates the ripples, while we found no significant ramping-up difference between hippocampal ripples and HFA. We therefore have expanded the Discussion as follows (Page 14):

      “In addition, our results indicate that hippocampal ripples are unlikely to be the sole mechanism supporting VSTM. While we validated the ripple events, our current data did not show significant differences in the ramping-up effects between hippocampal ripples and HFA. Recent research demonstrated that HFA exhibited broad subsequent memory effects across MTL regions, whereas hippocampal ripples were more selectively associated with subsequent temporal and semantic clustering during recall (Sakon and Kahana, 2022). Thus, future studies with denser MTL coverage and direct comparisons between ripples and HFA under specific task manipulations are needed to better investigate whether ripples make a functional contribution beyond general high-frequency activation. Moreover, prior work has shown that gamma bursts in the prefrontal cortex gate access to encoded VSTM representations and that ramping of such bursts supports working memory in primates (Lundqvist et al., 2016). Recent rodent research demonstrates that replay sequences can occur even in the absence of sharp-wave ripples (Widloski and Foster, 2025). These findings suggest that hippocampal ripple ramping-up should be interpreted as one component within a broader, distributed set of dynamic mechanisms supporting short-term memory maintenance.”

      Finally, while formal published studies on this specific topic remain limited, a recent human iEEG preprint closely corroborates our findings. This study shows that hippocampal ripples and HPC-LTL coupled ripples support working memory maintenance by coordinating representational reactivation under varying memory loads. These independent findings strongly align with our conclusions and reinforce the validity of our reported mechanisms. Here is the information for the preprint:

      Verzhbinsky IA, Daume J, Rutishauser U, Halgren E. 2025. Cross-region neuron co-firing mediated by ripple oscillations supports distributed working memory representations. bioRxiv 2025.09.04.674061. DOI: https://doi.org/10.1101/2025.09.04.674061, PMID: 40950034

      (3) Related to the last point, since there are no parametric manipulations (e.g., different delay durations, different set sizes, varying lure difficulties) there's no way to assess increased hippocampal ripples with stronger loads, which would be important for determining the hippocampal dependence of their task in the first place. Do the authors have any justification for this task as an assessment of hippocampal working memory? I could imagine using a top vs. bottom tercile of lure discrimination difficulty (as assessed across all participants or control non-patients) to compare hippocampal activity. But only after the first trial, each pair is used since only then would the patient have awareness of the difficulty of the upcoming comparison. Or maybe something could be done by comparing VSTM performance by splitting patients based on how they performed at the LTM test.

      We thank the reviewer for these insightful suggestions. We agree that parametric manipulations of delay duration, memory load, or lure similarity would provide stronger evidence for testing whether hippocampal ripples scale with VSTM demands. However, the current task did not include such manipulations. We thus have explicitly discussed these points and the lack of parametric load manipulations as limitations in the revised manuscript (Pages 17-18), which reads:

      “Future studies incorporating parametric manipulations, such as varying memory load, delay duration, or lure similarity, will be essential to directly test whether hippocampal ripple activity selectively scales with VSTM demands, thereby providing stronger evidence for its specific role in online maintenance versus LTM-related processes.”

      To address the reviewer’s other suggestion regarding potential behavioral interactions between VSTM and LTM performance, we performed a subgroup analysis. We quantified overall LTM cued-recall accuracy for each participant, where trials were scored as correct (1) if the participant reported subjective retrieval success accompanied by a correct category report, and incorrect (0) otherwise. Using a median split (median accuracy = 0.45), we stratified our 13 participants into a “Poor LTM” group (n = 7) and a “Good LTM” group (n = 6). A two-sample t-test comparing VSTM accuracy between these two subgroups revealed no significant difference (t(11) = -1.20, p = 0.254) (see Author response image 4).

      Author response image 4.

      Visual short-term memory (VSTM) accuracy stratified by long-term memory (LTM) performance. VSTM retrieval accuracy compared between poor- and good-LTM-performing subgroups, partitioned via a median split of participants’ overall LTM retrieval accuracy. n.s.: not significant.

      (4) Also related to the VSTM vs. LTM framing, the authors use an "LTM" cued category recognition task--presumably done at the end of the repeat/lure recognition task--as a way to argue that the hippocampal ripple effects they see relate to VSTM and not LTM. The LTM task is disappointingly underdescribed, where even in the methods (lines 588-592) I cannot figure out when this task was probed, how many trials were done in comparison to the VSTM task, etc. Considering they use the LTM task to support their VSTM interpretation, it's rather crucial to understand precisely what they did. As is, the comparison they do present relies on a statistical error, where they compare p-values (n.b. https://www.nature.com/articles/nn.2886) instead of performing a direct interaction test (lines 177-180). Specifically, if they want to say their signal relates more to VSTM subsequent memory rather than LTM subsequent memory, they need to run a model of the form: ripple_rates ~ remembered + test_type + remembered × test_type (where test_type is either their VSTM or LTM task).

      We thank the reviewer for raising these important points. In this revision, we have now provided more details regarding the long-term memory task in the Methods as follows (Page 19):

      “Following the completion of each VSTM run, participants performed a 1-minute mathematical countback task, followed by a brief rest period (1-4 min) before the LTM cued-recall test. During each LTM test run, 14 learned, unique cue-picture pairs were tested in a randomized order, with each pair tested only once. There are, on average, 88.31 ± 19.28 trials per participant. For each trial, participants first performed a self-paced, binary keypress to indicate subjective retrieval success (“remember” vs. “don’t remember”). Upon a subjective “remember” response, an objective category verification prompt was presented for a maximum of 3 s, requiring a 4-alternative forced-choice response to identify the semantic category of the associated target picture (animals, electronics, fruits, or furniture). Trials were operationally classified as LTM “remembered” trials only if the subjective recall was accompanied by a correct objective category verification. Trials receiving a “don’t remember” response or an incorrect category report were classified as LTM “forgotten” trials.”

      Additionally, following the reviewer’s suggestion, we have added a three-way interaction analysis between memory performance, test_type (VSTM vs. LTM), and time, for hippocampal ripples, using the following LMM:

      ripple ~ time × memory × test_type + (1 + time | participant) + (1 | participant: trial)

      The results revealed that the three-way interaction effect (time × remembered × test_type) exhibited a non-significant trend (β = 0.039; p = 0.071).

      We have incorporated the interaction result into the Results section (Page 12):

      “A further analysis examining the three-way interaction between time, memory accuracy, and test type (VSTM vs. LTM) for hippocampal ripples revealed a trend but statistically non-significant interaction effect (β = 0.039, z = 1.809, p = 0.071).”

      (5) As noted, the increase in hippocampal ripples during maintenance seems substantial, and the MEM confirms a significant increase over time. That said, the presentation of the data is atypical, with an example raster from one channel followed by average time courses of ALL participants below it. Why not show full raster plots for all participants? Ripples are so sparse that all the data in the task can be visualized in a single raster easily. A swarm plot indicating inter-patient variability in the maintenance signal also seems crucial. As is, there is no way to assess how much of the signal depends on a small subset of channels or patients.

      We thank the reviewer for these insightful comments. In the revised manuscript, we have removed the single-channel exemplar raster plot from Figure 2, which now exclusively displays the group-level results. In addition, we have generated full raster plots depicting all detected hippocampal ripple events across all trials for each of the 13 participants as Supplementary Figure S3. In these raster plots, each row represents a single VSTM trial. For patients with multiple hippocampal recording sites, the ripple events detected across all channels are overlaid within the same trial row. Consequently, patients with a higher number of hippocampal channels naturally display a higher spatial density of plotted dots (with each dot representing an individual ripple).

      Furthermore, for the concern regarding inter-individual variability, we have provided a detailed breakdown of electrode counts and individual ramping coefficients (β) in Supplementary Table S1, accompanied by a participant-level swarm plot in Supplementary Figure 5b. These data demonstrate highly consistent patterns across our patient cohort: 11 out of 13 participants exhibited positive ramping coefficients (β > 0) during VSTM-remembered trials, whereas only 4 out of 13 participants showed positive coefficients during forgotten trials. The paired samples t-test revealed that the ramping coefficients for remembered trials were significantly greater than those for forgotten trials (t(12) = 3.400, p = 0.005). This confirms that the reported ramping effect reflects a robust, group-wide phenomenon.

      Author response table 2.

      Participant-level summary of hippocampal channel counts and ramping-up coefficients (β) for remembered and forgotten trials.

      (6) To compare ripple rates across task phases, they average over the bounds of each phase (lines 657-660) and input these into their MEMs. This approach makes sense for quantifying what we see in the ripple plots (Figure 2), except for Encoding, where they average over the entire 3 s window, even though there is clear tuning only from ~0-1 s. Using the tuned region and not the entire window is standard and would be more appropriate for the comparisons to maintenance, retrieval, etc (e.g., line 147-148 doesn't check out when looking at the figure), otherwise you are averaging over a seeming ripple inhibition from 1-2 s. They perform a cluster-based permutation test as is, so that a window or something a bit wider would be appropriate.

      We thank the reviewer for raising this important point and have performed a control analysis to use [0,1s] after stimulus onset as the encoding time window of interest. We then re-ran our Linear Mixed-Effects Models (LMMs) comparing the ripple rates between every two task stages. This result revealed that encoding showed significantly higher hippocampal and LTL ripple rates than baseline and maintenance (ps<sub>FDR</sub> < 0.001), while there is no significant difference in hippocampal ripple rates between encoding and retrieval (p<sub>FDR</sub> = 0.859). For the LTL ripple rates, encoding is lower than retrieval (p<sub>FDR</sub> = 0.001). These results were added to the revised Results and shown in Supplementary Figure S4.

      “Given that both the hippocampal and LTL ripple rates increased within the 0-1 s of encoding, we re-performed the comparisons of the averaged ripple rates between task stages using this 0-1 s encoding time window while keeping other stages unchanged, and the pattern of the main results remains (see Fig. S4).”

      (7) The authors pivot to a hippocampal-cortical ripple coupling analysis to build the argument that the hippocampal ripples shown in Figure 2 support memory maintenance in the cortex. They use a window of -500 to 500 ms from hippocampal ripples to assess coupling. This is quite wide, since it doesn't seem plausible that a cortical ripple 500 ms from a hippocampal ripple means they synchronize. They cite two papers to justify the analysis, both of which use {plus minus}500 ms windows, but for spindle-ripple coupling, not ripple-ripple, so are miscited. Later in the paper, they switch to {plus minus}50 ms for another coupling analysis, raising the question of why they used {plus minus}500 ms in the previous analysis to begin with. If they want to claim cortical ripples are tuned by hippocampal ripples all the way up to 500 ms away, they should show the rasters (as in Figure 4a) and timecourse ripple rates, but going beyond {plus minus}500 ms to show that ripples in the {plus minus}50-500 ms range are above, say 500-1000 ms to justify their window selection. I will point out that there IS previous work that used {plus minus}500 ms to measure cortical-cortical ripple coupling (Dickey et al 2022 PNAS, which should be cited regardless, as I believe the first hippocampal-cortical ripple paper showing memory effects), although the figures in that paper suggest anything beyond {plus minus}250 ms returns to baseline (see Figure 2A-B).

      We apologize for the lack of clarity in our original description. We recognize that our terminology conflated two distinct analytical approaches for measuring the temporal coordination between ripples and have explicitly clarified this distinction in the revised manuscript. In addition, we have changed the papers referring to these analyses.

      Specifically, for the analysis in Figure 4b (i.e., LTL Ripple Rate Locked to HPC ripple peak), we computed the LTL ripple rate within a broader time window (i.e., [-0.5 s, 0.5 s]) centered HPC ripple peaks (Dickey et al 2022 PNAS). We thus normalized the HPC ripple-locked LTL ripple rate to a baseline of LTL ripple rates that were not coordinated by HPC ripple peaks, yielding the normalized LTL ripple rate time-locked to HPC ripple peaks. This broader window was employed to examine the lead-lag or directional dynamics between the two regions. We agree that labeling this as “coupled ripples” in the original text is misleading. In the revised manuscript, we have changed the y-axis label of Figure 4b into “Normalized LTL ripple rate (z-score)”.

      For the coupled ripple and the coupled ripple locked decoding analyses (Figure 4c and Figure 5), “coupled ripples” were defined as LTL ripples that temporally overlapped with or occurred within ± 50 ms of an HPC ripple peak, following a previous study (Vaz et al., 2019, Science). We have revised the corresponding text in both the Results and Methods sections (Pages 9-10 and Page 24) to clearly separate these two analyses and ensure that the term “coupled ripples” is reserved exclusively for LTL ripple events within ± 50 ms of HPC ripple peaks.

      (8) Lines 239 to 243 comparing p-values instead of an interaction test.

      We thank the reviewer for raising this important statistical point. In the original lines 239-243, we compared the coupled HPC-LTL ripple rates between remembered versus forgotten conditions, separately for each stage, without performing the task stage (encoding, maintenance, and retrieval) × memory accuracy (remember vs. forget) interaction effect. In this revision, we performed the (task stage × memory accuracy) repeated ANOVA and found no significant interaction effect (F(2,24) = 0.49, p = 0.619). This non-significant interaction effect does not undermine our main finding of a significant memory effect during maintenance itself, given we mainly focus on the maintenance period following the ramping-up results. We have also reported this interaction result in the revised Results (Page 10).

      (9) I don't understand what "Further analysis based on the identified cluster" means (line 271). I see in Figure 5c that their broadband classifier identified a window of optimal decoding, but did they use only activity in this cluster to train the subsequent classifier (Figure 5d)? If so, this is not described in the methods. And if it is done that way, I don't think the logic makes sense. As mentioned in comment 6, the ripples during encoding tune to 0-1s after image presentation. So it doesn't make sense to use a 1.85-2.25 s window for ripple-locked decoding-they should just be using the 0-1 s window (or whatever their cluster-based permutation test shows in Figure 2b). Otherwise, it would appear they are studying two different phenomena.

      We thank the reviewer for raising this important point. We apologize for the lack of clarity. To clarify, we did not predefine an encoding cluster based on ripple rate change. Rather, we used a data-driven method to find the “identified cluster”, which refers to the temporal window during which representation reactivation was significantly locked to coupled ripples. Here is the step-by-step procedure we used and more detailed described in the revised Methods (Pag 26):

      (1) We trained category-level classifiers on broadband iEEG data at every single time window during the encoding stage, and tested them across all time windows of both the encoding and maintenance stages using a leave-one-trial-out cross-validation method (yielding the cross-temporal generalization matrix shown in Figures 5a & b).

      (2) For every single trial, we extracted the continuous decoding accuracy time series locked to each HPC-LTL coupled ripple within a window of [-0.5 s, 0.5 s] (using the HPC ripple peak of coupled ripples as the reference zero time point), following previous research (Zhang et al., 2018).

      (3) To determine if memory reactivation was significantly locked to these coupled ripple events, we compared this empirical ripple-locked decoding accuracy against a surrogate baseline (constructed by randomly selecting non-coupled time points locked decoding accuracy 1,000 times to create a z-score distribution). A cluster-based permutation test was then performed across the [-0.5 s, 0.5 s] time window. The “identified cluster” (shown in Figure 5c) is the resulting significant time window around the ripple peak where decoding accuracy was significantly elevated above the surrogate baseline.

      Additionally, the reviewer pointed out that, if the encoding ripples peak early (0-1 s after stimulus onset, as shown in Figure 2), why did the classifier trained on late encoding data (1.85-2.25 s) yield the most robust ripple-locked reactivation during the maintenance delay? This temporal discrepancy aligns well with the memory representational transformation framework (Xue, 2022). According to this framework, memory representations are highly dynamic. Following stimulus presentation, early sensory cortical activity (0-1 s) primarily represents low-level visual and perceptual features. As processing progresses into late encoding (e.g., 1-2 s post-stimulus onset), these representations are transformed into more abstract and stable semantic formats (e.g., category-level information), which are supported by the lateral temporal lobe (LTL) in prior research (Ralph et al., 2017). Given that our decoding analysis is a category-level classifier, it is reasonable that more stable decoding evidence would be obtained when the classifier was trained using the late-encoding semantic window. Consequently, our finding that delay-period coupled ripples reactivate representations from this late-encoding window suggests that coupled HPC-LTL ripples are engaged in coordinating the reactivation of semantic representations during VSTM maintenance. In contrast, the early perceptual features encoded during the early window (which match the peak of encoding ripples) may rely on different pathways, such as coupled ripples between the hippocampus and primary visual cortices, which could not be directly assessed due to limited occipital coverage in the present clinical iEEG dataset. We have expanded the Discussion in this revision as follows (Pages 15-16):

      “Notably, while encoding ripples peaked early after stimulus onset, the classifier trained on late encoding activity showed the strongest ripple-locked reactivation during maintenance. This temporal discrepancy is consistent with the memory representational transformation framework, which proposes that mnemonic representations evolve over time (Xue, 2022). Early encoding activity may primarily reflect low-level visual/perceptual features, whereas later encoding may contain more stable category-level or semantic representations. Prior intracranial and neuroimaging studies have implicated lateral temporal regions in such higher-level coding (Ralph et al., 2017). Given that our decoder targeted category-level information, it is reasonable that the decoder performed well when trained on this later window. Thus, delay-period hippocampal-LTL coupled ripples may preferentially reinstate higher-level category/semantic representations during VSTM maintenance. Early perceptual representations may instead rely more on hippocampal-visual cortical interactions, which could not be assessed due to limited occipital coverage.”

      (10) As is, the results in Figure 5d need to be redone. First, the results described on lines 271-275 once again suffer from comparing p-values. They need to run an interaction model if they want to claim Maintenance shows stronger ripple-locked decoding than Encoding (it almost certainly will not, since Encoding appears to show some evidence of decoding (p=0.118)). Second, even if they do change the framing to say Encoding and Maintenance show significant decoding, is it meaningful if Retrieval fails to? If you cannot decode the same information at the time of retrieval as is theoretically being held in working memory during the delay, the coupled ripple reactivation story wouldn't appear to make sense. They do show significant Retrieval decoding in Figure 5a-b, but since I don't really understand how they settled on the "identified cluster" in Figure 5c, I'm not sure what to make of the difference between these decoders.

      We thank the reviewer for raising this important point. As we have responded to your Comments #8 above, our original analysis did not aim to claim maintenance shows stronger ripple-locked decoding than encoding or retrieval stages. Thus, we reported the coupled ripple-locked decoding results separately for each stage, with a special focus on the maintenance period, given the hippocampal ripple ramping-up was found in prior results sections.

      Nevertheless, following the reviewer’s suggestion, we directly compare coupled ripple-locked decoding across phases (i.e., Maintenance vs. Encoding, and Maintenance vs. Retrieval). The results revealed no significant difference between encoding and maintenance (ps<sub>cluster</sub> > 0.800, see Supplementary Fig. S8a). The comparison between maintenance and retrieval revealed a significant cluster-corrected difference (p<sub>cluster</sub> = 0.024). In this revision, we have incorporated these results into the revised manuscript (Page 11).

      We also want to clarify that the absence of coupled ripple-locked decoding during the retrieval phase may not contradict our theoretical framework. As the reviewer may note, neither the encoding nor the retrieval phase exhibited significant coupled ripple-locked memory reactivation. During both the encoding and retrieval stages, participants were exposed to salient, feedforward visual inputs (i.e., the target picture or the highly similar visual lures). Consequently, the high decoding accuracy observed in the lateral temporal lobe (LTL) during these phases (Figures 5a & b) is probably driven by feedforward perceptual processing. In contrast, our finding of significant coupled ripple-locked memory reactivation is mainly observed during the maintenance period, where no external visual inputs are present. This suggests that coupled ripples may serve as a specialized, internally generated mechanism to transiently reactivate and sustain representations when external sensory inputs are absent.

      In this revision, we have extended our Discussion as follows (Page 16):

      “In addition, no significant coupled ripple-locked decoding accuracy was observed during encoding or retrieval. This likely arises because encoding and retrieval involve salient visual inputs (target picture or lure), such that the LTL decoding accuracy is probably driven by feedforward perceptual processing. In contrast, during maintenance, where no external input is available, coupled ripples may serve as a specialized, internally generated mechanism to transiently reactivate and sustain representations.”

      (11) Finally, as mentioned in the summary, the analyses in Figures 2-3 seem disjointed from those in Figures 4-5. Part of this has to do with the switch to a broadband classifier, then a switch back to coupled ripples, and then, as I already mentioned, decoding results with time windows that don't align with the hippocampal ripple effects they showed earlier. Further, since the main point of Figures 2-3 is to establish a ramp in hippocampal ripples across maintenance, shouldn't they be trying to show how the decoding changes over the course of the Maintenance period? It would also help the interpretation of Figure 5 to see how the coupled ripples change over time in Figure 4 (as they showed them in Figure 2).

      We thank the reviewer for these insightful comments. Following the reviewer’s comments, we performed the following analysis:

      First, we examined the temporal dynamics of both hippocampal-cortical coupled ripples during maintenance time windows. Coupled ripples showed a non-significant ramping-up pattern for both remembered and forgotten trials (ps<sub>FDR</sub> > 0.281), and there was no significant time × memory accuracy interaction (p = 0.506, see Fig. S6), suggesting no significant ramping-up for the coupled ripples regardless of VSTM memory performance.

      Second, we tracked how decoding accuracy and the memory reactivation index evolved across the maintenance period (using the classifier trained on the [1.85 s, 2.25 s] encoding window). The LMM revealed a highly significant time × memory accuracy interaction (p = 0.009, see Fig. S6). Further analysis revealed that this interaction was driven by a significant decline in decoding accuracy on forgotten trials (p<sub>FDR</sub> = 0.031), whereas decoding accuracy on remembered trials was maintained (p<sub>FDR</sub> = 0.214).

      Finally, we extracted the coupled ripple-locked decoding accuracy and examined whether this event-locked reactivation changed over the maintenance period. For remembered trials, the coupled ripple-locked memory reactivation showed a non-significant numeric increase across the maintenance period (p = 0.586, see Fig. S6). We have revised the Results and Discussion as follows:

      “We next examined the temporal dynamics of coupled ripples during maintenance. HPC-LTL coupled ripples showed non-significant ramping patterns for both remembered and forgotten trials (ps<sub>FDR</sub> > 0.281), with no significant difference between these two conditions (p = 0.506; see Fig. S6).” (Page 10)

      “We also examined the temporal dynamics of coupled ripple-locked memory reactivation during maintenance. The memory decoding accuracy showed a significant time × VSTM accuracy interaction (p = 0.009; see Fig. S6), with a significant decline on forgotten trials (p<sub>FDR</sub> = 0.031), while relatively stable on remembered trials (p<sub>FDR</sub> = 0.214). Within remembered trials, coupled ripple-locked memory decoding accuracy showed a non-significant numeric increase across the maintenance stage (p = 0.586; see Fig. S6).” (Pages 11-12)

      “However, neither the coupled ripples nor the coupled ripple-locked memory reactivation shows a significant ramping-up effect. Nevertheless, our results indeed observed that, in contrast to the significant decrease in decoding accuracy for forgotten trials, the remembered trials showed relatively stable memory reactivation during the maintenance period, suggesting that coupled ripples may coordinate discrete reactivation events in supporting the stable VSTM maintenance.” (Page 13)

      Minor issues:

      (1) Instead of citing a software package like Emmeans, the statistical test being performed should be explained.

      We apologize for the lack of clarity. We have added more details of the statistical test:

      “We then conducted post hoc pairwise contrasts between estimated marginal means (emmeans) of the four stages to test whether ripple rates differed between specific stages. The resulting p-values from these pairwise contrast tests were corrected for multiple comparisons using the Benjamini-Hochberg false discovery rate (FDR) procedure (Benjamini and Hochberg, 1995).” (Page 22)

      (2) Decoding % accuracy in the heatmaps in Figure 5 and supplementary would be more intuitive, particularly since Figure 5b uses accuracy anyway.

      We thank the reviewer for the constructive comments. In this revision, we have now revised the values in Figure 5a and Figure 5c into the decoding accuracy and the normalized decoding accuracy, respectively (see Figure 5).

      (3) Figure 2b is misleading with an unnecessary change in the y-axis for retrieval.

      We have now changed Figure 2b to keep the y-axis the same for the encoding, maintenance, and retrieval phases (see Figure 2b).

      (4) In Figure 2d, a significant cluster is mentioned, but not drawn onto the figure as in Figure 2b.

      We thank the reviewer for the suggestion and apologize for the absence of cluster illustration in the original manuscript. In this revision, we have now marked the cluster in Figure 2d (see Figure 2d).

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      Below, I list a few points that I think would benefit the manuscript if the authors addressed them.

      (1) Coupled Hippocampo-Neocortical Ripples: The duration of a ripple varies between 20 - 200 ms (line 624). However, the time window for a coupled ripple is 1 second, which is 5 times the maximum duration of a ripple. It therefore would mean that many ripples which are referred to as 'coupled' actually don't overlap in time, which questions whether those could be termed coupled. Wouldn't a better analysis approach be to analyse the start and end times of individual ripples and only count those as coupled ripples where the start and end times actually overlap (for example be computing the duration of interval intersection, which has to be > 0 for coupled events)?

      We apologize for the lack of clarity. Please see our detailed response to your comments on Pages 3-4 of this response letter.

      (2) Spurious vs real ripples: As I have said, the ripple detection method is thorough and generally appropriate. However, one improvement could be made to make it even more convincing. This suggested improvement is to run a peak detection on the unfiltered data in the time window where a ripple is being detected and quantify the inter-peak interval. If the ripple is truly present in the raw data, then this inter-peak interval should roughly correspond to the ripple frequency. If it doesn't, then there probably isn't a ripple. This would circumvent the problem of misclassifying artifacts that look like ripples after filtering (i.e., spikes). I appreciate that the authors inspected the time-frequency transformed data visually and excluded events where a broadband increase extended into the ripple frequency range, as typically occurs in IEDs, but this suggested analysis would be a more formal approach that doesn't rely on individual criteria and hence is more reproducible.

      We thank the reviewer for the constructive comments. Please see our detailed response to your comments on Pages 2-3 and 37-38 of this response letter.

      (3) Visualization of the ramping-up effect. I found the ramping-up effect in Figure 2b fairly subtle and difficult to appreciate. I wonder whether the authors could make an effort to somehow highlight this effect a bit more? Relatedly, ripples seemed to be locked to the onset of the retrieval cue, but that is difficult to see because the data is plotted locked to the response onset. Wouldn't it make more sense in this case to lock to the probe onset?

      We thank the reviewer for the insightful comments. For the visualization of the ramping-up effect in Figure 2b, we have now revised it as Figure 2b, in which we indicate the ramping-up effect using the pink arrow.

      Moreover, we re-plot the ripple rates during the retrieval stage by locking ripple rates to the probe onset. This alternative alignment revealed a significant decrease in ripple rates approximately 1-2 seconds post-probe (indicated by the black horizontal bar, see Author response image 5). This time window is highly consistent with the time window observed in our original response-locked plot. We have therefore retained the response-locked plots in the main text.

      Author response image 5.

      The probe onset-locked hippocampal (HPC) ripple rates during retrieval.

      Reviewer #2 (Recommendations for the authors):

      (1) It would strengthen the paper to provide a more explicit theoretical account of why hippocampal ripples, as a mechanism canonically associated with offline sleep-dependent consolidation, should be recruited during online short-term memory maintenance - including some engagement with the observation that ripple dynamics here are associated with short-term but not long-term memory performance.

      We thank the reviewer for the constructive comments. Please see our detailed response to your comments on weakness #1 on Pages 6-7 of this response letter.

      (2) Providing group-level average power spectra and mean waveforms of detected ripple events would help demonstrate a narrowband spectral peak distinct from broadband high-gamma, and clarifying the precise spectral and temporal criteria used in IED exclusion would aid reproducibility.

      We thank the reviewer for the constructive comment. In this revision, we have now changed the Figure 2a lower panel into the group-level averaged power spectral and mean waveforms of ripple events (see Figure 2a).

      For the IED exclusion, we have added more details as follows:

      “IEDs were independently visually inspected, marked and verified by two neurologists at Beijing Xuanwu Hospital before the ripple detection analysis. In addition, IEDs typically exhibit broadband power increases (1-180 Hz), whereas physiological ripples show narrow high-frequency activity (70-180 Hz) and were further confirmed by performing the time-frequency analysis in Brainstorm (https://neuroimage.usc.edu/brainstorm/). Candidate ripple events occurring within 50 ms of an IED duration range were excluded.” (Page 21)

      (3) Including participant-level lateral temporal lobe channel counts and ramping-up slopes alongside the hippocampal data in Table S1, with confirmation that all participants contributed lateral temporal lobe data, would be a useful addition.

      We thank the reviewer for the constructive comment. We have now incorporated the participant-level lateral temporal lobe channel counts and ramping-up slopes alongside the hippocampal data in Table S1.

      (4) Describing the bootstrapping procedure for trial-count matching in greater detail, and reporting raw remembered versus forgotten trial counts per participant, would improve reproducibility.

      We thank the reviewer for the constructive comment. We have now provided more details of the bootstrapping procedure in Methods, and a Supplementary Table S2 with remembered and forgotten trial counts per participant (Page 25) as follows:

      “To rule out the possibility that the observed difference in coupled ripple rates between remembered and forgotten trials was driven by unequal trial numbers (i.e., a greater number of remembered trials), we performed a bootstrapping analysis. Specifically, for each participant, we randomly resampled remembered trials with replacement 1,000 times, matching the number of remembered trials to the number of forgotten trials (see Tables S2). For each bootstrap sample, we computed coupled ripple rates separately for remembered and forgotten trials. Statistical significance was assessed based on the proportion of bootstrap samples in which the coupled ripple rate was higher in remembered than in forgotten trials.”

      (5) One sentence in the Introduction: "persistent activity is not consistently observed in the neocortex, where the short-term memory information can be successfully decoded" may confuse readers, as the relative clause appears to contradict rather than support the main point.

      We thank the reviewer for noting this issue. During this revision, the Introduction has been reorganized, and this sentence was removed; it now reads:

      “Traditional models of VSTM proposing sustained, persistent neural activity during delay periods have been challenged by “activity-silent” or dynamic coding frameworks (Fiebig and Lansner, 2017; Miller et al., 2018; Mongillo et al., 2008; Stokes, 2015).” (Page 4)

      (6) The Discussion contains a sentence fragment beginning "First of all, no overall above-baseline hippocampal ripple rate..." that would benefit from revision.

      We thank the reviewer for noting this issue. We have revised this sentence for clarity and grammatical completeness. Now it reads:

      “The hippocampal ripple rate progressively ramps up over the 7-s maintenance period, while the overall average rate during this period does not exceed the pre-encoding baseline.” (Page 12)

      (7) The claim that "the absence of lateral temporal ripple ramping-up cannot be attributed to more heterogeneous ripple activity" would benefit from a reference to the specific justification supporting this conclusion.

      We thank the reviewer for pointing this out. We have revised this statement in the main text to directly reference the corresponding control analysis in Supplementary Figure S5, which demonstrates that ripple-rate variability does not significantly differ between HPC and LTL channels.

      Reviewer #3 (Recommendations for the authors):

      I want to commend the authors for going through the public eLife process. I put everything in the public review since I think it's good to have a transparent process so both the authors and others reading can directly see the peer review process. There's potential for a meaningful paper here, and I would be happy to look at a next round to try and make that happen.

      We sincerely thank the reviewer for the constructive and encouraging comments. We have carefully responded to all your comments in the public review and revised the manuscript accordingly. We believe that these revisions have addressed the reviewer’s concerns and improved the clarity and interpretation of our results.

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    1. Author response:

      The following is the authors’ response to the previous reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      A fundamental technique for the identification of peptide-specific CD8 T cells is the use of fluorophore-conjugated and peptide-loaded MHC tetramers. Classically, refolding of specific peptides with MHC monomers can be labour-intensive and not optimal for screening large numbers of different peptides. Hence, UV-exchanged tetramers have been developed to upscale this, however, still has some associated challenges such as UV-mediated damage to peptide complexes. Here, Pothast, C.R. et al demonstrate the efficacy of using temperature-exchanged tetramers for the prevalent alleles HLA-A*03:01, A*11:01, B*07:02, and C*07:02. Building upon their previous work with HLA-A*02:01, H-2Kb, and HLA-E. They first demonstrate the complex stability of tetramers with different affinity peptides at high temperature, showing complex destabilisation can be rescued with higher affinity peptides. This is followed by an optimisation of peptide exchange temperatures, tailored for each allele. The authors then demonstrate successful binding to clonal T cell lines, and then a step further with viral peptides against PBMCs from individuals with confirmed infection history. For the later they compare to conventional tetramers and demonstrate comparable signal.

      Due to the prevalence of these 4 alleles, the ease of handling, and short me requirements, these tetramers are likely to show high utility.

      Strengths:

      The manuscript is well-written and results are solid, although more detail may add clarity to some of the results, in particular figure 1 and 2. Other than the points reported below, the study uses accurate controls to demonstrate the specificity of the tetramers, and the data is convincing.

      Overall, their interpretation of the results is accurate and the discussion thorough, additional comments may be included to cover potential tetramer batch variability, and differences in the stability of different alleles. Specifically, whether certain alleles require higher affinity peptides to be stable, compared to others.

      Comments on revised version.

      The authors addressed the weaknesses highlighted in the previous version, specifically addressing that they do not conclude that thermal peptide exchange is not superior to existing technologies, but may be more feasible, as well as including a section on the stability of the different alleles and template peptides. The authors also updated the labelling and description of figures, making them much more interpretable. Addition of the LILRB1 reporter cell line to demonstrate successful peptide exchange and stability adds extra validity to the results.

      We thank the reviewer for the careful evaluation of our work and for the positive assessment of the manuscript. We are pleased that the reviewer finds the study well written, the data convincing, and the approach likely to be of practical utility for the analysis of antigen-specific T-cell responses.

      Reviewer #2 (Public review):

      Summary:

      This work highlights a new approach to build an array of highly stable peptide MHC-I using temperature exchange, which can be used to identify antigen specific CD8+ T cells.

      Strengths:

      In this work, the authors have proposed an alternative method to reload the peptide MHC-I molecule. Their temperature-exchange approach is distinct from current reloadable peptide MHC technologies involving photo labile peptide, empty MHC-I (Nat Community 11, 1314 (2020). https://doi.org/10.1038/s41467-020-14862-4), tapasin/TAPBPR chaperone-assisted (eLife 7:e40126.), enzyme exchangeable (https://pubmed.ncbi.nlm.nih.gov/31201791/) and small alcohol (Curr Res Immunol. 2022 Aug 18;3:167-174. doi: 10.1016/j.crimmu.2022.08.002) approaches

      Weaknesses:

      The temperature-exchange approach identifies antigen-specific T cells at the same frequency of the photolabile peptide MHC-I molecules. The time saved using temperature-exchange protocol may not be a pull factor as the photolabile peptide MHC-I approach is not unreasonably laborious.

      As with other exchange systems, performance can vary by HLA allele and complex stability, so each new allele needs empirical optimization.

      In short, temperature-based p-MHC exchange is a practical and fast loading strategy with good utility for multimer generation, but its main limitation is dependence on thermal stability and careful template selection.

      We thank the reviewer for the positive evaluation of our work and for recognizing temperature-mediated peptide exchange as a practical approach for the generation of peptide–MHCI multimers.

      We appreciate the reviewer placing our methodology within the broader context of existing peptide loading technologies, including photolabile peptide, empty MHC-I, chaperone-assisted, enzyme-mediated, and small alcohol-based exchange systems. In response to comments raised during review, we have expanded the Introduction to include a more comprehensive discussion of these alternative approaches and their respective strengths and limitations.

      We agree that the primary advantage of thermal peptide exchange is not necessarily improved sensitivity or detection of antigen-specific T cells compared with established methodologies. Rather, its value lies in providing an additional peptide-exchange platform that is simple to implement, requires only standard laboratory equipment, and enables rapid generation of peptide–MHC multimers. We also agree that successful implementation requires empirical optimization for each HLA allele and relies on the identification of suitable template peptides.

      We are grateful for the reviewer's constructive comments, which have helped us improve the clarity and balance of the manuscript.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      No additional experiments required.

      Resolution of figures could be improved unless it is a caveat of the software used.

      We thank the reviewer for this positive assessment and constructive suggestion. High-resolution versions of all figures have been included in the revised manuscript

      Reviewer #2 (Recommendations for the authors):

      The following sentences are incorrect.

      Line 101: "The MHC-multimers are multimerized and fluorescently labeled prior to peptide exchange" is incorrect. Instead, combinatorial peptide MHC multimers involves peptide exchange prior to multimerization during barcoding and not vice versa (https://pubmed.ncbi.nlm.nih.gov/23748502/).

      We thank the reviewer for carefully noting this inaccuracy. As suggested, we have revised the text to better reflect the different workflows used across MHC multimer platforms. The sentence now reads: “Depending on the platform, peptide exchange may be performed either before or after multimerization and labeling.”

      Line 296: "Quantifying the efficiency of UV-induced peptide destruction and subsequent peptide exchange remains challenging" is incorrect. The thermal stability of empty MHC-I vs loaded peptide MHC-I after UV irradiation or thermal exchange can be measured using either gel filtration chromatography or SyPro orange thermal shift.

      The sentence now reads: “While the stability of UV-exchanged p-MHC complexes can be assessed using methods such as thermal shift assays and size-exclusion chromatography, the efficiency of peptide exchange is more difficult to quantify directly.”

    1. Author response:

      The following is the authors’ response to the original reviews.

      We thank you all for the careful evaluation of our manuscript and for the numerous constructive comments and suggestions. As noted by the reviewers, the study directly compares two distinct approaches for detecting m<sup>6</sup>A modifications using the same RNA input material. The inclusion of IVT and STM2457-treated RNA as negative controls, as well as the high-depth long-read datasets from two different cellular systems, enable robust analysis and interpretation of the data, providing a rigorous and reproducible analysis workflow and a valuable reference for the rapidly expanding community aiming to use Oxford Nanopore Technologies’ (ONT) latest flow cell chemistry and Dorado base calling tool.

      We have revised the manuscript according to this feedback and believe the changes have greatly improved the clarity and utility of the work. We have, where possible, addressed all the points raised and have further discussed or acknowledged those that involve broader technical considerations beyond the scope of the present study.

      Reviewer #1 (Public review):

      Summary:

      The authors set out to evaluate how accurately direct sequencing of RNA can identify and quantify several chemical modifications on RNA molecules, focusing primarily on m6A. A central goal of the work is to compare this approach with an independent chemical-based method (glyoxal and nitrite-mediated deamination of unmethylated adenosines (GLORI), using the same RNA samples, in order to assess reproducibility, false-positive signals, and sensitivity across a range of detection strategies. The authors further aim to demonstrate the biological utility of this approach by applying it to two human cell types, primary human fibroblasts and HD10.6 neurons. While the manuscript also reports detection of additional RNA modifications (pseudouridine and m5C), the depth of analysis and strength of controls are greatest for m6A, which forms the primary focus of the study.

      Strengths:

      A strength of this work is the direct comparison of two distinct measurement approaches performed on the same RNA input material; this has not been done in other recently published benchmarking studies evaluating the utility of the recent direct RNA sequencing for calling m6A. The authors systematically test multiple analysis models and show that, when appropriate filtering is applied, detection of modified sites is reproducible across software versions. The use of synthetic RNA standards and METTL3 inhibitors as negative controls helps to reinforce the overall results. The data show good agreement between the two methods at higher m6A modification levels, supporting the conclusion that direct RNA sequencing can reliably detect high-confidence modification sites. The authors also demonstrate that this approach can, in principle, provide information at the level of individual RNA variants (although only one example was provided), which is difficult to achieve with short-read methods. The methodology described here is likely to be useful to others seeking to apply similar approaches to identify and quantify m6A. The study also explores the detection of other RNA modifications, which highlights the broader potential of the approach, although these analyses are necessarily more exploratory given the more limited controls and data available.

      Weaknesses:

      Despite these strengths, several issues limit the interpretation of the results and should be clarified for readers.

      First, the authors appropriately address false-positive signals by estimating expected false-positive rates and by quantitatively comparing sequence motif enrichment before and after filtering. These analyses provide important support for the use of stoichiometry-based thresholds and demonstrate that filtering substantially improves specificity. However, even after filtering, a subset of detected sites remains outside the expected sequence context. It therefore remains unclear to what extent these non-canonical sites reflect genuine biology versus residual technical artifacts.

      The detected sites that were outside of the expected sequence context (0.1% of the sites per cell type) exhibited sensitivity to STM2457 treatment, supporting the conclusion that these sites represent genuine signals. This point has been clarified in the text (lines 424-455 and 563-578) and additional supporting data have been included in the supplementary figures (Supplementary Fig. S23 and S24).

      Second, claims regarding the ability of direct RNA sequencing to resolve modification patterns across different RNA variants are supported by very limited evidence. The conclusion that this approach provides superior isoform-level quantification relative to short-read methods is based largely on a single gene example. While this case is interesting, it does not establish how widespread or general this advantage is. A broader analysis indicating how many genes show isoform-specific modification patterns detectable by this method, and how often these are missed by the comparison approach, would be necessary to support a general claim.

      We thank the reviewer for this valuable comment. To strengthen this point, we have added two additional examples illustrating isoform-specific m<sup>6</sup>A modification patterns, as well as one monoexonic gene for comparison (new Supplementary Figure S22). KRTAP1-5 is a monoexonic gene with a single detectable isoform and shows that Dorado detects more m<sup>6</sup>A sites than GLORI. HSPA8, with five detectable isoforms, is a good example to show that two isoforms carry additional m<sup>6</sup>A sites not resolvable by GLORI. CITED2 has three detectable isoforms, and differential m<sup>6</sup>A patterns can only be resolved with Dorado. We adjusted the text accordingly in lines 395-401.

      Third, the biological interpretation of cell type-specific differences in modification levels remains underdeveloped. Although differences in modification stoichiometry are reported between fibroblasts and neuron-derived cells, the functional consequences of these differences are not addressed. It is unclear whether changes in modification levels are associated with differences in RNA abundance, stability, or translation. As a result, statements suggesting that these modifications fine-tune core cellular pathways are speculative and should either be supported with additional analyses or framed more cautiously.

      We have updated the text (lines 477-481) to ensure a more cautious interpretation of the observations.

      Related to this point, differences in gene expression between the two cell types are a potential confounding factor. The pathway enrichment patterns presented appear biased toward particular functional categories, but without clear control for differential gene expression, it is difficult to determine whether the observed enrichment reflects cell type-specific regulation of RNA modification or simply differences in which genes are expressed. Clarifying how background gene sets were defined for these analyses would help readers interpret the results.

      We thank the reviewer for raising this important point. For the KEGG pathway enrichment analysis, we used genes harboring shared m<sup>6</sup>A sites in both NHDF and HD10.6 cells as the input gene list, irrespective of their expression levels. We initially did not use a custom background gene set, which is also a valid point brought up by the reviewer. Hence, we repeated the analysis and used all genes expressed in both cell types (~13,000 genes) as background (i.e. excluding those only expressed in one cell type). We have revised the results (lines 467-468) and methods section (lines 740-749) accordingly. We replaced the plot in Figure 4H with the new plot.

      The manuscript also suggests broader differences in overall modification levels between cell types, but this is not validated using an independent global assay. An orthogonal measurement of total modification levels on polyadenylated RNA (for example, dot blot) would help place site-specific stoichiometry differences in a clearer biological context.

      We tried to assess global changes in modification levels using a dot blot assay. However, even when loading 2 µg of RNA per sample, we did not detect visible differences between DMSO- and STM2457-treated samples in either cell type, which we expected to serve as a positive control. This most likely indicates that the dot blot assay is much less sensitive than our DRS-based sequencing approach. However, as we agree that for making a statement about broader differences between cell types, orthogonal validation would be necessary. Accordingly, we have adjusted our statements in lines 44-46 and 477-481.

      Finally, the effects of the METTL3 inhibitor on these cell types are not fully characterized. While changes in m6A modification patterns are reported following treatment, the manuscript does not address whether the treatment affects cell growth or viability.

      Cell viability following STM2457 treatment was determined in NHDF and HD10.6 cells using the CellTiter-Glo® assay. HD10.6 cells are terminally differentiated and post-mitotic; therefore, proliferation/growth is not applicable to this cell type, and cell viability (assessed by CTG assay) is the relevant endpoint. We added the results, which showed no significant differences in either cell type, as a supplementary figure (Fig. S1). While we ensured that NHDFs showed normal growth behaviour when treating them with STM2457, because HD10.6 cells are non-proliferative, we assessed cellular health in each of the experiments conducted. We updated a description of the assay in the methods section, lines 637-643, and in the results section (lines 137-138).

      Appraisal of conclusions and impact:

      Overall, the study provides an informative technical assessment of direct RNA sequencing for modification detection and establishes clear conditions under which the method performs well. The evidence strongly supports conclusions related to technical benchmarking, reproducibility, and the importance of filtering and controls, particularly for m6A. In contrast, conclusions regarding isoform-specific regulation and cell type-specific biological roles of RNA modification are less well supported by the data currently presented, and would benefit from either additional analysis or more restrained interpretation.

      The work is likely to have a meaningful impact as a practical reference for researchers using direct RNA sequencing, particularly by clarifying sources of false positives and the value of appropriate controls. With clearer limits placed on biological interpretation or more data presented in support of the biological interpretation, the study would serve as a valuable reference for users seeking to apply these technologies reliably.

      We thank the reviewer for this positive evaluation of our work. To address major concerns, we have adjusted our interpretation of the biological findings throughout the manuscript to better reflect the scope of the presented data. We believe these revisions more clearly distinguish the technical benchmarking aspects of the study from the biological insights that need further investigation.

      Reviewer #2 (Public review):

      Summary:

      In this study, the authors aim to establish a calibrated framework for detecting RNA modifications using long-read sequencing and apply it to compare modification patterns between fibroblasts and neuron-like cells. The work combines long-read sequencing, in vitro transcribed controls, methyltransferase inhibition, and comparison to an orthogonal sequencing-based method in an attempt to derive filtering strategies that reduce false positive modification calls. The authors further apply this framework to explore differences in modification levels between the two cell types. The resulting dataset may be of interest to researchers working on RNA modification detection using long-read sequencing technologies. Independent datasets across additional cellular systems can be useful for benchmarking computational methods and evaluating the behavior of modification detection models. However, the conceptual advance of the analytical framework presented here remains somewhat unclear, as many aspects of the analysis closely resemble strategies that have already been described in recent benchmarking studies.

      Strengths:

      A clear strength of the study is the generation of a relatively large long-read sequencing dataset together with several useful experimental controls, including in vitro transcribed RNA and pharmacological inhibition of the methyltransferase enzyme responsible for installing this modification. These controls are helpful for illustrating the challenges associated with distinguishing high-confidence modification sites from background signals. The inclusion of two different human cellular systems also provides an additional dataset that may be useful for benchmarking and cross-validation in the field. The study addresses a practically relevant question for the community, namely, how to reduce false positive calls in long-read sequencing-based RNA modification analyses.

      Weaknesses:

      The main weakness of the manuscript is its limited methodological novelty. Much of the analytical framework presented here closely follows benchmarking strategies that have already been described in recent studies of RNA modification detection using long-read sequencing. Several previous studies have evaluated modification-aware basecalling approaches, discussed the need for stringent filtering strategies, and compared long-read sequencing-based predictions with orthogonal mapping approaches. The manuscript would therefore benefit from a deeper engagement with the recent benchmarking literature and a clearer explanation of what conceptual or methodological advance the present study provides beyond these earlier analyses.

      We thank the reviewer for this constructive comment. At the time our study was conducted, relatively few benchmarking studies addressing these methodological aspects were available, and the analytical approach and thresholds applied in our study were therefore established independently of these reports. Several relevant studies (some initially as preprints) subsequently emerged within a relatively short period. Now that these studies are available, we have considered their findings, including the thresholds and filtering criteria applied, and have incorporated the relevant comparisons and methodological considerations into the revised manuscript. We have rewritten the introduction section (lines 99-117) and the discussion (lines 537-546, 547-549, 553-562) to incorporate newer studies and correctly integrate our study into the field. Furthermore, we consider these findings not to be supportive of our work, as they strengthen the overall interpretations and guidelines for ONT DRS users.

      A second concern relates to the filtering strategy that forms the core of the proposed workflow. The manuscript applies several thresholds, including modification probability, stoichiometry, and read coverage cutoffs, but it is not clearly explained how these thresholds were determined. It remains unclear whether these cutoffs were derived from statistical calibration, empirical optimization using the presented dataset, or adopted from previous studies. Because the downstream conclusions depend strongly on these filtering choices, a clearer methodological justification would strengthen the work and help readers assess the robustness of the proposed framework.

      We thank the reviewer for raising this important point. For the modification probability thresholds, we compared the distribution of modification probabilities in the biological samples with that observed in the IVT controls. In the revised manuscript, we have integrated a new statistical framework that enables an unbiased determination of modification probability cutoffs for each dataset (see lines 174184, Methods, as well as Fig 2 and Supplementary Figs 5, 8, 9 and 10). We further report error rates relative to IVT across different modification probability cutoffs and probability ranges (lines 186-200). The validread coverage threshold was introduced as an additional safeguard against sites supported predominantly by reads that were neither confidently called as the canonical nucleotide nor confidently assigned as modified (since valid coverage includes only reads supporting the canonical base or the corresponding modification above the selected probability threshold (≥0.98 or ≥0.99, depending on the modification) (lines 233-240). Finally, the stoichiometry cutoff was also informed by comparison with the IVT controls. Although stringent modification-probability filtering substantially reduced background, the majority of residual sites detected in the IVT controls occurred at low modification proportions, particularly below 10%. We therefore introduced the stoichiometry threshold to further distinguish biological modification signal from low-level background calls observed in the unmodified IVT reference (lines 241-249).

      The interpretation of the comparison between the two modification detection approaches also appears somewhat overstated. Differences between the methods are frequently interpreted as evidence that one approach produces large numbers of false positive calls, but the analyses presented do not fully exclude alternative explanations such as differences in sensitivity, sequencing depth, or methodological biases. A more cautious interpretation of these discrepancies would therefore be appropriate.

      Some discussion points also appear speculative. In particular, certain interpretations propose mechanistic explanations without presenting analyses that would allow these possibilities to be distinguished. Such interpretations would benefit from either additional supporting analyses or more cautious phrasing.

      We have revised the relevant sections accordingly to provide a more cautious interpretation of these findings (lines 583-592).

      From a methodological perspective, the statistical robustness of the thresholds used throughout the analysis could also be discussed in more detail. Given the relatively modest read coverage cutoff applied in the study, low stoichiometry estimates may be strongly influenced by sampling noise, and fixed stoichiometry thresholds may therefore not correspond to a consistent level of confidence across sites. In addition, the manuscript relies heavily on fixed modification probability cutoffs to define high-confidence calls, but it does not discuss whether these scores are statistically calibrated or how they relate to expected error rates. Neural network outputs are often not well-calibrated probabilities, and interpreting these values as direct confidence estimates can therefore be problematic. Finally, modification detection models trained on known modification sites may capture sequence-context patterns present in the training data, meaning that motif enrichment or positional distributions along transcripts may partly reflect model biases rather than purely biological signals. A brief discussion of these limitations would help readers better interpret the robustness of the proposed filtering strategy and the downstream biological conclusions.

      We thank the reviewer for raising these important methodological considerations. We acknowledge that modification proportion estimates, particularly at sites with relatively low coverage and low modification proportions, may be influenced by sampling variability and may not accurately reflect the true modification proportion.

      In terms of our filtering strategy, we performed false-positive rate analyses across multiple modification probability thresholds using repeated subsampling of biological and modification-free IVT datasets. In addition, we performed an independent change-point analysis to identify where modification signals in biological samples diverged from the IVT background. These analyses, together with the reduction in high-probability m<sup>6</sup>A calls following METTL3 inhibition, provide complementary empirical support for the applied filtering criteria.

      We also acknowledge that sequence-context features learned by modification-detection models may influence predicted motif distributions. We therefore performed additional analyses of non-DRACH predictions, identifying both technical sources of erroneous calls and non-canonical sites consistent with genuine biological modifications, including STM2457-sensitive sites.

      Overall, while the dataset may be of interest to the community, the extent to which the study advances current methodological understanding beyond recent benchmarking efforts remains limited.

      We thank the reviewer for their comments and critiques. The revised version of the manuscript has addressed these points (as detailed above), and we consider the fact that other recently published benchmarking studies come to broadly similar conclusions provide additional support to our work.

      Notably, however, our study remains the only one to use the same RNA as input for distinct sequencing approaches (i.e. nanopore vs. GLORI-Seq).

      Minor comments:

      The discussion of the "DRACH" versus "all-context" outputs would benefit from greater technical precision. The statement that the number of sites within DRACH motifs identified by the all-context approach was nearly identical to the number reported by the DRACH model may suggest that these outputs derive from fundamentally different predictive models. As I understand it, the underlying neural network is the same, whereas the distinction lies primarily in the classification context. Clarifying this explicitly in the manuscript would improve interpretability and avoid potential confusion for readers.

      We have updated the text accordingly to ensure greater technical precision (lines 342-350).

      The manuscript compares results obtained with different basecalling and modification settings but refers primarily to Dorado software versions. This may be misleading, as software version and model version are not necessarily equivalent. Different basecalling or modification models can be used with the same software release, and newer software versions may still use older models. For clarity and reproducibility, the authors should report the exact basecalling and modification model names used in the analyses rather than referring only to the Dorado software version.

      We thank the reviewer for highlighting this distinction. We have revised the manuscript and figures accordingly and clarified the specific Dorado software version as well as the individual models used for each analysis (lines 315-330).

      Reviewer #2 (Recommendations for the authors):

      (1) To strengthen the methodological robustness of the proposed framework, the authors should clarify how the filtering thresholds used throughout the analysis were determined. If these thresholds were derived empirically from the present dataset, the authors could consider providing additional analyses demonstrating their robustness (for example, by showing how key results change across different probability or stoichiometry cutoffs). If the thresholds were adopted from previous studies, the relevant sources and the rationale for using them should be explicitly cited.

      We thank the reviewer for this recommendation. As outlined before, the filtering thresholds used in the analysis were empirically informed by comparison of the biological samples with the unmodified IVT controls. In the revised manuscript, we have implemented a statistical framework that enables the identification of appropriate modification probability cutoffs on a per-sample basis. Specifically, we report error rates relative to the IVT controls across different modification probability cutoffs and probability ranges (lines 186-200), together with statistically supported identification of modification probability cutoffs for each biological sample (by comparing with the corresponding IVT reference, lines 220-230). These analyses support the modification probability thresholds applied in the downstream analyses.

      We have also clarified the rationale for the additional filtering criteria, such as valid coverage and stoichiometry cutoffs. (lines 233-240 and 241-249).

      (2) Because the analysis relies strongly on modification probability scores, the authors may also wish to discuss how these scores relate to expected error rates. If possible, providing an analysis of how false positive rates behave across probability thresholds using the IVT controls included in the study could help readers better interpret the meaning of the chosen cutoff values.

      We thank the reviewer for this suggestion. As described above, we have now directly assessed how false-positive rates vary across modification probability thresholds using the unmodified IVT controls. In the revised manuscript, we report error rates relative to the IVT controls across a range of modification probability cutoffs and within discrete probability intervals (lines 203–213). These analyses demonstrate that false-positive rates decrease with increasing modification probability and provide an empirical basis for interpreting the selected probability thresholds.

      (3) For the comparison between the two modification detection approaches, the authors may consider providing additional analyses that clarify the source of discrepancies between the methods. For example, examining whether differences depend on read coverage, sequence context, or site stoichiometry could help readers better understand the conditions under which the two approaches converge or diverge.

      Thank you for this suggestion. We agree that analyses of read coverage, sequence context, and site stoichiometry could help explain the differences between the two methods. However, our current results suggest that the main reason for the discrepancy is the limited conversion efficiency of the GLORI dataset (see Fig. 3D). To properly assess the effects of coverage or sequence context, we would need a higher-quality GLORI dataset with better conversion efficiency. Generating such a dataset and repeating the analysis was beyond the scope of this study. We have therefore revised the text to make this limitation clearer and adjusted our interpretation accordingly (lines 343-361 and 583-593).

      (4) The interpretation of modification patterns between fibroblasts and neuron-like cells could also be strengthened by additional analyses that account for potential confounding factors such as differences in transcript abundance, transcript coverage, or gene expression levels between the two datasets.

      We thank the reviewer for this important suggestion. Our comparison was restricted to m<sup>6</sup>A sites shared between both cell types, minimizing potential biases from cell type-specific transcript detection. We agree that transcript abundance, coverage, and the effects of m<sup>6</sup>A on transcript stability and translation should be considered to assess the biological significance of these differences, but such analyses are beyond the scope of this study. We have therefore rephrased our statements more cautiously (lines 478-482).

      (5) In the description of the modification detection models, the manuscript would benefit from clearer reporting of the exact basecalling and modification model names used in the analyses. Because software version and model version are not necessarily equivalent, specifying the model identifiers would improve clarity and reproducibility.

      As mentioned above, we have revised the manuscript and figures accordingly and clarified the specific basecalling and modification models used for each analysis (lines 315-330).

      (6) The manuscript would also benefit from clarifying the relationship between the "DRACH" and "allcontext" outputs, particularly whether these represent distinct predictive models or the same model applied in different classification contexts.

      As mentioned above, we have revised the corresponding paragraph to avoid ambiguity regarding the models used in each analysis (lines 315-330).

      (7) Finally, the manuscript would strongly benefit from a more detailed discussion of the relationship between the present analysis and previous benchmarking studies of long-read RNA modification detection, which would help readers understand how the current work relates to and extends existing efforts in the field.

      We thank the reviewer for this helpful suggestion. We have expanded the discussion to better place our findings in the context of new benchmarking studies (538-547, 554-563).

      Reviewer #3 (Public review):

      In this study, the authors aim to establish a calibrated framework for identifying RNA chemical marks from direct RNA sequencing data using a modification-aware basecalling workflow, with a particular focus on N6-methyladenosine. By combining native RNA sequencing with an unmodified control transcriptome, enzyme inhibition, comparison across multiple software versions, and orthogonal validation using an independent mapping approach, the authors seek to define a best-practice pipeline for reducing falsepositive calls and improving confidence in quantitative interpretation across cell types.

      A major strength of the work is the rigor of the benchmarking strategy. In particular, the inclusion of an unmodified control transcriptome is both important and useful, and the study provides compelling evidence that this control remains necessary for robust interpretation, despite being omitted in many current workflows. The comparison across software versions and the matched analysis with an independent sequencing-based approach also substantially strengthen the evidence presented. The work therefore makes a valuable contribution to the community by offering a more stringent analytical framework that will likely be broadly useful to groups applying native RNA sequencing to study RNA chemical marks.

      The evidence supporting the main conclusions is solid overall. The authors convincingly show that stringent filtering substantially reduces false-positive calls and improves agreement with orthogonal approaches, particularly at highly modified sites. The observation that many sites are conserved across cell types, while showing differences in relative modification levels, is also supported by the presented analyses.

      At the same time, several conceptual issues limit the strength of some downstream interpretations. Most importantly, the manuscript repeatedly refers to the reported values as "stoichiometry," whereas the underlying software output is more appropriately interpreted as a statistical estimate of the proportion of aligned reads classified as modified. This distinction is important because the conclusions regarding celltype differences rely on quantitative comparisons of these values. In addition, the current calling framework depends on successful canonical base assignment before modification calling, which raises an important limitation: sites with the strongest signal deviations may be underrepresented if they are more likely to be miscalled during basecalling. This issue may be especially relevant for RNA marks that induce stronger mismatch signatures than N6-methyladenosine and should be more explicitly discussed. Overall, the authors largely achieve their primary aim of establishing a more rigorous and broadly applicable analytical framework for direct RNA sequencing-based modification detection. The work is likely to have a meaningful impact on the field, particularly by reinforcing the importance of appropriate negative controls and benchmarking standards. With clearer framing of the quantitative outputs and explicit discussion of current software limitations, this study will serve as a highly useful resource for the community.

      Reviewer #3 (Recommendations for the authors):

      I have several conceptual and methodological concerns.

      (1) Please avoid the term "stoichiometry". A major concern is the repeated use of the term "stoichiometry." In the context of Dorado-based nanopore calling, this is fundamentally a statistical estimate of the proportion of aligned reads classified as modified, rather than a direct biochemical measurement of true molecular stoichiometry or occupancy. I strongly recommend replacing this term throughout the manuscript with:

      - predicted m6A/A proportion

      - relative modification proportionThis distinction is especially important because the manuscript draws biological conclusions from differences in these values across cell types. At present, the language risks overstating the quantitative certainty of the method.

      The reviewer is correct, and where applicable (text, figures), we have replaced the word “stoichiometry” with “predicted m<sup>6</sup>A/A proportion”.

      (2) Canonical basecalling dependency requires explicit discussion.

      A key conceptual concern is that the modification caller requires the base to first be correctly called as A before assigning it as m6A. This point needs to be explicitly addressed in the manuscript. Because the proportion is being calculated only from reads that are first aligned and called as canonical A, I strongly encourage the authors to include a mismatch analysis and explicitly frame the reported values as proportions derived only from correctly aligned A-containing reads. This raises an important question: are the strongest signal-distorting sites being systematically excluded from analysis because they are more likely to be basecalled incorrectly? This is an important limitation of the ONT Dorado/Modkit framework and should be discussed directly.

      We thank the reviewer for raising this important point. We agree that the reported modification proportions do not capture all reads overlapping a given position. The proportions are calculated from reads in which the corresponding base is basecalled as an A and is confidently assigned as either canonical A or m<sup>6</sup>A above the selected modification-probability threshold. Reads in which the position is basecalled as a different nucleotide, contain a deletion, are assigned another modification, or have an m<sup>6</sup>A probability below the selected threshold are therefore not included in the proportion estimate. For the DRACH context model, reads containing a non-matching base at other positions within the required motif context are likewise excluded from modification calling. We have now clarified this limitation explicitly in the revised manuscript (lines 285-296). In addition, to assess the potential magnitude of this effect, we performed a mismatch analysis examining the percentage of reads in which the reference A was basecalled as another nucleotide and evaluated its relationship with the predicted m<sup>6</sup>A/A proportion across sites in our filtered dataset (lines 297-313). This analysis provides information that is not captured by the predicted modification proportions.

      (3) The concern above (2) is likely stronger for Pseudouridine and Inosine RNA editing.

      I think this issue is likely even more important for Pseudouridine and Inosine RNA editing than for m6A. For these modifications, the basecalling error at the modified site is expected to be substantially stronger than for m6A, which may leave very few aligned reads available for downstream proportion calculations. This could potentially explain why the authors require a higher modification probability threshold for these marks. I would strongly encourage the authors to explicitly discuss whether this basecalling dependency contributes to the need for the {greater than or equal to}0.99 threshold and whether this introduces a systematic detection bias.

      To investigate the potential impact of basecalling errors on modification proportion estimates, we examined alternative nucleotide calls at modification sites, including pseudouridine and inosine sites, focusing on positions where non-reference basecalls accounted for ≥25% of the reads overlapping the site (lines 297-305). At pseudouridine sites, the predominant alternative basecall was C, whereas at inosine sites, G was most frequently observed. These results indicate that modification-associated basecalling errors may lead to the exclusion of a fraction of reads from downstream modification proportion calculations. Consequently, the reported modification proportions may be underestimated at sites where the presence of a modification strongly affects canonical basecalling, introducing a potential detection bias.

      Importantly, however, the modification probability thresholds used in our analysis were derived empirically by comparing modification probability distributions in the biological samples with those observed in the corresponding IVT and STM2457-treated controls. Basecalling accuracy was not considered in establishing these thresholds.

      (4) Need better framing of multiple modifications on the same transcript.

      In the Introduction, I would encourage the authors to better position nanopore DRS relative to short-read approaches by explicitly noting that short-read methods are also limited in their ability to resolve multiple modifications on the same transcript molecule. This is an important conceptual advantage of native longread sequencing and deserves clearer emphasis early in the manuscript.

      We agree that the ability to examine the co-occurrence of multiple modifications on individual RNA molecules represents an important distinction between nanopore DRS and short-read approaches. We have therefore revised the Introduction to explicitly note the limitation (lines 79-80, 83-84).

      (5) Clarify unclear experimental step.

      The stoichiometry distribution experiment (lines 189-195) in the Results section is difficult to follow.

      We thank the reviewer for pointing this out. We have revised and restructured this section to more clearly describe the stoichiometry analysis (lines 255-274).

      (6) Discussion of non-DRACH sites.

      The manuscript interprets many non-DRACH GLORI sites as likely false positives. While this is a reasonable interpretation, I would like the authors to also discuss whether true cellular m6A may exist at non-DRACH motifs, and whether any non-canonical sites identified by nanopore DRS may represent biologically real events rather than technical artifacts.

      We agree and have added a new analysis (Fig. S23 and S24) addressing this point. Most non-DRACH calls derive from technical causes (SNPs, homopolymers, proximity to true DRACH sites), but a subset conforming to DRAC motifs, e.g., are STM2457-sensitive, indicating they likely represent genuine METTL3-dependent m<sup>6</sup>A sites. We have added a description of the new figures in the results section 425456) and discuss this further in lines 564-579.

      This is especially important given emerging evidence that non-canonical motifs can occasionally occur in vivo.

      We thank the reviewer and have added corresponding data and discussion, as pointed out above. While most all-context non-DRACH calls reflect similar technical artifacts, we identify STM2457-sensitive GGAUU sites, e.g., and a distinct STM2457-insensitive, METTL16-like class (e.g., ACAGA in MAT2A), supporting that some non-canonical calls represent true m<sup>6</sup>A sites.

      Regarding lines 236-240: Are there also sites from nanopore sequencing that are unexpectedly positive?

      We thank the reviewer for this question and refer to our newly added figures (Figure S23 and S24) and explanations described above.

      (7) Strongest point of the paper. I want to emphasize that one of the strongest contributions of this study is its clear demonstration that the modification-free transcriptome control is necessary. This should be stated even more explicitly as a best-practice recommendation, as the field increasingly trends toward analyses that omit such controls.

      We thank the reviewer for highlighting this important aspect of our study. We have strengthened this point in the Discussion (lines 610-611) and now more explicitly recommend using a modification-free transcriptome control as a best practice for reliable RNA modification detection by DRS.

      Overall, I find this to be a strong manuscript, with its methodological rigor being a major strength. Addressing the concerns above would substantially improve both the clarity and interpretability of the work.

      We thank the reviewer for their positive assessment and constructive feedback. We believe that the revisions have improved the clarity of the manuscript and the interpretability of our findings.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      The authors aim to study mutational paths connecting WW domains with different binding specificities. Their approach combines an unsupervised sequence generative model based on RBMs with a path-sampling algorithm. The key result is that most intermediate sequences along the designed transition paths retain measurable binding activity in wet-lab assays, whereas paths containing the same mutations introduced in a randomized order are largely non-functional. This difference is attributed to epistatic interactions captured by the RBM model.

      Strengths:

      Exploring mutational paths in high-dimensional protein sequence space is a challenging problem. The computational framework used here is state-of-the-art and is strengthened by systematic experimental characterization of binding activity. The study is comprehensive in scope, including multiple transition paths both within and across WW specificity classes, and the integration of modeling with high-throughput experimental validation is a clear strength.

      Weaknesses:

      A major concern is whether the stated goal of specificity switching is fully achieved. Along the sampled transition paths, most intermediate variants appear to retain specificity close to either the initial or the final class, rather than exhibiting gradually shifting specificity. For example, in Figure 4G (Class I to Class II/III), binding appears largely binary, with intermediates behaving similarly to one of the endpoints. A similar pattern is observed in Figure 3H for the Class I to Class IV transition, where binding responses are close to 0 or 1. In this sense, the specificity-switching objective is only partially realized by assigning two endpoints with different specificity. This raises a broader conceptual question: is it possible that different WW specificities evolved from a common ancestor without passing through intermediates that exhibit mixed or intermediate specificity? If so, then inferring specificity-switching pathways purely from extant natural sequences may be fundamentally challenging.

      We have added a sentence in the introduction to underline these points, in particular: Is the specificity switch happening through abrupt or more gradual specificity changes? Does it correspond to a bottleneck in sequence space?

      Reviewer #2 (Public review):

      This is an extremely important work that shows how one can use generative models to construct specificity-switching mutational paths in complex fitness landscapes. The experimental evidence is very clear, and the theoretical tools are innovative.

      The work will likely have a deep impact on future research aimed at understanding how evolution navigates fitness landscapes as well as reconstructing ancestral sequences.

      The manuscript is extremely clear and well written, the experimental evidence is strong, and the methods are clearly described, so I do not have major issues to raise. A few minor issues are listed below.

      (1) I consider the WW domain as an 'easy' case from the point of view of generative modelling. The domain is rather short, epistatic effects are not very strong (e.g. Boltzmann learning usually converges very quickly to a very paramagnetic state), and the resulting models are well interpretable (e.g. the hidden units of the RBM correlate well with subclasses).

      This is not always (not often?) the case, however. In more complex proteins, the learning procedures can be slower and the resulting models less interpretable. Just for completeness, perhaps the authors could comment on the generality of the results and what they would expect for other systems based on their experience.

      We have added a sentence in conclusion to discuss the application of our framework to more complex and longer proteins.

      (2) In Section 3.3, the authors say that direct paths connecting Class I and Class IV behave similarly to indirect paths, despite having lower scores according to the RBM. How generic is this? Does it also happen for other classes? This might be an important point to address, as direct paths are easier to sample.

      We have added a sentence in conclusion to emphasize the need for a more exhaustive study of non-direct vs direct paths.

      (3) The path shown in Figure 4 goes through a region of non-functionality around sequences 18-19. It seems that the sample path is basically exploring the functional regions for Class I and Class II/III separately, trying to approach the other class, but then it can't really make the switch.

      By contrast, the path going from Class I to Class IV seems able to perform the functional switch in a single step (20-21) without losing too much of the function.

      Perhaps the authors could better comment on this? Is this a limitation of the sampling method, or a fundamental biological fact?

      We now better stress and discuss the comparison between Class I to Class IV paths and Class I to Class II paths in the conclusion.

      (4) On page 12, it is stated that the temperature was chosen to 1/3 to maximize the score. This is important and should be mentioned earlier (I didn't notice it until that point).

      We have added a sentence in Section 3.2 on the lowering of the sampling temperature to 1/3 to obtain high-scores sequences.

      (5) On page 13, it is stated that: "However, the scores of the ancestral sequences along the phylogenetic pathways assigned by the RBM are significantly lower than the ones of the RBM-designed sequences. This result is expected as ASR reconstruction does not take into account epistasis, differently from RBM, and we expect ASR sequences to generally be of lesser quality."

      I was very surprised by this result. My own experience with ASR shows that, on the contrary, sequences found by ASR (via maximum likelihood) tend to have high scores in the (R)BM, and tend to be more stable than extant sequences. I attribute this to the fact that ASR typically finds a "consensus" sequence that maximizes the contribution to the score coming from the fields (the profile), which is typically dominant over the epistatic signal, resulting in a bigger score. Maybe the authors did not use maximum likelihood in the ASR? Some clarification might be useful here.

      We have updated Figure 5 with shuffled and ASR sequences, and added Suppl Figure 7 to compare the score of the consensus sequences and the ones of the most ancestral nodes along the path in the ASR reconstruction with the natural scores.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      I suggest that the authors either more clearly acknowledge that smooth specificity switching is not fully demonstrated or reconsider the use of "specificity switching" in the title. An alternative framing could emphasize the study of mutational paths connecting different specificity classes, without implying a transition in specificity.

      One of the main questions motivating our study was precisely to investigate where along the path and how the transition in specificity happens, i.e. through intermediate that exhibit mixed or intermediate specificity (which we had defined as ‘smooth’) or more abruptly.

      For class I-IV paths, we observe a smooth specificity switch with some cross-specificity of the sequences designed in the switching-specificity region, with low but significant binding responses not only towards class I and IV ligands (the extant sequences specificity class) but also to ligand of class II. On the contrary, in the paths from class I to class II-III, we observe the abrupt switch, at the predicted specificity boundary, with sequences with a clear response to one or the other peptide. This abrupt switch requires the change of several amino acids determining the specificity class, and binding is loss when this change is incomplete.

      We understand that the term “smooth” to design the cross-reactivity of the few sequences in the predicted ‘switching boundary zone’ could be misleading, so we have removed it from the abstract.

      Moreover, we have added a sentence in introduction to motivate the study of where and how the specificity transition takes place, and two sentences in conclusion about the identification of where the specificity switching take place along the path, and to underline the difference between the paths from class I to class IV and the ones from class I to class II/III.

      It is striking that all scrambled paths are non-functional. Given that sequences adjacent to the end states differ by only a few mutations, one might expect at least some of these variants to remain functional, as small numbers of mutations often do not abolish activity. The authors should discuss this result in greater depth and more clearly explain how it uniquely supports the role of epistatic interactions.

      The sampling of the scrambled paths is not strictly random. Along the scrambled path the mutations are inserted in the reverse order; the scrambled paths are therefore chosen to maximize the sequence divergence between the unscrambled sequences (in which the mutation is predicted to be functional by the path sampling algorithm) and the one in which it is tested in the scrambled path. The fact that the background matters is a clear sign of epistasis.

      We have better explained this important point in Section 3.3, where we introduce scrambled paths.

      Specificity class annotations are inferred using RBM latent weights. However, as shown in Figure 2E, the boundaries between classes in latent space are not sharply defined. It would strengthen the analysis to validate these class assignments using alternative representations, such as clustering in the latent space of a VAE or embeddings from protein language models, to assess whether the inferred class boundaries are robust and consistent.

      Beyond RBM weights, the boundaries between clusters have been assessed by inferring two different RBMs (which we call class specific RBM) on class specific MSA, such models validated the robustness of the boundaries. Most importantly, we have shown that the classification is consistent with experiments.

      To further answer this comment, we have added Suppl. Figures 7 and 8, showing that a simple PCA approach, as well as VAE agree with our clustering.

      In Figure 3C and Figure 3F, variants 18 and 19 appear to represent transition states located in regions of latent space with little or no training data. Intuitively, such variants would be expected to have a lower probability than variants 22, which lie in a high-density region of the RBM model. However, this expectation is not reflected in Figure 3C. A similar issue appears in Figure 4. The authors should carefully re-examine these results and clarify whether this behavior arises from the model, the scoring procedure, or a potential error.

      We confirm that variants 18 and 19 in mutational path between classes I-IV have larger scores than the class IV wild-type domain. We have attributed the low score of this class IV wild-type (the extant sequence) to its smaller structural stability, as discussed in Sec 3.3 and with Supplementary Figure 3.

      The key point here is that the scores of Natural sequences are spread, as shown with the histogram in Fig. 5 (green distribution), corresponding to more or less stable natural protein. The RBM model (with a low sampling temperature favoring higher RBM scores) is able to generate artificial sequences far away in sequence space (i.e. with high Hamming distance with respect to natural one), while keeping high scores. The functionality of designed proteins with high RBM scores has been demonstrated in previous work by some of us, e.g. [Malbranke et al PLoS Comp Bio 2026], [Huot, Monasson, Cocco Cell system 2026], [Fernandez-de-Cossio-Diaz Nature Communication 2026], building up on similar results for BM models [Russ et al Science 2020].

      We have now clarified the point of the sampling at low temperature earlier in the manuscript in Section 3.2.

      Reviewer #2 (Recommendations for the authors):

      (1) In Figure 2 F-G, maybe a histogram of the scores of natural sequences could be added for comparison.

      We have added the histogram of scores of natural sequences in figure 5, where we discuss the scores of the generated sequences for the different paths.

      (2) In Section 3.4, "(Wild type 1YWI or formin binding protein)" is not clear; there might be a typo. Please check

      We do refer to Formin-binding protein 1, also known as FNBP1. We have reformulated the corresponding sentence.

      (3) On page 16 at the end of section 4, the authors could consider citing "Integrating experimental feedback improves generative models for biological sequences" by Calvanese et al. among the active learning methods.

      Thanks for suggesting to cite this very relevant work. We have added the reference.

      (4) Reference 78 is stated "in preparation (2019)", I guess this is a mistake and could be fixed.

      The reference has been updated.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Changes made independently of the reviewers' comments

      In addition to the revisions described below, we have made the following three changes during the revision process. None of them affects the overall claims of the paper.

      (1) Removal of the blebbistatin data. The blebbistatin experiments (Figure 3f and h in the original manuscript) did not reproduce in repeated trials. We have therefore removed these data, together with the related descriptions in the Results, Discussion, and Materials and Methods.

      (2) Removal of the pan-KRT6 KO-2 data. The original manuscript presented two pan-KRT6 KO cell lines. We subsequently found that an insufficient number of biological replicates had been obtained for KO-2, although its results were consistent in direction with those of KO-1. We have removed the KO-2 data and renamed pan-KRT6 KO-1 as pan-KRT6 KO.

      (3) Revised statistics. As described in our response to Reviewer #1's comment (2), we re-analyzed the quantitative data using a generalized linear model that accounts for experimental batch. With this analysis, the effect of ruthenium red on cell exit (Figure 4b) and the effect of one TGF-β receptor inhibitor on cell exit (Figure 3e) no longer reached statistical significance. The corresponding descriptions in the Results have been amended.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      The study describes the migration of epidermal keratinocytes through porous membranes and observes a unique size selection whereby only on 3-micron membrane are keratinocytes able to migrate and reform an intact epidermis. The authors propose that the model replicates three cell states of the intact epidermis, EMT, and MET. They also show that this response depends on the actin cytoskeleton and Piezo1, and the migration could be stimulated with TGF-beta ligands.

      Strengths:

      Strengths of the study include the establishment of a simple yet robust in vitro model that captures all three cell states, which could be useful for future investigation of wound healing or metastasis. There is also good characterisation of the pore size effects, providing some interesting observations about the physical regulation of keratinocyte migration. The images and presentation are clear.

      Weaknesses:

      (1) Some of the terminology would benefit from better definition or refinement. Triphasic suggests different physical behaviours (e.g. liquid-liquid phase separation) rather than cellular properties. Perhaps it would be better to refer to these as cell states or to describe the model more specifically as an invasion or EMT model. Likewise, the term 'reciprocating' implies two-way communication, but it is used to describe two-way migration or oscillating migration. Here, perhaps oscillatory would be clearer.

      We appreciate the reviewer’s comment. According to the reviewer’s suggestion, we have revised the title, abstract, and main text to avoid the terms “reciprocating” and “triphasic” and have instead adopted “oscillatory” and “three-compartment,” respectively.

      (2) The quantification and statistical analysis of key results could be improved. Notably, quantification of immunostaining in Figures 1 and 2 would strengthen core findings, and greater detail is needed on the sample sizes and number of experiments used for statistical analysis. These details are missing or only appear to N=1 in some places.

      We have added the quantification and statistical analysis to the revised manuscript. We realized that some of the data in the original manuscript combined technical and biological replicates. Therefore, we have revised the statistical analysis and presented the sample size in each experiment in the revised manuscript.

      (3) There is an attempt to analyse the underlying molecular mechanisms, but these studies lack depth and detail. For example, it is not clear how actin, keratins, and piezo1 communicate to regulate cell migration. Are they acting directly on EMT genes such as SNAI1 or through changes in cell mechanics and cell-cell adhesions? Likewise, is TGF-beta signalling active in the system (e.g. nuclear pSMAD during cell migration)? As a result, the new biological insight is somewhat limited and confirms much of what is known about these pathways in keratinocyte migration.

      We have elaborated these matters in the Discussion section of the revised manuscript. Unfortunately, we were not able to specifically determine if nuclear pSMAD is present in the cells within micropores, due to technical issues described below. However, as TGF-β inhibition did not affect the entry into and the exit from the micropores (Figure 3b, e), TGF-β signaling is unlikely to be essential for this process.

      Reviewer #2 (Public review):

      Summary:

      The manuscript by Nohara et al. presents a novel 3D assay that allows for stratification of epithelia, active EMT through small pores, and active MET. They show that 3 µm pores allow for keratinocytes to sample the pore through filopodia and upregulate EMT genes to transverse the pores to the other side of the membrane where EMT genes are downregulated as the cells re-establish stratified epithelia. The TGFbeta pathway and actin polymerization promote the movement of cells into the pores and Piezo1 and KRT6 actively block this movement. This work provides a novel 3D assay that is likely to become a benchmark to analyze these processes using a more complex system than other current culture-specific EMT and MET assays.

      Strengths:

      The strengths of the manuscript include the foundational analysis of the pathways involved in establishing the tri-phasic epithelium. The authors have incorporated live imaging, drug studies, KO analysis, and RNA sequencing to show the relevant pathways involved.

      Weaknesses:

      While the authors provide strong evidence that the tri-phasic epithelium represents the EMT process, the MET process is largely relegated to the absence of EMT genes. It would be interesting to know how the stratified MET epithelia submerged in the media is similar or different from the stratified epithelia at the air-liquid interface.

      We appreciate the reviewer's comment and agree that the comparison between the MET-derived epithelium beneath the membrane and the original epithelium at the air–liquid interface is an intriguing question. Our current data provide partial insight: the epithelium beneath the membrane re-expressed E-cad (Figure 1d) and showed laminin β3 deposition comparable to that of the epithelium above the membrane (Figure 1—figure supplement 1e), indicating that it re-establishes at least some features of an epithelial tissue. However, it also retained elevated Vim and N-cad relative to the epithelium on the 0.4-µm-pored membrane (Figure 1—figure supplement 1b, c), suggesting that the MET is not complete. A systematic comparison, including barrier function and terminal differentiation markers, would require a dedicated study, which we plan to undertake.

      Reviewer #3 (Public review):

      Summary:

      The authors established an experimental system that reproduced three-dimensional triphasic epithelia, i.e., the original epithelium, its EMT, and MET. Keratinocytes (KCs), skin epithelial cells, placed on a microporous membrane migrated through 3.0-um or larger micropores. The 3.0-um-pored membrane induced an epithelial structure with three states: stratified KCs above the membrane, KCs showing EMT within the micropores, and a new stratified epithelium under the membrane. The membrane with larger micropores failed to maintain this triphasic epithelium. Live imaging revealed that KCs moved in a reciprocating manner, with actin-rich filopodia-like KC structures extending into and out of the 3.0-um micropores, while the cells migrated unidirectionally into larger micropores. KO of Piezo1 and keratin 6 increased KC entry to and exit from the 3.0-um micropores. Their results demonstrate that benign keratinocytes migrate through confined spaces in a reciprocating manner, which might help form triphasic epithelia, recapitulating wound healing processes.

      Strengths:

      Careful observation of the behaviour of keratinocytes on the different-sized pores. CrispR-Cas9 gene editing to KO Piezo 1 and keratin 6 isoforms in HaCaT keratinocytes.

      Weaknesses:

      There is no analysis of the matrix produced by the keratinocytes on the different pore sizes as this may influence migration.

      According to the reviewer’s suggestion, we have included images of laminin β3 labeling in 3D epidermis formed on 0.4-µm- or 3.0-µm-pored membranes in the revised manuscript (Figure 1—figure supplement 1e). Laminin β3, a subunit of laminin 332, was detected in the epithelium formed on the 0.4-µm-pored membrane, as well as in all three compartments of the tissue formed on the 3.0-µm-pored membrane. We did not observe an apparent difference in laminin β3 deposition between the two pore sizes, although we note that this assessment is qualitative and that a quantitative comparison of matrix production would require a separate study.

      HaCaT cells are quite different from normal keratinocytes in terms of migration. Pilcher et al. PMID: 9182674

      We have included this limitation in the Discussion section of the revised manuscript and cited the suggested publication (Pilcher et al. 1997).

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      (1) Some of the terminology needs better definition or refinement. Triphasic suggests different physical behaviours (e.g. liquid-liquid phase separation) rather than cellular properties. Perhaps it would be better to refer to these as cell states or to describe the model more specifically as an invasion or EMT model. Likewise, the term 'reciprocating' implies two-way communication, but it is used to describe two-way migration or oscillating migration. Here, perhaps oscillatory would be clearer.

      According to the reviewer’s suggestion, we have revised the title, abstract, and main text to avoid the terms “reciprocating” and “triphasic” and have instead adopted “oscillatory” and “three-compartment,” respectively.

      (2) The qualitative images in Figure 1 need better quantitative support through image analysis of the immunostaining to confirm changes in marker expression within the different regions of the epidermis. As this is a core finding of the study, it requires additional quantification beyond the qPCR results, which also do not provide spatial information.

      In accordance with the reviewer's suggestion, we have added quantitative image analysis of E-cad, N-cad, Vim, and Slug in the epithelium on the 0.4-µm-pored membrane and in the compartments above and below the 3.0-µm-pored membrane (Figure 1—figure supplement 1a–d). Vim was significantly more abundant in both compartments of the 3.0-µm-pored condition than in the 0.4-µm-pored condition. N-cad showed the same trend, reaching statistical significance for the comparison between the 0.4-µm-pored membrane and the compartment below the 3.0-µm-pored membrane, and was also significantly more abundant below than above the 3.0-µm-pored membrane. Slug showed a similar trend that did not reach statistical significance, and E-cad did not differ significantly among the three regions. Unlike the qPCR results, these data provide spatial information on marker expression.

      (3) More detail is needed regarding the number of independent experiments and cells analysed. This appears to be missing from both the methods and figure captions.

      We apologize for the lack of detail. In the Materials and Methods, we have added a full description of the experimental design (measurement points per biological replicate, composition of each experimental batch) and of the statistical analysis, including the gamma generalized linear model with experimental batch as a categorical fixed effect, and the software used. In the figure legends, we have added the number of biological replicates, the statistical test, and the meaning of each graph element for every quantitative panel, as well as the number of replicates underlying each representative image. For Figure 2g and 2h, we have stated the number of independent experiments. We note that our quantification is based on the fraction of the imaging field occupied by GFP fluorescence rather than on individual cell counts; we therefore report the number of biological replicates and measurement points rather than the number of cells analyzed.

      (4) Figure 2i,j needs quantification to support the conclusions. Were the studies in 2g,h replicated in independent experiments? Likewise, could KCs in the micropores simply appear more positive for Vimentin because they are smaller? It would help to show quantification of a marker that does not change or goes down in the channel.

      In response to the reviewer's suggestion, we quantified the Vim/E-cad fluorescence intensity ratio, using E-cad as the internal reference marker (Figure 2—figure supplement 1d). The ratio was significantly lower within the micropores than above the membrane, indicating that Vim signals were not enriched within the micropores relative to E-cad. We therefore agree with the reviewer that the apparent increase in Vim positivity within the micropores in the original images was, at least in part, attributable to the smaller apparent size of the cells in this region. The quantification instead indicates that the partial EMT phenotype was already present in the cells above the membrane rather than being acquired upon entry into the micropores, which is consistent with the elevated Vim intensity both above and below the 3.0-µm-pored membrane in primary KCs (Figure 1—figure supplement 1c). We have revised the description of Figures 2i and 2j accordingly.

      The experiments shown in Figures 2g and 2h were performed three times independently, and both panels summarize the pooled data from all three experiments. This is now stated in the Materials and Methods and in the figure legends.

      (5) How does the oscillatory migration response depend on the length of the channel? If the channels were longer, would they not be able to exit and reform the epithelium? This would require a different experimental system but could be important for understanding the fundamental principles of the observed migratory responses.

      We agree with the reviewer that the length of the channel may influence cellular behavior. In our study, we used 3.0-µm-pored membranes from Millicell (Merck) and Transwell (Corning), both of which have a membrane thickness of approximately 10 µm. Greiner also offers 3.0-µm-pored membranes with longer channels; however, the pore orientation in these products is not uniform, making them unsuitable for our experimental setup. As these are the only commercially available options accessible to us, we are currently unable to perform experiments addressing the effect of channel length. We agree that this is an important question and warrants investigation in future studies using appropriately engineered systems.

      (6) The underlying mechanisms are not described in much detail and there is no linkage between the pathways and molecules investigated. How exactly do actin, keratins, and piezo1 communicate to regulate cell migration? Are they acting directly on EMT genes such as SNAI1 or through changes in cell mechanics and cell-cell adhesions? Likewise, is TGF-beta signalling active in the system (e.g. nuclear pSMAD during cell migration)?

      Our data support a model in which mechanosensing and cytoskeletal remodeling, rather than transcriptional EMT programs alone, primarily regulate keratinocyte migration through confined micropores. Notably, inhibition of TGF-β signaling, a major driver of canonical EMT programs, did not impair keratinocyte entry into or exit from the micropores (Figure 3). These findings suggest that while EMT-associated pathways can modulate the process, as evidenced by the enhanced migration observed upon addition of TGF-β ligand, keratinocyte migration through micropores does not depend on classical TGF-β–driven EMT signaling. We could not directly assess nuclear pSMAD localization within the micropores because autofluorescence of micropore walls hindered the detection of nuclear signals in whole-mount imaging. Moreover, sagittal sectioning of frozen or FFPE-reconstructed 3D epidermis did not yield a sufficient number of nuclei in the micropores for assessing pSMAD positivity. Therefore, we cannot exclude context-dependent activation of TGF-β signaling. However, the lack of functional inhibition upon TGF-β receptor blockade indicates that canonical TGF-β signaling is not essential for this process. Our experiments further indicate that actin polymerization is essential for both entry into and exit from 3.0-µm micropores, suggesting that dynamic protrusive activity is a prerequisite for confined migration. Piezo1 and keratin 6 appear to function as negative modulators of this process. Piezo1, a mechanosensitive ion channel, likely influences migration by regulating cytoskeletal tension and cell shape, consistent with previous reports (Holt et al., 2021). Keratin 6, a stress-induced intermediate filament, may modulate actin organization and the mechanical properties of keratinocytes, as suggested by increased stress fiber formation in Krt6a/Krt6b-null cells (Wong & Coulombe, 2003).

      We have incorporated these points into the revised Discussion accordingly.

      (7) While the culture model is interesting and a simple yet useful tool to study EMT/MET, the new insight into these processes is somewhat limited and confirms much of what we already know about Piezo1, TGF-beta, and the cytoskeleton in KC migration. A clearer demonstration of new insight would help to strengthen the utility of the model.

      We agree that Piezo1, TGF-β signaling, and cytoskeletal dynamics have previously been implicated in keratinocyte migration. Our intention was not to claim the identification of entirely new molecular regulators of migration. Rather, the conceptual advance of our study lies in demonstrating how confined spatial architecture alone can generate a spatially organized epithelium comprising spatially graded EMT and MET states within a single continuous tissue.

      Specifically, our model reveals that keratinocytes undergoing confined migration exhibit oscillatory protrusive behavior that preserves the integrity of the overlying epithelium while enabling the formation of a new stratified epithelium beneath the membrane. To our knowledge, this dynamic integration of confined migration, partial EMT, and subsequent MET within a stratified epithelial context has not been previously demonstrated. The oscillatory behavior itself represents a distinct migratory mode compared to the predominantly unidirectional migration described in two-dimensional or Transwell assays.

      In summary, the novelty of this study lies in revealing how physical confinement can organize epithelial states and migratory dynamics in a self-organizing manner. We have included these conceptual advances in the revised manuscript.

      Reviewer #3 (Recommendations for the authors):

      In the introduction the authors state that 3D epidermis is not useful for wound healing. There are lots of papers using 3D epidermis for wound healing/re-epithelialization experiments.

      We agree with the reviewer’s point. Our original intention was to emphasize the utility of our new 3D model; however, we have moderated the tone in the Introduction to avoid underestimating the applicability of existing 3D epidermis models for wound healing and re-epithelialization studies and cited the relevant papers in the revised manuscript.

      As the cultures on the different membrane pore sizes are in culture for 14 days, a substantial matrix is produced. I think it would be useful to show staining for laminin 332 at the minimum as this may regulate migration.

      Production may also be influenced by the pore size/substrate.

      According to the reviewer’s suggestion, we have included images of laminin β3 labeling in 3D epidermis formed on 0.4-µm- or 3.0-µm-pored membranes in the revised manuscript (Figure 1—figure supplement 1e). Laminin β3, a subunit of laminin 332, was detected in the epithelium formed on the 0.4-µm-pored membrane, as well as in all three compartments of the tissue formed on the 3.0-µm-pored membrane. We did not observe an apparent difference in laminin β3 deposition between the two pore sizes, although we note that this assessment is qualitative and that a quantitative comparison of matrix production would require a separate study.

      HaCat cells are a slightly flawed keratinocyte model but I can see why you used them for gene manipulation, actin expression. Their flaws should be acknowledged in the Discussion.

      We have included this limitation in the Discussion section of the revised manuscript and cited the suggested publication (Pilcher et al. 1997).

      The RNA-seq dataset should be publicly available.

      We have made this RNA-seq dataset available publicly (https://www.ncbi.nlm.nih.gov/geo/query/acc.cgi?acc=GSE282553) and have presented this information in the Data availability section.

      In Figure 2, i and j in the legend the authors refer to 3 and 8-micron pores, but these are not labelled in the Figure.

      This was our error in mentioning 8.0-µm micropores in the Figure 2 legend. We intended to show only the 3D structure formed by the 3.0-µm-pored membrane. We have removed the reference to “8.0-µm micropores” in the revised manuscript.

    1. Author response:

      The following is the authors’ response to the original reviews.

      eLife Assessment:

      This important study presents convincing findings on creating an exhaustive library of new enhancer-AAVs targeting astrocytes and oligodendrocytes with high potential for both basic and translational work, which will be of value to a large and growing community. However, the outdated description of glial biology in the Introduction, the overstated claims of utility in the Conclusion, and the loose stringency in the criteria used to assemble the library diminish the strengths of the claims. The work will be of interest to neuroscientists working on glial cell biology.

      We thank eLife for the positive comments. We also are happy to provide a revised manuscript in response to the critical feedback. Revisions focus on improving the language and the descriptions of the vectors. We believe these improvements will help clarify the study and showcase the importance of astrocyte- and oligodendrocyte-specific enhancer AAVs for genetic access to these important cell types.

      Public Reviews:

      Reviewer #1 (Public review):

      The goal of this study was to generate a library of new enhancer-driven AAVs in order to selectively and efficiently target astrocytes and oligodendrocytes in rodents. The implied criteria are that such viral vectors should have high specificity for the intended cell type and effectively express in all astrocytes/oligos in the brain or, alternatively, be specific for defined brain regions, layers, or subtypes of astrocytes/oligos. In addition, they should be compatible with intravenous retro-orbital delivery to facilitate experimentation and brainwide targeting (i.e., show organ specificity and high efficiency in the brain). Ideally, these new AAVs would also maintain their characteristics across disease contexts and show applicability in non-human primates. Tools with such characteristics are generally lacking in studying glial cells and would be extremely useful to scale up and accelerate glial research, allowing targeting of astrocytes/oligos with distinct molecular identity and intersectional strategies.

      At present, however, none of the enhancer-AAVs presented in the study seems to meet this combination of criteria, at least not with the level of stringency typically expected in the field. The main reason is that, in its current form, the study does not present one candidate AAV iteratively improved to meet all these criteria; instead, it presents a catalogue of new AAVs with various degrees of specificity, completeness, and mixed characteristics. Therefore, their utility should be interpreted cautiously. Moreover, the way specificity and completeness are intermixed in the analysis makes it difficult to evaluate the actual utility of any given AAV. The study might have been strengthened by focusing on a small set of the most promising candidates (i.e., AiE0890m_3x2C) and validating them thoroughly for expression specificity, completeness, effective cargo expression, ability to allow specific pan-astrocyte or astrocyte-subtype targeting in vivo, and preserved properties in NHPs and in disease, as this would encourage their adoption by the community. Currently, too many AAVs are assessed inconsistently against the desired criteria, with none being evaluated through and through.

      The impact of the catalogue is also greatly diminished by the fact that a suite of AAVs with outstanding specificity and efficiency is already available for the study of astrocytes (e.g., 4x6T AAVs) and was not utilized as a standard to benchmark the new library, making it difficult to appreciate the relative benefits of the new AAVs. The inclusion of expression data in NHPs is very significant, but benchmarking against established AAVs would also be needed to fully appreciate their value.

      Importantly, readers should also be aware that the study seems noticeably limited in its literacy with glial biology. The introduction and discussion frame the field in a way that seems outdated, creating the impression that the diverse roles of glia in health and disease have not yet been studied, which may inadvertently be perceived as dismissive and stigmatizing.

      In summary, the paper introduces potentially useful viral tools and lays the foundations for future multiplexed targeting of distinct glial cell subpopulations in rodents and in nonhuman primates, which are extremely important directions. Some of the regionally restricted or even sparsely expressed AAVs may prove valuable in enabling subpopulation specific targeting or molecular profiling strategies, but currently lack full benchmarking. At present, the promises over the utility of the new tools seem overstated, and the library may not yet represent an actionable resource for targeting astrocytes and oligodendrocytes.

      We thank Reviewer 1 for the constructive commentary. We would like to point out that these enhancer-AAV sequences are all publicly available for research use through Addgene and have already been in use in multiple other publications. As one example, our enhancer AiE0380h was used as a recent positive control astrocyte-specific agent to help guide the discovery of enhancers that were activated in gliosis conditions (Zamboni et al., 2026 Nat Neurosci; PMID: 41331142). As another example, several of the vectors have been highly requested at Addgene including AiE0390m_3xC2 and AiE0410m to target astrocytes and oligodendrocytes.

      The reviewer pointed out that we did not compare the effectiveness of our enhancer-AAV vectors to the GfaABC1D-4x6T elements described by Gleichman et al. Although it is true we did not perform head-to-head comparisons, we have characterized our vectors by the same metrics as Gleichman et al. which is summarized in Author response image 1. The results shown here indicate that our enhancer-AAV vectors are comparable to the GfaABC1D-4x6T vector characterized by Gleichman.

      Author response image 1.

      AiE0390m-based enhancer-AAV vectors show comparable levels of specificity and completeness to that observed with GfaABC1D as observed by Gleichmann et al.

      It was not the intent of our study to quantitatively compare our vectors or studies, rather to provide independent sets of reagents to allow astrocyte and oligodendrocyte marking that will provide utility to the neuroscience community. However we have provided additional characterization that adds value to the enhancer elements we studied. We characterized our best-performing vectors by scRNA-seq, in peripheral tissue (liver), across species (mouse, rat, NHP), with a known difficult transgene (NeuroD1-mCherry), with a physiologic reporter (iACH-SnFR), and in disease context (Dravet syndrome). We also found new agents that provide astrocyte regional specificity and also those that mark oligodendrocytes. We feel that having sets of tools with differing properties will provide greater flexibility in choosing one that works for many applications. As examples, it could be desired to have higher or lower expression levels for any certain applications, or possibly different levels of completeness or sparsity. Sparse labeling is particularly valuable for evaluating morphology, while dense labeling could be advantageous to deliver a ubiquitous therapeutic. Having multiple validated tools enables this flexibility and support the whole field.

      Finally we would like to highlight that the enhancer elements we describe here are fully complementary to the existing sets of glial tools, including GfaABC1D and the 4x6T elements described by Gleichman et al. Importantly, enhancer elements are fully compatible with microRNA-binding sites like 4x6T, so combinations of these elements can provide fine control over targeted cell types. Furthermore, some enhancers provide different types of responses to cell states. AiE0390m has activity that is unperturbed by Dravet syndrome epilepsy, unlike GfaABC1D which expresses more strongly and in some neurons in this disease (Figure 8). This is similar to the IREN5 element described recently which activates in gliotic astrocytes near sites of damage (Zamboni et al.). Therefore, enhancer activities will help the field target and manipulate astrocytes and other glial cells in differential pathological disease states. As a result of these extra layers of flexibility, we anticipate that these enhancers will become tools for marking and manipulating astrocytes and enhancers in unforeseen ways. To help adoption in the community, detailed characterization of these and all related Allen Institute enhancer-AAV vectors are now available online in an easy-to-use resource (Allen Institute Genetic Tools Atlas at https://brain-map.org/bkp/experiment/genetic-tools/genetic-tools-atlas).

      We have also added new references and reframed the introduction and discussion of this work to provide a more current survey of the glial field.

      Reviewer #2 (Public review):

      Enhancer elements are regulatory DNA sequences that are capable of driving specific expression patterns. As these elements are generally short and context-independent, enhancers can be used in expression vectors (e.g., packaged in an adeno-associated virus, AAV) to limit expression to target cell populations. This approach was identified as a major strategy for cell-type-specific manipulation in the brain and has been pursued by both standard research studies as well as large-scale efforts led by the BRAIN Initiative. This manuscript describes a major effort to generate enhancer-AAVs targeting astrocytes and oligodendrocytes orchestrated by a large research team led by the Allen Institute for Brain Science. This manuscript parallels other recent publications describing sets of enhancerAAVs, following rigorous, similar methods with relatively broad testing and application.

      To identify and screen candidate enhancers, the scientists prioritized candidates via analysis of single-nucleus accessibility and methylation datasets (i.e., snATAC-seq) and tested them in mice. The scientists prioritized candidate enhancers that exhibited specificity of accessibility in the target cell type. Following selection, the scientists cloned the candidate sequences into AAV vectors with a minimal promoter and reporter gene, packaged the virus, delivered it to the mouse brain, and screened for activity based on reporter expression. Candidates that passed initial screening were further characterized via imaging and sorting, followed by single-cell RNA-seq. This process had around a 50% success rate and yielded 25 astrocyte and 21 oligodendrocyte enhancer-AAVs with the targeted cell-type-specific expression patterns.

      The scientists went on to test for subtype-specific activity patterns, finding wide diversity in astrocyte activities across sub-populations and conversely, homogenous oligodendrocyte activation. They optimized a few of these via concatenating the enhancer core sequence to increase expression levels of the reporter gene and showed strong specificity and completeness of cell targeting for a set of these enhancer-AAVs. Following characterization and validation, they then deployed these enhancer-AAVs in a number of demonstration applications to show the utility for basic and translational science. All the constructs developed here are available for public use via Addgene, ensuring that these new tools can be used by other researchers.

      There really are no obvious weaknesses in the work presented here, from the generation of the enhancer-AAVs to use in sophisticated validation studies. The enhancer-AAV testing is rigorous and provides critical information necessary for other scientists to select and use these constructs. The applications demonstrate the power of enhancer-AAV approaches. The toolbox presented here may not enable specific targeting of all relevant cellular subtypes or activity states for astrocytes and oligodendrocytes, and future work will be needed to fully understand the activity of the enhancers, identity of the target cell types, and context-dependent utility of these constructs. However, the set of enhancer-AAVs developed here should be transformative for researchers working on accessing and manipulating these cell types and have a major impact on the field.

      We thank Reviewer 2 for their positive feedback. We would like to re-emphasize that these enhancer-AAV sequences are all publicly available for research use through Addgene, with characterization data beyond what we have presented here is available publicly on Allen Institute Genetic Tools Atlas. Further these tools have already been in use in multiple other publications. We are eager to see how the research community makes use of these tools.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      My main suggestion is that the authors should try to make their library less of a catalogue and more focused on delivering one or two enhancer-AAVs that surpass existing ones, thus effectively delivering a new tool with great utility to the field. To achieve this, authors should pick their best candidate AAVs and evaluate them systemically across all the criteria, with side-by-side comparison to two benchmarks: the classic GFAP promoter AAV, and the 4x6T AAVs developed by Gleichman et al (PMID: 37973910).

      Thanks for the recommendation. Figures 2P, 5K, 6, 7, and 8 show comparison of our best astrocyte enhancer elements (AiE0390m and AiE0390m_3xC2) to GFAP promoter GfaABC1D. This work was done prior to the Gleichman et al. study so GfaABC1D-4x6T was not available at the time for direct comparison. However, as shown in Author response image 1, our data with AiE0390m and AiE0390m_3xC2 are comparable to that shown for GfaABC1D4x6T. Additionally we compared our enhancer-AAV vectors to the proB12 enhancer element described by Juttner et al. (Figures 2P and 5L), and again our enhancer-AAV vectors compare similarly. Finally, we also compared our oligodendrocyte-specific enhancers to the MBP promoter and we find our enhancers strongly outperform that promoter element in terms of specificity and completeness (Figure 3P and 5M). Overall, we have compared our new enhancer elements against reagents commonly used in the field, using established criteria for benchmarking effectiveness.

      Despite the effort put towards quantification and benchmarking, we believe there is significant value to having a variety of diverse and orthogonal tools in the field. Although GfaABC1D is an excellent promoter tool and maintains strong specificity under homeostatic conditions, it changes its character in different contexts. It took years and difficult experiments to realize this and caused investigators to believe astrocytes can differentiate into neurons with the right transgene. We confirm that the reality is this promoter changes activity when it expresses the NeuroD1 transgene (Fig. 6). Also, we demonstrate AiE0390m3xC2 maintains faithful astrocyte expression (Fig. 6). In a more recent example, Zamboni et al. showed that AiE0380h is downregulated in activated astrocytes. This isn’t an experiment we conducted and were not aware of that property. However, having multiple strong tools is a huge advantage when evaluating astrocytes and oligodendrocytes in different disease states and different experimental contexts. Investigators with only one or two tools available are at the mercy of the quirks of the tool. In this way, having a large collection of astrocyte and oligodendrocyte tools available is a major advantage to researchers that need a viral tool for glial expression in a new context. And importantly, as we show for hepatocytes (Fig. 7), investigators can predictions if any of our tools will change activity in different experimental contexts if epigenetic data is available. This prediction is not possible with promoters.

      For instance, 0390m is described as their best candidate but its efficiency is very low (~60%, Fig.10I). The concatenated version (AiE0390m_3x2C) is greatly improved, but it was not thoroughly evaluated: no data are provided regarding how its characteristics are maintained in disease context, its expression in other organs when delivered intravenously, or how it would be classified in Fig.2. Most notably, despite being engineered for RO injection, it was tested ICV in Fig. 9, missing an opportunity to demonstrate ease of use.

      As shown in Author response image 1, the efficiency (we prefer the term “completeness” since “efficiency” conflates labeling extent with expression level) we observed for AiE0390m is actually similar to or better than that observed for GfaABC1D-4x6T. AiE0390m_3x2C shows a still greater completeness of labeling, at the expense of a slightly diminished specificity with indirect reporter (Cre; Ai14). We have amended the colored bar graphs to write the observed completeness values directly in the figure for clarity.

      We have not tested this tool in the context of disease or the background expression in liver since the point of the manuscript was to present a library, not one specific tool. These are important experiments for a user focused on epilepsy or gene therapy to independently evaluate.

      Several sections of the text include claims or descriptions that are misleading and should be revised. This applies both to conclusions drawn from the presented data and to the framing of the field of glial biology.

      (1) Overstated/misleading conclusions: Segments such as "this collection of glial enhancer-AAVs will enable characterization of astrocyte and oligodendrocyte populations and their roles across species, disease states, and behavioral epochs" are unfounded based on the current library authors present and need to be revised. The conclusion that 2120m and 2160m are labeled "mutually exclusive regions" is misleading too, and no information is available on the specificity of 2160m. Similarly, the claim that the new AAVs are more predictable "across disease states" is a stretch, considering that a single disease model was employed. These are only examples.

      Thank you for the suggestions. We have amended the language in our manuscript as suggested to improve the accuracy and clarity of our claims, and limited our interpretation to one mouse model of epilepsy. AiE2160m predominantly labels subtelencephalic astrocytes (Figure 2—Figure Supplement 3) of the molecular taxonomy label “5109-AstroNT NN_3” (Figure 4D; taxonomic labels from Yao et al., 2023 PMID 38092916). However, we do strongly believe that this collection of tools, admittedly incompletely validated, will serve as an excellent starting point for investigator who need tools tailored to their biological need.

      (2) Outdated description of the field of glial biology: The text contains multiple segments that are incredibly dismissive of the current state of glial research. Sentences such as "Astrocytes provide trophic support for neurons, coordinate regional wiring patterns, respond to and regulate neurotransmission", or "this suggests that the astrocytes help selectively maintain glutamate or GABA tone depending on the local neurotransmitter balance" are incredibly reductive and dissonant with the reality of what the field has achieved, both conceptually and technically, and seem shockingly siloed from the past1520 years of research. This dramatically taints the credibility of what the authors have achieved and needs to be revised.

      Thank you for the constructive criticisms. Our language was intended to highlight the importance of glial cells without providing a comprehensive review. However the examples and wording did tilt toward passive roles and outdated references, whereas much recent work shows active instructive glial roles in regulating neural circuits. We have revised the language and added more recent examples/citations to reflect the chief roles that astrocytes play in the healthy brain.

      (3) The framework used to assess specificity and completeness would benefit from being more systematic, clear, and aligned with standards in the field.

      Thank you for the criticism. We have made our definitions of “Specificity” and “Completeness” more clear in the text. We have also added numerical text to our bar graph color presentation of completeness levels in Figures 2, 3, and 5 for easier interpretation. As shown in Author response image 1, our metrics are equivalent and comparable to those presented previously by Gleichman et al.

      (4) The apparent lack of core expertise in biology is detrimental to methodology. The authors seem unaware of the extreme stringency in the field: a 'specificity' of 80% would be considered extremely poor, and 90% would be merely acceptable. The bar for what the field typically expects for astrocyte-targeting is upward of 95%, usually close to 98-99%. See PMID: 37973910 as an example.

      We are happy that all of our best astrocyte-specific enhancer-AAV vectors (AiE0380h, AiE0390m, AiE0390h, AiE0387m, AiE0390m_3xC2, AiE0390h_3xC2, AiE0387m_3xC1) showed typical specificities of 98-99% or more. This was assessed by both IHC and scRNAseq. As one example, AiE0390h showed 452/454 cells positive by IHC (99.6% specific), and 86/86 sorted cells by RNA-seq (100% specific). This was data from two different animals in each assay (four total). In some assays we observed literally 100% specificity (807/807 labeled cells were astrocytes by IHC for AiE0390m). We made similar observations with the best oligodendrocyte-specific vectors (AiE0410m, AiE0641m, AiE0395h, AiE0397m, AiE0410m_3xC2). Moreover, it is not common for investigators to use transcriptomics to assess specificity in addition to histology.

      (5) AAVs with specificity above 95% could thus be labeled "specific," but all others should be considered "not specific" (perhaps with a gradation "poorly specific" for 95-90% and "not specific" below 90%). Either way, the category "mixed specificity" makes little sense.

      We are happy that all of our best astrocyte-specific enhancer-AAV vectors (AiE0380h, AiE0390m, AiE0387m, AiE0390m_3xC2, AiE0390h_3xC2, AiE0387m_3xC1) showed specificities of 98-99% or more, and only cells with astrocyte morphology observable throughout the brain. Other vectors were highly specific in cortex but also strongly labeled neurons in other regions; for example, AiE2118m shows strong and specific (>99%) astrocyte labeling in VISp, but changes specificity to isolated neuron populations in other regions like midbrain and medulla. Hence it has a “mixed” specificity profile. We have edited the text to clarify this grouping. Additionally, we hope that the matrix we provide in the new Figure 2—Figure Supplement 2 will aid in interpretation of regions where specificity is high and where specificity is low.

      (6) The tables that the authors provide (Figure 2 and Figure 2 Supplement 1) currently mix notions of specificity with notions of completeness, making it extremely difficult to assess the utility and quality of any of the AAVs. Instead, they should be separated, with first an assessment of specific and then an assessment of completeness/regionality only for those AAVs that are fully specific. Alternatively, authors could present their results as a matrix.

      We have amended the colored bar graphs to state the observed completeness levels directly in Figures 2, 3, and 5, rather than only as color scales as previously shown. We believe this improves the interpretability of the figure.

      (7) A more rigorous and useful way to assess CNS-wide or regional expression would be to provide quantitative region-by-region data with color-coded z-scoring per region, combined with meaningful descriptors (e.g., "Forebrain + cortex" instead of "most brain"). This could be a matrix with regions listed at the top and AAVs vertically.

      We thank the reviewer for the suggestion. We have added this suggested matrix as Figure 2—Figure Supplement 2. We hope it aids in interpretation of the data.

      (8) The criteria used for the classification of AAVs seem confusing or misleading. For example, AiE0390h is described as "CNS-wide" but then highlighted for its lack of expression in the basal ganglia, making it unsuitable as a true pan-astrocyte AAV. Conversely, Ai0386m and AiE0386h, classified as "weak", show stronger expression than several of the AAVs classified under the "most CNS" category.

      We thank the reviewer for the observations. Delivering AAVs IV via PHP.eB routinely target basal ganglia structures including striatum less efficiently than other parts of brain including cortex. This was quantified in our recent publication using molecular barcodes, and is true regardless of targeting neurons or oligodendrocytes or astrocytes in this region (approximately ½ log lower transduction as shown in Supplementary Figure 7a, 7c; Hunker et al., 2026 Nat. Comm. PMID 42049725). This is reflected in the current dataset of weaker expression in striatum and other related structures with each of the astrocyte or oligodendrocyte-targeting AAVs including GFAP promoter. However, some signal is present in striatal astrocytes with AiE0390h. On data review the example full-stitch images given for AiE0386m/h were not representative of average signal intensity across replicates, whereas the inset images were representative. In this resubmission we have swapped images for 386h and 386m in Figure 2—Figure Supplement 1 with more representative full-size images. We hope this has increased the interpretability of the dataset. Importantly we assessed fluorescence levels from enhancer-AAV vectors by multiple techniques: microscopy, immunohistochemistry, flow cytometry, and scRNA-seq.

      (9) Additionally, a concern is that the regional specificity reported for some AAVs is extremely loose, which seems to be of limited practical use. It would be more impactful to focus on a couple of truly non-overlapping AAVs with genuine potential, and thoroughly assess whether, injected together, they could be used to express distinct cargos (effectors or reporters) into distinct populations, layers, or regions with no or minimal overlap. This could include 2120m and 2121m, which may hold promise for targeting subregions of the basal ganglia (though, because they also express outside of the BG, a follow-up experiment involving stereotaxic injection into these regions would be needed to test whether regional specificity is preserved with that route of delivery). Similarly, AiE0381h seems oddly specific to the CA2 of the hippocampus, and this could be very useful. These additional experiments could open the way to cell-type-specific combinatorial strategies, which would represent a monumental technical leap for the field.

      Thank you for the insightful comment. Although we agree that the suggestions of multiplexing two enhancer-AAV vectors with different specificities has high significance, we have done similar multiplexing work and unfortunately at present it is not yet predictable which combinations will work for multiplexing. Some combinations do work and others do not. For examples see Figures 7 and S9 of Hunker et al., 2025 Neuron PMID 40403704. Because of the complication of interpreting results, we have decided not to pursue these experiments in this manuscript. We have added text to the discussion to highlight the future unrealized possibility of multiplexing enhancer-AAVs.

      AiE0381h has background expression in CA2 projection neurons, which is a frequent site of off-target labeling for AAV9-derived vectors in enhancer and capsid screens. As one example Nonnenmacher et al. observed frequent CA2 neuron-enriched expression in a capsid screen (PMID: 33553485 Figure 5B). As another example we observe off-target labeling in CA2 with AiE2119m as well (Figure 2—Figure Supplement 1). It is unclear what makes CA2 neurons unique in this way, and it is unclear why it is the most prominent for AiE0381h in this set. Regardless, we have demarcated the off-target CA2 site of expression in Figure 2—Figure Supplement 1, along with other off-target sites of expression from other vectors, and noted it in the figure legend.

      (10) The "sparse" AAVs (which authors labeled "scattered") should not be dismissed. It would be worth assessing whether astrocytes expressing these AAVs map onto specific molecular signatures, i.e., these AAVs target a very specific population of sparse astrocytes in various regions. This would be of substantial benefit to the field, allowing subpopulation-specific molecular characterizations (e.g., TRAP) or functional manipulations via chemogenetic actuators (e.g., DREADDS).

      We thank the reviewer for this important highlight. We too are fascinated by the enhancerAAVs that show sparse/scattered labeling patterns. We have confirmed that the sparse labeling pattern is reproducible with multiple replicate animals tested per vector, and reproducible across orthologous pairs, with the best example being AiE0374m (mouse ortholog) and AiE0374h (human ortholog) both showing this sparse expression pattern. Our interest led us to conducting single cell RNA-seq profiling studies to see if we could see any clear molecular distinctions of the labeled cells (compared to other labeled astrocytes. However, we did not observe any gene expression differences using scRNA-seq when comparing the sparse AiE0374m-labeled cortical astrocytes to cortical astrocytes labeled by enhancer-AAV vectors that broadly labeled cortical astrocytes (Fig. 4A). Furthermore, tools for locating transcription factor binding motifs (MAST) did not elucidate any obvious unique transcription factor that defined this group of enhancer-AAVs (not shown). As a result the molecular interpretation of the sparse expression patterns is not yet known. We cannot say what distinguished these astrocytes from others, but the phenomenon inspires further experimentation that is beyond the scope of this study. We provide these data and vectors to the field in hopes of it enabling unique experiments to better understand this population, as well as conduct experiment where sparse astrocyte labeling is valuable. We have edited the text to call this set “Sparse” and highlight these possible use cases in the discussion.

      Other concerns:

      (1) Terms such as cell type vs. subtype or subpopulation are not used adequately.

      (Astrocytes are a cell type, and protoplasmic astrocytes are a subtype of astrocytes.)

      We are following the nomenclature of molecular taxonomies of brain cells (example references Yao et al., Nature 2023 PMID: 38092916; Siletti et al., Science PMID: 37824663; Zu et al., Nature 2023 PMID: 38092917). This nomenclature has the advantage of linking molecular information to enhancer discovery and the eventual targeting of every brain cell type with this technology.

      (2) Considerations about the effect of viral titers would be important.

      We deliver a constant dose of 5e11 vg per animal, irrespective of production titer.

      Production titers ranged from 4.47e12 to 1.47e14 gc/mL, interquartile range 3.13e13-6.55e13 gc/mL, mean 5.10e13 gc/mL, n = 215 total viral preps. This detail has been added to the

      methods.

      (3) A stronger articulation to distinguish this paper from the prior publication in Cell [PMID: 40403729] would be needed.

      We focus our characterization of the vectors across species, organs, disease states, and with difficult non-reporter vectors. The prior paper was focused on a larger breadth of testing with a publicly accessible database attached, whereas this paper constitutes a deeper dive into the properties glial cell targeting reagents. We have added additional text in discussion to highlight the differences between the manuscripts. Furthermore, Supplementary Table 2 shows the additional experiments added in the current study which allows deeper characterization of these glial cell-targeting collections. We strongly believe the community is best served by our deep dive into glial enhancer discovery and evaluation of these tools.

      (4) The NHP data is highly significant, but here again, it is missing benchmarking against established tools such as 4x6T.

      Since Gleichman did not test their element in NHP it is not validated in NHP. It may or may not work there. Our enhancer elements, by virtue of being selected for conservation of activity across mammalian species, are predicted to work across mammalian species, and many of them in fact do work across mammalian species. Besides GFAP promoter (references Heffernan et al., 2022 J. Neurosci. Meth. PMID: 35202614; Matsuzaki et al., 2024 MTMCD; PMID: 39391837) our enhancer elements are the only control elements validated for highly specific astrocyte expression in primate, and our oligodendrocytespecific element AiE0410m shows higher specificity than that observed for MBP promoter in primate previously (Matsuzaki et al., 2024 MTMCD; PMID: 39391837).

      (5) Figure 5 M is never cited.

      Thank you for the comment. We cite Figure 5M on line 233 of the revised manuscript.

      Reviewer #2 (Recommendations for the authors):

      I have no recommendations for the authors. This work is rigorous, broad in scope for testing, validation, and application, and overall an exceptional and significant piece of work.

      We thank Reviewer 2 for their positive comments.

    1. Author response:

      Thank you very much for your constructive assessment and the thoughtful comments provided by both reviewers. We greatly appreciate their valuable and insightful suggestions, which will help us strengthen the analyses and interpretation of our study. We are pleased to provide the following provisional responses outlining our planned revisions. A fully revised manuscript, together with detailed point-by-point responses to all reviewer comments, will be submitted in due course.

      Responses to Reviewer #1:

      Phylogenetically informed statistical analyses. We fully agree that phylogenetically informed analyses should take precedence when interpreting cross-species associations. In the revised manuscript, we will reorganize the Results to present PGLS and SEM findings as the primary evidence. We will also carefully revise the Abstract, Results, and Discussion to ensure that our conclusions are consistent with the phylogenetically corrected results, particularly regarding the relationship between generation time and TE content across all species and the strength of the association between dN/dS and TE content.

      Assembly quality as a potential confounding factor. We will examine whether BUSCO completeness scores and contig N50 are associated with genome size and TE content. Where appropriate, we will incorporate assembly quality metrics as covariates in the PGLS and SEM models or perform additional sensitivity analyses. We will also consider conducting separate analyses for avian and non-avian sauropsids to evaluate the robustness of our findings and further explore their phylogenetic scale dependence.

      SEM methodology. We will expand the Methods section to provide a clearer explanation of how the piecewise SEM was constructed, the biological rationale underlying the proposed pathways, and the criteria used for model evaluation and selection, including comparisons of alternative model configurations where appropriate. We will also explore the feasibility of conducting separate SEM analyses for avian and non-avian sauropsids.

      Residual support for the MHH and contrast dependence. We agree that the weak but persistent associations between TE content and proxies of effective population size (Ne) in the pooled dataset deserve greater emphasis. We will discuss these relationships more explicitly, including the association between dN/dS and genome size. We will also expand our discussion of contrast dependence, particularly the possibility that reduced variation in life-history traits and TE content, together with differences in sample size and lineage-specific evolutionary dynamics, may contribute to the weakening of associations at smaller phylogenetic scales.

      dN/dS estimation. We will clarify the procedures used for gene-level filtering and dN/dS estimation, particularly the treatment of genes with very low dS values, and evaluate the potential influence of alternative estimation approaches. We will also further examine the relationships among body mass, generation time, and dN/dS to assess the consistency of these variables as indirect proxies of Ne and selection efficacy. In addition, we will discuss the potential influence of GC-biased gene conversion (gBGC) on dN/dS estimates in birds, with reference to the relevant literature.

      Recent TE elements. We agree that examining recently accumulated TEs would provide a valuable additional perspective. We plan to investigate whether the abundance of recent TEs (Kimura divergence <5%) is associated with life-history traits or dN/dS and present the results in the supplementary materials.

      We will also address all minor comments, including moving interpretive statements from the Results to the Discussion, incorporating the suggested references (including doi:10.1111/mec.70265 and RepeatMasker), applying log transformations to genome size where appropriate, correcting the order of figure citations, defining the abbreviation "RE", clarifying or removing the unexplained close-up in Figure 1, and refining the relevant wording throughout the manuscript.

      Responses to Reviewer #2:

      Statistical assumptions (normality, linearity, and homoscedasticity). We will systematically evaluate the statistical assumptions underlying our analyses, including the distributional properties of the data and the residuals of the fitted models. Specifically, we will (i) complement Pearson correlations with non-parametric alternatives, such as Kendall's tau, to assess the robustness of the observed associations; (ii) examine PGLS residuals for normality, homoscedasticity, and remaining phylogenetic dependence, and consider non-parametric correlations based on phylogenetic independent contrasts (PIC) as an additional sensitivity analysis; and (iii) assess the assumptions and goodness of fit of the SEM component models and explore alternative modeling approaches where appropriate.

      Direction of the generation time correlation. We will clarify the definition and units of generation time used in the dataset (duration of a generation, in years) and discuss this counterintuitive positive association explicitly, relating it to the expectation under the MHH and to previous findings.

      Reproducibility. We will improve the reproducibility of our analyses by providing the input datasets alongside the corresponding R scripts, detailed README files, and relevant software and package information. We will also make the analysis code available under an appropriate open-source license to facilitate the reproduction of our statistical models and figures.

      Minor comments. We will provide additional justification for selecting Sauropsida as the phylogenetic scope of our study, clarify the definition of the "matched" dataset, revise the use of "superficially", and further explain the interpretation of body mass as a potential physiological factor or an indirect proxy for population density across different taxonomic groups.

      We have no factual concerns regarding the eLife Assessment or the public reviews.

      Thank you again for the opportunity to strengthen our work. We believe that these revisions will improve the statistical robustness of our analyses and provide a more nuanced interpretation of the associations between TE accumulation, life-history traits, and molecular evolutionary indicators across phylogenetic scales.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Reviewer #1 (Public review):

      Summary:

      Negreira, G. et al clearly presented the challenges of conducting genomic studies in unicellular pathogens and of addressing questions related to the balance between genome integrity and instability, pivotal for survival under the stressful conditions these organisms face and for their evolutionary success. This underlies the need for powerful approaches to perform single-cell DNA analyses suited to the small and plastic Leishmania genome. Accordingly, their goal was to develop such a novel method and demonstrate its robustness.

      In this study, the authors combined semi-permeable capsules (SPCs) with primary template-directed amplification (PTA) and adapted the system to the Leishmania genome, which is about 100 times smaller than the human genome and exhibits remarkable plasticity and mosaic aneuploidy. Given the size and organization of the Leishmania genome, the challenges were substantial; nevertheless, the authors successfully demonstrated that PTA not only works for Leishmania but also represents a significantly improved whole-genome amplification (WGA) method compared with standard approaches. They showed that SPCs provide a superior alternative for cell encapsulation, increasing throughput. The methodology enabled high-resolution karyotyping and the detection of fine-scale copy number variations (CNVs) at the singlecell level. Furthermore, it allowed discrimination between genotypically distinct cells within mixed populations.

      Strengths:

      (1) This is a high-impact study that will likely contribute to our understanding of DNA replication and the genetic plasticity of Leishmania, including its welldocumented aneuploidy, somy variations, CNVs, and SNPs - all key elements for elucidating various aspects of the parasite's biology, such as genome evolution, genetic exchange, and mechanisms of drug resistance.

      Overall, the authors clearly achieved their objectives, providing a solid rationale for the study and demonstrating how this approach can advance the investigation of Leishmania's small, plastic genome and its frequent natural strain mixtures within hosts. This methodology may also prove valuable for genomic studies of other single-celled organisms.

      We thank the reviewer for the positive feedback and appreciation of the potential applications for the methodology we describe here.

      Weaknesses:

      (2) The discussion section could be enriched to help readers understand the significance of the work, for instance, by more clearly pointing out the obstacles to a better understanding of DNA replication in Leishmania. Or else, when they discuss the results obtained at the level of nucleotide information and the relevance of being able to compare, in their case, the two strains, they could refer to the implications of this level of precision to those studying clonal strains or field isolates, drug resistance or virulence in a more detailed way.

      We thank the reviewer for the suggestions. Indeed, single-cell DNA sequencing has successfully revealed cell-to-cell variability in replication timing and fork progression in mammalian cells [1,2] and we believe that the SPC-PTA workflow could be used in similar studies in Leishmania to complement bulk-based observations [3,4]. We have included a discussion about this in the revised version:

      “[…]scDNAseq has been used to study DNA replication programs, revealing fork progression speeds and replication timing along the cell cycle in mammalian cells [67,68]. Unlike most eukaryotes, Leishmania has a unique DNA replication program based on a single large replication origin per chromosome which is highly active during S-phase and which is complemented by thousands of minor low-efficiency origin sites that are active during G1 and G2/M phases [69,70]. However, it is still unclear if there is cell-to-cell variability in origin use and replication timing, and how this may link to genome instability, which could be addressed using the SPCPTA workflow in parasites at different stages of the cell cycle.”

      Regarding nucleotide information, it is indeed of high relevance to detect minor circulating variants with potential virulence impact and/or effect on drug resistance which could be missed by bulk sequencing. This includes the ability to detect co-occurring variants with potential epistatic effects. We have extensively expanded the discussion section in the “heterogeneity of nucleotide sequence” section to discuss these topics:

      “[…] Moreover, population-genomic studies of the L. donovani complex have identified isolates with allele-frequency patterns consistent with mixtures of genetically similar subclones, including mixtures within the same phylogenetic group [54]. Mixed-genotype infections are likely under-detected by routine diagnostics [55], and confounds bulk genomic analyses. This was evident when cultured parasites showed genomic signatures distinct from their clinical counterparts, likely due to the expansion of initially undetectable genotypes in culture [56]. Similar challenges have been described in other protozoan parasites such as Plasmodium falciparum, where polyclonal infections can contain mixed drug-sensitive and drug-resistant genotypes [57,58] and conventional bulk genotyping may reduce this complexity to binary calls [59], motivating the development of approaches that resolve subpopulation structure more explicitly. This complexity makes it challenging to link genotype to phenotype and to study evolutionary dynamics, especially for traits like drug resistance or virulence where minor variants can be clinically relevant […]”

      And:

      “In addition, another advantage of the single-cell approach is that it enables detecting co-existing mutations in the same cell, as illustrated in Figure 5D. This is particularly relevant in protozoan parasites, where resistance may depend on multi-locus haplotypes or combinations of mutations, as illustrated by resistance against sulfadoxine-pyrimethamine treatment in Plasmodium falciparum, which is characterized by mutations in dhfr and/or dhps genes, including triple and septuple mutant forms as well as mutations in both genes [62–64].”

      Reviewer #2 (Public review):

      Summary:

      Negreira et al. present an application of a novel single-cell genomics approach to investigate the genetic heterogeneity of Leishmania parasites. Leishmania, while also representing a major global disease with hundreds of thousands of cases annually, serves as a model to test the rigor of the sequencing strategy. Its complex karyotypic nature necessitates a method that is capable of resolving natural variation to better understand genome dynamics. Importantly, an earlier single-cell genomics platform (10x Chromium) is no longer available, and new methods need to be evaluated to fill in this gap.

      The study was designed to evaluate whether a capsule-based cell capture method combined with primary template-directed amplification (PTA) could maintain levels of genomic heterogeneity represented in an equal mixture of two Leishmania strains. This was a high bar, given the relatively small protozoan genome and prior studies that showed limitations of single-cell genomics, especially for gene-level copy number changes. Overall, the study found that semi-permeable capsules (SPC) are an effective way to isolate high-quality single cells. Additionally, short reads from amplified genomes effectively maintained the relative levels of variation in the two strains on the chromosome, gene copy, and individual base level. Thus, this method will be useful to evaluate adaptive strategies of Leishmania. Many researchers will also refer to these studies to set up SPC collection and PTA methods for their organism of choice.

      Strengths:

      (1) The use of SPC and PTA in a non-bacterial organism is novel. The study displays the utility of these methods to isolate and amplify single genomes to a level that can be sequenced, despite being a motile organism with a GC-rich genome.

      (2) The authors clearly outlined their optimization strategy and provided numerous quality-control metrics that inspire confidence in the success of achieving even chromosomal coverage relative to ploidy.

      (3) The use of two distinct Leishmania strains with known clonal status provided strong evidence that PTA-based amplification could reflect genome differences and displayed the utility of the method for studies of rare genotypes.

      (4) Evaluating the SPCs pre- and post-amplification with microscopy is a practical and robust way of determining the success of SPC formation and PTA.

      (5) The authors show that the PTA-based approach easily resolved major genotypic ploidy in agreement with a prior 10x Chromium-based study. The new method had improved resolution of drug resistance genotypes in the form of both copy-number variations and single-nucleotide polymorphisms.

      (6) In general, the authors are very thorough in describing the methods, including those used to optimize PTA lysis and amplification steps (fresh vs frozen cells, naked DNA vs sorted cells, etc). This demonstrates a depth of knowledge about the procedure and leaves few unanswered questions.

      (7) The custom, multifaceted, computational assessment of coverage evenness is a major strength of the study and demonstrates that the authors acknowledge potential computational factors that could impact the analysis.

      We deeply appreciate the positive and encouraging feedback on our manuscript.

      Weaknesses:

      (8) The rationale behind some experimental/analysis choices is not welldescribed. For example, the rationale behind methanol fixation and heat-lysis is unclear. Additionally, the choice of various methods to assess "evenness" is not justified (e.g. why are multiple methods needed? What is the strength of each method?). Also, there is no justification for using 100k reads for subsampling. Finally, what exactly constitutes a "confidently-called SNP"?

      The methanol fixation prior to lysis is part of the original protocol described in the Single-Microbe Genome Barcoding Kit manual and was meant to facilitate lysis and DNA denaturation in bacterial cells (for which the kit was originally developed). However, in our preliminary tests with bulk samples – described in the supplementary material – we noticed a strong negative effect on lysis efficiency/DNA recovery when parasites were fixed with methanol. Thus, we decided to test the effect of skipping this step in the single-cell DNA workflow. We kept the SPC_STD1 sample to have a safe control where the full workflow described in the kit manual was followed.

      As we were unsure if the standard lysis (25 ˚C for 15 minutes) would work efficiently for Leishmania, we included the heat-lysis (99˚C for 15 minutes) as well as the longer incubation lysis (25 ˚C for 1h). These modifications were listed as validated alternatives in the kit's manual. In the revised version, we have included a paragraph in the results section explaining the reason why we tested different lysis conditions:

      “We based our scDNAseq approach on the Single Microbe DNA Barcoding Kit from Atrandi BiosciencesTM, which uses semi-permeable capsules (SPCs) for high-throughput cell encapsulation30. The kit includes a pre-defined cell lysis protocol developed for bacteria, which starts with a methanol fixation step followed by incubation for 15 minutes at room temperature in the provided lysis buffer (0.8 M KOH, 20 mM EDTA, 200 mM DTT). Because it was unclear whether this protocol would be effective for Leishmania cells, we also tested modified lysis conditions by either extending the incubation time from 15 to 60 minutes or increasing the incubation temperature to 99 ˚C. In addition, we assessed if the protocol could be simplified by omitting the methanol fixation step. These modifications were first evaluated in pools of ~1,000,000 parasites per condition, by measuring with qPCR the quantity of free-floating DNA in the supernatant after parasite lysis and centrifugation. This analysis indicated that omitting methanol fixation in fact improved DNA release, whereas no clear differences were observed among the different lysis conditions (see Supplementary Text, Supplementary Figures 1 and 2, and Supplementary Tables 1 and 2).”

      Regarding read subsampling, in fact, we used two different thresholds, 20k reads for when 10X datasets were included in the comparisons, and 100k reads for when comparisons were done only among the SPC samples. These thresholds were always chosen to match the number of reads found in the true cell with the lowest read count across the datasets being compared: 20K reads in the 10X-scDNA data for BPK081 and 100K in the SPC-STD1 sample. This is now mentioned in the materials and methods:

      "Counts were then randomly subsampled to a total of 20,000 reads per cell – matching the number of reads found in the least covered true cell in the scDNA-10X datasets (see below) – to allow cross-sample comparisons. " and in the results section:

      "After equalizing each sample to 100,000 reads per cell (the number of reads observed in the least covered true cell in sample SPC-STD1), PTA still performed best"

      and:

      "Thus, we compared coverage uniformity in our dataset with that of two libraries generated using the Chromium Single-Cell CNV solution (10X-scDNA), considered the gold standard for this application. For this, we first subsampled each cell to 20,000 reads, matching the cell with the least read count in the 10X-scDNA dataset."

      Regarding variant calling, a variant was considered confidently called if it was covered, at single-cell level, by at least one deduplicated read with Phred quality above Q30 and mapping quality (MAPQ) also above 30. This is now mentioned in the materials and methods section:

      "A variant was considered confidently called when it was covered, at single-cell level, by at least one deduplicated read with Phred quality above Q30 and mapping quality (MAPQ) also above 30."

      (9) In the methods, the STD protocol lists a 15-minute amplification at 45C whereas the PTA protocol involves 10h at 37C. This is a dramatic difference in incubation time and should be addressed when comparing results from the two methods. It is not really a fair comparison when you look at coverage levels; of course, a 10-hour incubation is going to yield more reads than a 15-minute incubation.

      We agree with the reviewer that the longer incubation period of PTA might explain the higher read count seen in the PTA samples, although the differences in amplification kinetics (linear in PTA, exponential in STD) and potential differences in amplification saturation points make it difficult to compare them. For instance, an updated version of PTA (ResolveDNA V2) uses a lower amplification time (2.5 h) and achieves similar amplification levels compared to the 10h incubation time, suggesting PTA amplification saturates well before the 10h time. In any case, all quality check for coverage metrics were done with the cells subsampled to 20,000 reads to mitigate the effect of read count differences on the data quality.

      (10) There is a lack of quantitative evaluations of the SPCs. e.g. How many capsules were evaluated to assess doublets? How many capsules were detected as Syto5 positive in a successful vs an unsuccessful experiment?

      We agree with the reviewer but during experimental execution SPCs were only assessed qualitatively via microscopy following the Single-cell microbe DNA barcoding kit manual. No quantitative analysis was done and therefore we do not have this data. Regarding doublet, this was done in silico based on the detection of SPCs containing mixed genomes from the two strains used in the study as described in the Materials and Methods. As pointed by another reviewer, this only allow the detection of inter-strain doublets. We have now included in the revised version an estimate of total doublets in Table 1 and in the text:

      In the Materials and Methods:

      “Cells exhibiting a mixture of diagnostic SNPs from both strains above 5% were classified as inter-strain doublets. Total doublet frequency was estimated under the assumption of random cell pairing, by dividing the observed frequency of interstrain HU3/BPK081 doublets by the expected proportion of mixed doublets among all doublets, 2pq, where p and q are the relative frequencies of HU3 and BPK081 singlets respectively.”

      And in the results:

      “Successful WGA samples showed only 2–6 inter-strain doublets (4-12 estimated total doublets),

      (11) The authors do not address some of the amplification results obtained under various conditions. For example, why did temperature-based lysis of STD4 lead to amplification failure? Also, what is the reason for fewer "true" cells (higher background) in the PTA samples compared to the STD samples? Is this related to issues with barcoding or, alternatively, substandard amplification as indicated by lower read amounts in some capsules (knee plots in Figure 1C)?

      After exchange with the technical support team of the SPC generator kit, it was clarified that the heat lysis done in STD4 should have had a shorter incubation time (10 minutes instead of 15 minutes) and a lower KOH concentration (0.2 M instead of 0.8 M). We suspect that the longer incubation time, combined with the higher temperature and the harsh lysis condition with 0.8 M KOH might have damaged SPCs and therefore DNA might have leaked out of them before WGA. In the microscopy images, SPCs in STD4 show a swollen aspect not seen in the other samples. We added the following statement to the results section to explain this in the revised version:

      “SPC-STD4 also exhibited enlarged SPCs, which could indicate they were damaged during lysis.”

      and

      “According to follow-up guidance from the kit technical support team, it was suggested to use a shorter incubation time (10 min rather than 15 min) and a lower KOH concentration (0.2 M rather than 0.8 M) for heat-based lysis. We therefore infer that the combination of prolonged incubation, high temperature, and high KOH concentration in SPC-STD4 damaged the SPCs and promoted DNA leakage before WGA."

      (12) The paper presents limited biological relevance. Without this, the paper describes an improvement in genome amplification methods and some proof-ofconcept analyses. Using a 1:1 mixture of parasites with different genotypes, the authors display the utility of the method to resolve genetic diversity, but they don't seek to understand the limits of detecting this diversity. For some, the authors do not comment on the mixed karyotypes from the HU3 cells (Figure 3F) other than to state that this line was not clonal. For CNVs, the two loci evaluated were detected at relatively high copy number (according to Figure 4C, they are between 4 and 20 copies). Thus, the sensitivity of CNV detection from this data remains unclear; can this approach detect lower-level CNVs like duplications, or minor CNVs that do not show up in every cell?

      We have attempted an unbiased, genome-wide CNV calling approach across all samples to (i) confirm the two known loci and (ii) screen for novel short CNVs. CNV values were calculated as the ratio of median gene-level coverage to median chromosome-wide coverage. We have now added heatmaps summarizing this analysis for each sample in the supplementary material (Supplementary Figure 5). As expected, The SPC-STD1-3 samples sequencing depth was very sparse, with many genes showing low or even zero median coverage across the full chromosome. The SPC-PTA samples had substantially higher sequencing depth, making genome-wide CNV calculation feasible. However, the resulting heatmaps showed no clear, consistent signal across genes except for the two previously identified loci - the M-locus on chromosome 36 in BPK081 and the CNV on chromosome 29 in HU3. Thus, it is unclear if these are the only two differential CNVs present in these strains, or if our de novo detection method failed to retrieve other CNVs. We now describe this in the results section:

      “We also investigated if other CNVs could be present in our data using a gene-level unsupervised approach. For that, we divided the median read count of each annotated gene by the median count of the chromosome and looked for genes with median value 1.5 times higher than the chromosome median (supplementary figure 5). As expected, The SPC-PTA samples had substantially higher sequencing depth, making genome-wide CNV calculation feasible. Notably, the two previously identified loci - the M-locus on chromosome 36 in BPK081 and a known CNV on chromosome 29 in HU3 - stood out clearly against this background, consistent with the CNVs we had already characterized by bulk genome sequencing. However, this showed no clear, consistent signal across genes except for these two previously identified loci.”

      (13) The authors state that Leishmania can carry extrachromosomal copies of important genes. There is no discussion about how the presence of these molecules would affect the amplification steps and CNV detection. For example, the phi29 enzyme is very processive with circular molecules; does its presence lead to overamplification and overrepresentation in the data? Is this evident in the current study? This information would be useful for organisms that carry this type of genetic element.

      We believe our data, which uses short-read sequences, does not allow to differentiate between intra-chromosomal CNVs and linear or circular episomal CNVs derived from the nuclear genome. Of note, the Leishmania kinetoplast contains large circular DNA known as maxicircles (~10-40 kb), and we did not observe a clear dominance of maxicircle amplicons compared to nuclear genomic regions. The kinetoplast also contains thousands of minicircles (0.5- 2 kb) but those are not present in the reference genome and therefore it was not determined if they were detected and their prevalence in the data. As for the CNVs discussed in the paper, we have previously demonstrated that the M-locus CNV in chromosome 36 is intrachromosomal, not circular (episomal) [5].

      (14) The manuscript is missing a comparison with other similar studies in the field. For example, how does this coverage level compare to those achieved for other genomes? Can this method achieve amplification levels needed to assess larger genomes? Has there been any evaluation of base composition effects since Leishmania is a GC-rich genome?

      We believe the SPC-PTA workflow can be applied to organisms with larger genomes as PTA was developed specifically for mammalian cells [6], and also because, in our hands, it outperformed the 10X scDNA solution, which was developed for mammals.

      We believe direct comparison with other studies regarding coverage levels is elusive because other steps in the workflow apart from the WGA, such as the library preparation (PCR-based in our case), as well as genome features like GC content, size, and presence of repetitive regions, can also affect coverage levels and evenness. One strength of our approach was the use a single sample (the 50/50 mix between two L. donovani strain) for all conditions, thus removing potential parasite-specific biases. In addition, the application of a multiplexing system during barcoding allowed us to combine all samples prior to library preparation, thus removing potential differences introduced by this step.

      Regarding the effect of GC content, we did notice a negative bias in all samples in regions with higher GC content, which had to be corrected in silico. In the revised version, we have included a supplementary figure showing the GC bias and the correction result (supplementary figure 4).

      (15) Cost is mentioned as a benefit of the SPC platform, and savings are achieved when working in a plate format, but no details are included on how this was evaluated.

      We have improved the cost estimation in the discussion:

      “With SPCs we could apply PTA to a total of 399 cells (samples SPC-PTA1-2) while using the equivalent of 17 PTA reactions (17 cells if isolated in plates). Considering the costs of the PTA (~ €3100 for 96 WGA reactions) and library prep kits (~ €3100 for 96 libraries), a full plate-based system for 96 cells would have costed ~ €65 per cell excluding sequencing cost. In our hands, this cost was reduced to ~ €3,9 per cell including the required SPC generation kit (~ €230 for 1 encapsulation run) the PTA reactions (~ €550 eur for 17 reactions) the barcoding and library prep kits (~ €660 for 2 samples in the barcoding plate if using 6 sample multiplexing) and library prep (~ €130 for 4 final libraries). We also estimate that using the maximum capacity of 10.000 cells would further reduce price per cell to ~€0,39, although this comes with the caveats of a higher doublet rate and higher sequencing costs to achieve robust per-cell coverage. Overall, SPCs improves scalability and cost-efficiency, making high-throughput single-cell genome sequencing more accessible.”

      (16) The Zenodo link for custom scripts does not exist, and code cannot be evaluated.

      The full Zenodo link (https://doi.org/10.5281/zenodo.22876495) is now included in the revised version.

      Reviewer #2 (Recommendations for the authors):

      Suggestion for additional experiments:

      (17) In order to improve the CNV component of the work, the authors can employ a CNV caller as an unbiased method to identify all CNVs across the genome (including the 2 known loci). Assessing these patterns will be helpful to evaluate the sensitivity for CNV calling post-amplification.

      See response to Comment 12 of Reviewer 2.

      (18) Opportunities to include more biological relevance could include assessment of genetic changes under stress, or changes with parasite stage (current study is on promastigotes).

      We agree with the reviewer that these studies are highly relevant but we consider them out of the scope of the present work, which is more method-oriented. However, In the revised version we have expanded the discussion to include future potential applications for the SPC-PTA method:

      “Future perspectives

      The SPC-PTA scDNAseq workflow described here opens new possibilities for understanding the biology and adaptation mechanisms in Leishmania and other microbial eukaryotes. For instance, scDNAseq has been used to study DNA replication programs, revealing fork progression speeds and replication timing along the cell cycle in mammalian cells [67,68]. Unlike most eukaryotes, Leishmania has a unique DNA replication program based on a single large replication origin per chromosome which is highly active during S-phase and which is complemented by thousands of minor low-efficiency origin sites that are active during G1 and G2/M phases [69,70]. However, it is still unclear if there is cell-to-cell variability in origin use and replication timing, and how this may link to genome instability, which could be addressed using the SPC-PTA workflow in parasites at different stages of the cell cycle. Additionally, the SPC-PTA workflow could be applied to capture rare recombination events that occur in the insect vector – events that contribute to Leishmania genetic diversity but are hard to catch with bulk methods. It has been demonstrated that Leishmania undergo a cryptic sexual recombination following meiotic patterns of genome inheritance [71–73]. However, gamete-like cells were never identified. Our tool could be applied to identify cells harbouring whole-genome loss-of-heterozygosity signatures, which would be a strong indicative of meiosis.

      Another potential application is to combine the SPC-PTA workflow with loss-of-function assays to investigate key molecular factors involved in genome instability and DNA replication. For instance, small interfering RNA (siRNA) perturbations were combined with single-cell DNA sequencing to reveal a central role of Rap1 interacting factor 1 (RIF1) in coordinating replication timing in mouse embryos [74]. Although some Leishmania species lack a fully functional RNA interference pathway [75], loss-of-function assays can be achieved with CRISPR-Cas9-mediated gene knock-out [76]. More recently, genome-wide perturbation assays were made possible using CRISPR-Cas base editors opening the door to systematic, high-throughput functional screens in Leishmania [77,78]. Coupling these perturbation strategies with SPC-PTA could therefore enable direct testing of how some genes may shape replication dynamics, chromosome segregation, and genome instability at single-cell resolution.

      Lastly, the use of semipermeable capsules itself is also a key innovation and open the possibility of other applications. For instance, as we demonstrated, parasites remain alive after SPC encapsulation, and the semi-permeable nature of SPCs allow exchange of medium nutrients and cell metabolites, allowing cultivation of parasites inside SPCs [79]. This could be used to grow parasite clones trapped in SPCs, which would prevent cross-clone competition, allowing the recovery of slow-growing clones which would be otherwise outcompeted by faster-replicating clones. This is particularly important, e.g., for the study of quiescence, an emerging field of interest in Leishmania and other pathogens due to its adaptive role 80–83, as it would allow to cultivate and separate parasites with a low replicative phenotype.”

      Recommendations for improving the writing and presentation:

      (19) The paragraph in the Introduction beginning with "Although emulsion droplet..." could possibly be moved to the methods to provide a rationale for current procedures- as is, it dilutes the message at hand.

      We have removed this paragraph from the introduction and have replaced it with a short explanation about SPCs at the end of the introduction:

      “The main advantage of SPCs over emulsion droplet capturing lies in its semipermeable nature: large biomolecules (such as genomic DNA or whole organelles) are retained inside the capsule, while small molecules (e.g. enzymes, buffers, cofactors) can diffuse in and out [30]. Moreover, SPCs are resistant to harsh lysis chemicals, deep freezing and heat incubations. These properties permit multi-step reactions to be performed in the pools of encapsulated cells by simply washing or exchanging the surrounding solution, making custom protocol modifications easy.”

      (20) In the Introduction, the section describing the previous 10x study is relevant to understand the rationale, but again could be truncated, or moved to the methods or discussion.

      (21) The paragraph in the introduction beginning with "In this context, Leishmania..." could be combined with the paragraph introducing Leishmania ("To fully understand...." to improve flow and minimize repetitive information.

      We have restructured the introduction by rearraging the paragraphs and removing too technical information, so Leishmania is introduced earlier:

      “Introduction

      Genome instability plays a paradoxical and yet pivotal role in the evolutionary success of many unicellular pathogens. While genomic integrity is typically vital for cellular function, moderate levels of instability – either through intra-chromosomal copy number variations (CNV) or through dosage changes of whole chromosomes (aneuploidy) – can facilitate survival under environmental stress by quickly diversifying phenotypes in a cell population [1-3]. For instance, aneuploidy promotes survival to drug pressure and host immunity in Candida albicans [4,5], and CNVs were linked to survival under nitrogen-limiting conditions in Saccharomyces cerevisiae [6]. Aneuploidy and/or CNVs are also commonly found in cancer and are linked to tumor progression and drug resistance [7,8]. Moreover, these types of structural variation are also found in protist parasites such as Giardia intestinalis, Plasmodium spp., Trypanosoma cruzi, and Leishmania [9-13], representing potential adaptive mechanisms in clinically relevant organisms.

      Leishmania is a protist parasite that cause leishmaniasis, a neglected tropical disease which affects more than 99 countries with 700,000-1,000,000 new cases every year [14]. These parasites also represent an important model to study genome instability in eukaryotes, owing to its remarkable genomic plasticity and the central role that genome instability plays in its biology. First, while most eukaryotes maintain a euploid genome, i.e., with equal copy numbers of each chromosome, Leishmania breaks this rule, as aneuploidy is not an exception but the standard for these parasites. In its most basic form, aneuploidy is present as a characteristic polysomy of chromosome 31 contrasting with an otherwise fully diploid genome [15]. However, high levels of chromosome instability lead to frequent dosage changes involving virtually any of the 36 chromosomes, making any Leishmania population a ‘mosaic’ of distinct aneuploid karyotypes [16,17]. Aneuploidy patterns can shift in response to environmental stresses [18-21] and are directly reflected into RNA levels [18,22] and partially at protein levels [23]. In addition, Leishmania genome instability is also expressed in the form of frequent CNVs. Small segments of 20–70 kb can form extrachromosomal circular or linear amplicons carrying genes, including those encoding drug resistance factors [24]. Expansion of intra-chromosomal loci is also common. For instance, a common CNV found in chromosome 23 of some L. donovani strains was linked to resistance to antimonials in strains from Nepal [19,25]. In addition, the occurrence of mixed infections – where multiple Leishmania strains or even species coexist in the same host [26-28] – further highlight the need for genomic approaches that resolve parasite genotypes at single-cell resolution.

      In a previous study our group established the first single-cell DNA sequencing (scDNAseq) study with Leishmania [29]. Using single parasites isolated in plates with fluorescence-activated cell sorting (FACS), our group could successfully sequence 47 parasites, of which 28 had their karyotypes determined. This study also demonstrated that the whole-genome amplification (WGA) method must be chosen based on the downstream analysis, with multiple displacement amplification (MDA) being more suited for nucleotide sequence information, and PicoPlex<sup>TM</sup> performing better for structural variations such as chromosome copy number assessment and CNVs [29]. Later, we described the application of the Chromium single-cell CNV solution (10X Genomics<sup>TM</sup>) as a high-throughput, emulsion droplet-based approach that could reconstruct karyotypes in thousands of Leishmania cells, revealing potential paths towards karyotype diversification, but with no access to nucleotide variant detection due to shallow genomic coverage [17]. Moreover, the Chromium single-cell CNV solution was discontinued in 2020, with no replacement currently available to our knowledge. This gap highlights the urgent need for novel, high-throughput scDNAseq approaches.

      Here we developed a novel high-throughput scDNAseq method tailored to detecting structural and nucleotide variants at single-cell level in eukaryotic parasites such as Leishmania. Our method is based on the commercially available Single-Microbe DNA Barcoding solution (Atrandi Biosciences<sup>TM</sup>), which originally offers a workflow for cell encapsulation using semi-permeable capsules (SPCs), whole-genome amplification (WGA) and genome barcoding of bacterial cells. The main advantage of SPCs over emulsion droplet capturing lies in its semi-permeable nature: large biomolecules (such as genomic DNA or whole organelles) are retained inside the capsule, while small molecules (e.g. enzymes, buffers, cofactors) can diffuse in and out [30]. Moreover, SPCs are resistant to harsh lysis chemicals, deep freezing and heat incubations. These properties permit multi-step reactions to be performed in the pools of encapsulated cells by simply washing or exchanging the surrounding solution, making custom protocol modifications easy. We compared the performance of the method with libraries previously made with the Chromium single-cell CNV, showing that the original SPC-based protocol successfully generates scDNAseq libraries with Leishmania, but its uneven amplification prevents determination of structural variants. We solved this issue by using primary template-directed amplification (PTA) [31] as alternative WGA. This modification allowed us to fully reconstruct the karyotype of hundreds of L. donovani parasites and to detect distinct CNV patterns between cells. Moreover, the higher coverage seen in PTA unlocked the ability to simultaneously retrieve nucleotide sequence information from single-cells, which was not possible before. We demonstrate the ability of the method to distinguish parasite subpopulations of the same species, as well as small populations in the same strain, revealing minor genotypic variants among cells in clinical isolates, including variants in genes related to drug resistance in small subpopulations of parasites. Together, our results represent a significant advancement in single-cell genomics for Leishmania and other eukaryotes, providing a scalable, high-resolution tool to dissect both structural and sequence-level variation, and to deepen our understanding of parasite heterogeneity, evolution, and adaptation.”

      (22) The 4kb amplicon in HU3 is referred to as on chr 19 and 29 across the paper.

      We have fixed this mistake in the revised version.

      (23) Correct grammar: "A table summarizing the treatments that each sample was submitted to is provided in the results section (Table 1)."

      We replaced the sentence by:

      "A summary of lysis and WGA conditions is provided in the results section (Table 1)"

      (24) The Lorenz curve (Figure 2A) is not described in the methods. How was this analysis performed?

      We have now a description of the Lorenz curve in the materials and methods section

      “Lorenz curves were done for each cell by arranging genomic bins in ascending order for read counts and then calculating the cumulative read count sum. Cumulative sums were normalized by total count in each cell, and Lorenz curves were then summarized across cells of the same sample by calculating the mean cumulative fraction of counts at each genomic fraction.”

      (25) Move long lists of numbers across the Results into tables and cite them. It is hard to read as is.

      We have removed detailed statistical information from the results text. We also have included more information in Table 1.

      (26) For Figures 4A and B, please demark known amplicon boundaries to help interpret the plot. LD36 seems to have two nearby CNV regions, but the amplicon size is unclear.

      Figures 4A-B now include a dashed white line highlighting the CNV areas.

      Reviewer #3 (Public review):

      Summary:

      In this manuscript, Negreira et al. propose a new scDNAseq method, using semipermeable capsules (SPCs) and primary template-directed amplification (PTA). The authors optimize several metrics to improve their predictions, such as determining GC bias, Intra-Chromosomal fluctuation (ICF -metric to differentiate replicative and nonreplicative cells) and Intra-chromosomal coefficient of variation (ICCV - chromosome read distribution). The coverage evenness was evaluated using the fini index and the median absolute pairwise difference between the counts of two consecutive bins. They validate the proposed method using two Leishmania donovani strains isolated from different countries, BPK081 (low genomic variability) and HU3 (high genomic variability). Then, they showed that the method outperforms WGA and has similar accuracy to the discontinued 10X-scDNA (10X Genomics), further improving on short CNV identification. The authors also show that the method can identify somy variations, insertions/deletions and SNP variations across cells. This is a timely and very relevant work that has a wide applicability in copy number variation assessment using single-cell data.

      I really appreciate this work. My congratulations to the authors. All my comments below only aim to improve an already solid manuscript.

      We thank the reviewer for the enthusiasm and positive feedback.

      Remarks

      (1) Data availability: Although the authors provide a Zenodo link, the data is restricted. I also could not access the GitHub link in the Zenodo website: https://github.com/gabrielnegreira/2025_scDNA_paper. The authors should make these files available.

      Both the Zenodo (https://doi.org/10.5281/zenodo.22876495) and the GitHub (https://github.com/gabrielnegreira/2025_scDNA_paper) repositories are now publicly available.

      (2) SPC-PTA and SPC-STD cell count comparison: The authors have consistently proven that the SPC-PTA method was superior to SPC-STD. However, there are a few points that should be clarified regarding the SPC-PTA results. Is there an explanation for the lower proportion of SPC to true cells success in SPCSTD, which reflects the bimodal distribution for the reads per cell in SPC-PTA2 and a three-to-multimodal distribution in SPC-PTA1 in Figure 1B? Also, in Table 1, does the number of reads reflect the number of reads in all sequenced SPCs or only in the true cells? If it is in the SPCs, I suggest that the authors add a new column in the table with the "Number of reads in true cells" to account for this discrepancy.

      The reason for the higher presence of 'background' SPCs in the PTA samples is not clear, but we hypothesize that it could be due to PTA favoring amplification of small, free-floating DNA molecules that might have been trapped in cell-free SPCs, as PTA works with shorter amplicons. Also, the longer incubation time seen in PTA (10 h) might have allowed enhanced amplification of low quantities of free-floating DNA to detectable levels. Regarding Table 1, indeed it was only showing the total number of reads per sample. In the revised we have now included the suggested column to Table 1.

      (3) The authors should evaluate the results with a higher coverage for SCPPTA. I understand that the authors subsampled the total read to 100,000 to allow cross-sample comparisons, especially between SPC-STD and SPC-PTA. However, as they concluded that the SPC-PTA was far superior, and the samples SPC-PTA1 and SPC-PTA2 had an "elbow" of 650,493 and 448,041, respectively, it might be interesting to revisit some of the estimations using only SPC-PTA samples and a higher coverage cutoff, as 400,000.

      For the CNV analysis, we used all reads per cell, not the subsampled dataset, so SPC-PTA already benefit from their higher coverage. In addition, as mentioned in our response to Comment 8 of Reviewer 2, we have subsampled cells to 20,000 reads, not 100.000 reads per cell, to allow comparisons to the 10X datasets. We have corrected that information in the text now.

      (4) Doublet detection: I suggest that the authors be a little more careful with their definition of doublets. The doublet detection was based on diagnostic SNPs from the two strains, BPK081 and HU3, which identify doublets between two very different and well-characterised strains. However, this method will probably not identify strain-specific doublets. This is of minor importance for cloned and stable strains with few passages, as BPK081, but might be more relevant in more heterogeneous strains, as HU3. Strain-specific doublets might also be relevant in other scenarios, as multiclonal infections with different populations from the same strain in the same geographic area. One positive point is that the "between strain doublet count" was low, so probably the within-strain doublet count should be low too. The manuscript would benefit from a discussion on this regard.

      We fully agree with the reviewer. We have now included in the manuscript an estimation of total doublets based on the frequency of inter-strain doublets detected in each sample. See response to Comment 10 of Reviewer 2.

      (5) Nucleotide sequence variants and phylogeny: I believe that a more careful description of the phylogenetic analysis and some limitations of the sequence variant identification would benefit the manuscript.

      (a) As described in the methods, the authors intentionally selected two fairly different Leishmania donovani strains, HU3 and BPK081, and confirmed that the sequent variant methodology can separate cells from each strain. It is a solid proof of concept. However, most of the multiclonal infections in natural scenarios would be caused by parasite populations that diverge by fewer SNPs, and will be significantly harder to detect. Hence, I suggest that a short discussion about this is important.

      We agree that mixed infections might happen between closely related parasite populations and that the HU3/BPK081 mixture represents a relatively divergent strain pair. At the same time, our data suggest that the approach might not be restricted to highly divergent strains: in Fig. 5D, the two populations remain clearly separable using only a small subset of approximately 30 informative loci, and the within-BPK081 phylogeny in Fig. 5E further indicates that cell groups can be resolved based on comparatively few mutations. We therefore interpret the current dataset as evidence that the method retains discriminatory power with limited numbers of informative variants, while acknowledging that performance is expected to decrease as inter-clone divergence and per-cell SNP recovery decline. We have now added a small discussion about this:

      “Moreover, population-genomic studies of the L. donovani complex have identified isolates with allele-frequency patterns consistent with mixtures of genetically similar subclones, including mixtures within the same phylogenetic group [54].”

      And

      “Moreover, although the HU3/BPK081 mixture represents a relatively divergent two-strain model, the result shown in Figure 5D, which uses only a subset of 30 SNPs, indicates that separation can be achieved even with a limited set of informative loci, and the within-strain structure observed in the BPK081 tree in Figure 5E suggests sensitivity to relatively small mutational differences. This is of particular interest in cases where mixed infections happen between closely related parasite populations [54].”

      (b) The authors should expand on the description of the phylogenetic tree. In the HU3 on Figure 5F left panel, most of the variation is observed in ~8 cells, which goes from position 0 to position ~28.000. Most of the other cells are in very short branches, from ~29.000 to 30.4000 (5F right panel). Assuming that this representation is a phylogram, as the branches are short, these cells diverge by approximately 100-2000 SNPs. It is unexpected (but not impossible) that such ~8 divergent cells be maintained uniquely (or in very low counts) in the culture, unless this is a multiclonal infection. I would carefully investigate these cells. They might be doublets or have more missing data than other cells. I would also suggest that a quick discussion about this should be added to the manuscript.

      We have included in the Figure 5F a legend for the x-axis label as “cumulative inferred mutations”. We agree that the ~8 cells shown in figure 5F in HU3 with the largest cumulative inferred mutations needed closer inspection. We examined these cells in the sample depicted in figure 5F (SPC-PTA2), and observed a shift toward lower coverage and higher missingness (undefined loci), but these cells did not represent extreme QC outliers relative to the overall distributions, and other cells show comparable or even higher levels of missingness / reduced coverage but remain clustered with the main bulk rather than forming long branches in the phylogram. We have added graphs showing these values in the supplementary figure 6. In addition, we also investigated the corresponding pattern in the SPC-PTA1 sample, which represents a second independently sampled dataset from the same culture. In this second sample, we again observed a small subset of long-branch cells but this time showing a similar coverage and missingness values. Overall, this indicates that missingness and coverage may influence the inferred mutation load for the long-branch cells, but that elevated missingness alone is insufficient to fully explain why these specific cells extend to longer branches. Given that the long-branch shape is reproducible across independent samplings, we interpret the observation as most consistent with minor divergent subpopulation(s) persisting in the culture, while also acknowledging that locus-/depth-dependent calling sensitivity could contribute to the magnitude of inferred mutations in this subset. Lastly, because HU3 is a noncloned, long-term cultured population, polyclonality remains a plausible explanation for a small subset of more divergent cells. We have added this explanation in the results section of the revised version:

      “To determine whether the presence of 8 cells in long branches observed in HU3 in sample SPC-PTA2 could be driven by technical artefacts (e.g., reduced coverage, less variants called), we closely inspected the coverage values in these cells compared to the other cells in the same dataset. We did observe a consistent tendency toward lower coverage and higher variant missingness (undefined loci) in these 8 cells, but still within the range of variation seen across the other HU3 cells (supplementary figure 6A). Importantly, other cells show comparable or even higher levels of missingness/reduced coverage but remain clustered with the main bulk rather than forming long branches in the phylogram. Thus, it is unlikely that missingness/coverage is the sole cause of their phylogenetic separation. This is further supported by a similar analysis in sample SPC-PTA1, which represents and independent sampling of the same parasite population. Indeed, the phylogenetic tree of this sample showed the same overall pattern, where only a small subset of cells was present in long branches (supplementary figure 6B). However, in the case of SPC-PTA1 these cells did not show lower coverage or higher missingness compared to other cells (supplementary figure 6C). Thus, these results are most consistent with minor divergent subpopulation(s) persisting during long-term culture. As HU3 is a non-cloned isolate, polyclonality remains a plausible explanation for a small subset of more divergent cells. At the same time, we cannot exclude that locus-/depth-dependent calling sensitivity may contribute to the magnitude of inferred mutations in this subset.”

      Reviewer #3 (Recommendations for the authors):

      (6) The authors have shown the identification of two known copy number variants in these two strains. Has any effort been made to identify novel short CNVs?

      See response to Comment 12 of Reviewer 2.

      (7) In the results first section, in the passage "both strains differ in (bulk) aneuploidy profiles", please remove the parentheses from bulk.

      We have made the suggested modification.

      (8) Figure 3, D and F. Would it be possible to add legends for the colours, so that the data can be easily compared with the x-axis (karyotypes, as kar.1, kar.2, etc) in Figure 3, C and E?

      We have changed the figures 3D and F to highlight the top 5 karyotypes found in the 10X data. This helps comparing them to figures 3C and E.

      (9) Figure 5A. Would it be possible to include in the x and y axes the percentage of representation of PC1 and PC2? My guess is that most of the variability will be represented by PC1 (x-axis) as it is the one that separates the two populations and the hybrids.

      We have included the percentages of representation of the PCs in the figure in the revised version. Indeed, PC1 captured more than 90% of the variability.

      (10) In the discussion, section "SPCs as a viable tool for high throughput implementation of PTA" I would move this passage to the results (as it is a result): "By applying this strategy to Leishmania, we could sequence a total of 399 cells (from samples SPC-PTA1-2) while using the equivalent of 17 PTA reactions (17 cells) with cells isolated in plates, reducing the cost per cell by more than 20 fold."

      As mentioned in response to the Comment 15 of Reviewer 2 we have extended the discussion on costs and therefore kept this part in the discussion section.

      (11) Another advantage of the single-cell data that could be discussed by the authors is the possibility of checking if different variants occur in the same cell. For example, if a variation in position "X" in the resistance gene occurs in the same cell as the variation in position "Y". This is a great improvement compared to bulksequencing.

      We have now included a small discussion about this:

      “This is particularly relevant in protozoan parasites, where resistance may depend on multi-locus haplotypes or combinations of mutations, as illustrated by resistance against sulfadoxine-pyrimethamine treatment in Plasmodium falciparum, which is characterized by mutations in dhfr and/or dhps genes, including triple and septuple mutant forms as well as mutations in both genes6264.”

      REFERENCES

      (1) Dileep, V. & Gilbert, D. M. Single-cell replication profiling to measure stochastic variation in mammalian replication timing. Nat. Commun. 9, 427 (2018).

      (2) Miura, H. et al. Single-cell DNA replication profiling identifies spatiotemporal developmental dynamics of chromosome organization. Nat. Genet. 51, 1356–1368 (2019).

      (3) Marques, C. A., Dickens, N. J., Paape, D., Campbell, S. J. & McCulloch, R. Genomewide mapping reveals single-origin chromosome replication in Leishmania, a eukaryotic microbe. Genome Biol. 16, 230 (2015).

      (4) Damasceno, J. D. et al. Leishmania major chromosomes are replicated from a single high-efficiency locus supplemented by thousands of lower efficiency initiation events. Cell Rep. 44, (2025).

      (5) Imamura, H. et al. Evolutionary genomics of epidemic visceral leishmaniasis in the Indian subcontinent. eLife 5, e12613 (2016).

      (6) Gonzalez-Pena, V. et al. Accurate genomic variant detection in single cells with primary template-directed amplification. Proc. Natl. Acad. Sci. 118, e2024176118 (2021).

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      A primary limitation of this manuscript is its omission of foundational literature from the Schwartzberg and Littman laboratories, which originally established the indispensable role of IL-2-inducible Tcell kinase (ITK) in proximal T-cell receptor (TCR) signaling dynamics and thymic lineage commitment. Because classic studies demonstrate that ITK is a critical regulator of thymic T cell development and cellular proliferation (PMID: 8777721, 10213685), the authors' claim that "these findings indicate that ITK deficiency skews the T cell compartment toward a memory-like state, establishing a distinct immune baseline that may favor protective and regulatory responses over pathogenic inflammation" is not substantiated by evidence and requires more robust validation.

      We thank the reviewer for highlighting the foundational studies defining the role of ITK in proximal TCR signaling, thymic T-cell development, and proliferation. We agree that these studies provide essential context for interpreting the altered T-cell phenotype observed in Itk<sup>-/-</sup> mice. Accordingly, we have revised the Introduction and Discussion to incorporate this established literature, including PMID: 8777721 and 10213685, and to more clearly acknowledge the established role of ITK in T-cell development and differentiation.

      We also agree that our original statement suggesting that the memory-associated phenotype of Itk<sup>-/-</sup> mice may establish an immune baseline favoring protection from pulmonary inflammation was not directly supported by our experiments. Our data demonstrate altered relative distributions of naïve and memory-phenotype CD4<sup>+</sup> and CD8<sup>+</sup> T cells, together with increased expression of CD44, CD122, Eomes, and T-bet, but do not establish that these baseline differences mediate protection from pulmonary hemorrhage.

      We have therefore removed this causal interpretation and now present these findings as baseline characterization consistent with established ITK biology.

      The exclusive reliance on splenic immunophenotyping is a major limitation, as it fails to capture the local cellular dynamics within the primary organs of injury (the lung and kidney). Evaluating canonical and non-canonical Treg expansion solely in the spleen overlooks the distinct functional programming of tissue-resident subsets. The authors should extend their characterization of regulatory T cell compartments directly to the lungs and draining lymphoid structures.

      We thank the reviewer for this important suggestion. We agree that splenic analysis alone does not adequately capture the local regulatory T-cell response during pulmonary injury. We therefore expanded the revised manuscript to directly examine Treg populations in the lungs and draining lymph nodes.

      We now quantify canonical (CD4<sup>+</sup>CD25<sup>+</sup>Foxp3<sup>+</sup>) and non-canonical (CD4<sup>+</sup>CD25<sup>-</sup>Foxp3<sup>+</sup>) Tregs in the lungs of WT and Itk<sup>-/-</sup> mice, demonstrating that the altered regulatory phenotype associated with ITK deficiency is also evident locally in the lung (Figure 5E). In addition, using CD45.1 recipients and CD45.2 WT or Itk<sup>-/-</sup> donor Tregs, we directly tracked transferred cells and observed significantly greater accumulation of Itk<sup>-/-</sup> donor Tregs in both the lungs and draining lymph nodes (Figure 5F–I). Donor-derived CD4<sup>+</sup>Foxp3<sup>+</sup>CD45.2<sup>+</sup> cells were also confirmed in these tissues by immunofluorescence microscopy (Figure 5J).

      These new experiments extend our analysis beyond the spleen and provide direct evidence that the enhanced regulatory phenotype associated with ITK deficiency is present within tissues relevant to pulmonary inflammation.

      More importantly, the authors overlook key historical publications that explicitly established ITK as a negative "rheostat" or gatekeeper for regulatory T cell (Treg) differentiation. Specifically, Huang et al. (PMID: 25063868) previously demonstrated that Treg abundance is inversely correlated with ITK expression, and that ITK activity serves as a vital negative tuner of IL-2-driven Foxp3<sup>+</sup> Treg expansion. Since it is already well-established that suppressing or deleting ITK promotes Treg accumulation and function, and that these cells are intrinsically vital to suppressing systemic autoimmunity, it is unclear how these findings expand upon our existing mechanistic understanding of ITK regulatory biology.

      We thank the reviewer for highlighting the important study by Huang et al. (PMID: 25063868), which established ITK as a negative regulator of IL-2-driven Foxp3<sup>+</sup> Treg expansion. We agree that increased Treg abundance following loss of ITK is established biology and should not be presented as a novel finding. We have revised the Introduction and Discussion accordingly and incorporated this foundational literature. The present study extends this established ITK–Treg relationship into autoimmune pulmonary hemorrhage by demonstrating functional and tissue-associated differences between WT and Itk<sup>-/-</sup> Tregs. Equaldose adoptive-transfer experiments showed that purified Itk<sup>-/-</sup> Tregs provide substantially greater protection than WT Tregs in an otherwise ITK-sufficient host, including reduced pulmonary pathology and proteinuria and improved survival (Figures 5 and 6). Congenic CD45.1/CD45.2 tracking further demonstrated greater accumulation of Itk<sup>-/-</sup> donor Tregs in the lungs and draining lymph nodes (Figure 5F–J).

      In addition, lung-derived Itk<sup>-/-</sup> Tregs expressed higher levels of Amphiregulin (AREG), identifying a tissue-repair-associated phenotype (Figure 5K), while RNA-seq demonstrated a distinct transcriptional state enriched for metabolic, proliferative, and regulatory programs (Figure 7). Thus, the advance of this study is not increased Treg abundance itself, but the demonstration that ITK-deficient Tregs exhibit enhanced protective activity and distinct tissue-associated properties during severe autoimmune pulmonary injury.

      Reviewer #2 (Public review):

      (1) All loss-of-function experiments are from a global ITK knockout. This is a major limitation and weakness of this study. The protection observed in the intact knockout, therefore, cannot be attributed to Tregs specifically. The Treg-intrinsic claim rests almost entirely on a single adoptive-transfer experiment. In order to show that this effect is Treg-specific, the authors would need to generate a Treg-specific ITK-deficient mouse.

      We thank Reviewer #2 for highlighting this important limitation. We agree that experiments performed in global Itk<sup>-/-</sup> mice cannot establish that the protective phenotype is specifically attributable to Treg-intrinsic loss of ITK, because other ITK-deficient immune populations may also contribute. We have revised the manuscript to make this limitation explicit and agree that a Treg-specific conditional model, such as Foxp3-Cre × Itk^fl/fl mice, would be required to establish Treg-specific necessity in the intact disease model. To directly assess the contribution of Tregs independently of the global knockout environment, we transferred equal numbers (1 × 10<sup>6</sup>) of FACS-purified WT or Itk<sup>-/-</sup> CD4<sup>+</sup>CD25<sup>+</sup>Foxp3<sup>+</sup> Tregs into pristane-challenged WT CD45.1 recipients. Thus, all endogenous immune and stromal compartments in the recipients remained ITK-sufficient. Under these conditions, Itk<sup>-/-</sup> Tregs provided substantially greater protection than WT Tregs, including reduced pulmonary pathology and proteinuria and improved survival (Figures 5 and 6). Congenic tracking further demonstrated greater accumulation of Itk<sup>-/-</sup> donor Tregs in the lungs and draining lymph nodes. We therefore conclude that purified Itk<sup>-/-</sup> Tregs are sufficient to confer enhanced protective activity in an ITK-sufficient host, while recognizing that these experiments do not establish that Tregs are solely responsible for the protection observed in global Itk<sup>-/-</sup> mice.

      (2) In their sufficiency experiment (adoptive Treg cell transfer), donor and/or host cells are not congenially marked, so persistence, lung trafficking, and in vivo expansion of transferred Tregs are not demonstrated.

      We thank Reviewer #2 for this important comment. To directly address this limitation, we performed new adoptive-transfer experiments using CD45.1 WT recipients and CD45.2 WT or Itk<sup>-/-</sup> donor Tregs, allowing transferred cells to be clearly distinguished from endogenous host cells. Following transfer, flow cytometric analysis demonstrated significantly greater accumulation of donor-derived Itk<sup>-/-</sup> Tregs in the lungs and draining lymph nodes compared with WT donor Tregs (Figure 5F–I). Within the CD45.2<sup>+</sup> donor population, cells retained Foxp3 expression, and both CD25<sup>+</sup>Foxp3<sup>+</sup> and CD25<sup>-</sup>Foxp3<sup>+</sup> regulatory populations were detectable at the experimental endpoint. The presence of donor-derived CD4<sup>+</sup>Foxp3<sup>+</sup>CD45.2<sup>+</sup> cells within the lungs and draining lymph nodes was independently confirmed by immunofluorescence microscopy (Figure 5J).

      These new experiments directly demonstrate localization and enhanced accumulation/recovery of Itk<sup>-/-</sup> Tregs in disease-relevant tissues. However, because these are endpoint measurements, we have avoided attributing the increased donor-cell recovery specifically to proliferation or trafficking, as differences in survival, retention, or recruitment may also contribute.

      (3) The authors claim that ITK-deficient Tregs possess enhanced metabolic fitness. This conclusion is based on transcriptional profiling of isolated splenic Tregs from unchallenged mice, yet it concerns lung protection during active disease narrative. Additional functional validation would be needed (Seahorse assay, mitochondrial mass/potential, etc). Some of these GSEA programs enriched in ITK-deficient Tregs could reflect a more general proliferative signature.

      We thank Reviewer #2 for this thoughtful critique. We agree that enrichment of metabolic pathways by RNA-seq does not, by itself, demonstrate enhanced metabolic fitness and that direct functional assays, such as Seahorse analysis or measurements of mitochondrial mass and membrane potential, would be required to establish altered metabolic function.

      We also acknowledge that our RNA-seq was performed on FACS-purified splenic Tregs from unchallenged mice and therefore does not directly define the transcriptional state of Tregs within the inflamed lung during active pulmonary hemorrhage. Our intent was to determine whether ITK deficiency is associated with baseline transcriptional differences prior to disease challenge. The analysis identified enrichment of oxidative phosphorylation, mTORC1, glycolysis, MYC, E2F, and cell-cycle-associated programs in Itk<sup>-/-</sup> Tregs (Figure 7). We agree that some of these signatures may reflect proliferative or activation-associated transcription rather than enhanced metabolic function. We have revised the RNA-seq analysis, please updated Figure 8 and supplementary Tables. Accordingly, we have revised the Results and Discussion to describe these data as a distinct transcriptional state enriched for metabolic and proliferative programs, rather than direct evidence of enhanced metabolic fitness. We also note that disease-state lung Treg transcriptomics and direct metabolic assays will be required to determine the functional significance of these pathways during pulmonary injury.

      Reviewer #3 (Public review):

      The novelty of this study lies in the association between ITK-deficient Tregs and pulmonary hemorrhage in autoimmunity. The weakness of the manuscript is the lack of sufficient experiments to support the claim that ITK-deficient mice show protection specifically mediated by Treg cells, and to demonstrate that ITK-deficient Treg cells are more efficient than WT Treg cells in regulating other immune cells that drive pulmonary damage. The authors performed all the experiments in ITK global knockout mice, in which not only T cells but all other cell types are deficient in ITK. Furthermore, they have not performed any functional analysis to demonstrate the functional differences between WT Treg and ITK-deficient Treg cells, undermining the novelty of this study.

      We sincerely thank Reviewer #3 for this constructive critique. We agree that experiments performed in global Itk<sup>-/-</sup> mice alone cannot establish that protection is specifically mediated by Tregs, because other ITK-deficient immune populations may also contribute. We have revised the manuscript to clearly acknowledge this limitation.

      To directly compare the functional protective capacity of WT and Itk<sup>-/-</sup> Tregs independently of the global knockout environment, we transferred equal numbers of FACS-purified CD4<sup>+</sup>CD25<sup>+</sup>Foxp3<sup>+</sup> Tregs into pristane-challenged WT recipients. Under these conditions, Itk<sup>-/-</sup> Tregs provided substantially greater protection than WT Tregs, including reduced pulmonary pathology and proteinuria, a more regulatory systemic cytokine profile, and improved survival (Figures 5 and 6). These experiments provide direct in vivo evidence that purified Itk<sup>-/-</sup> Tregs have enhanced protective activity in an otherwise ITK-sufficient host.

      We further performed CD45.1/CD45.2 congenic tracking and observed significantly greater accumulation of donor-derived Itk<sup>-/-</sup> Tregs in the lungs and draining lymph nodes compared with WT donor Tregs (Figure 5F– J). Donor-derived cells retained Foxp3 expression following transfer. In addition, canonical Tregs isolated directly from Itk<sup>-/-</sup> lungs expressed substantially higher levels of Amphiregulin (AREG), identifying a tissue-repair-associated phenotype that accompanies their enhanced protective activity (Figure 5K). We have also incorporated our previous functional studies demonstrating enhanced suppressive activity of Itk<sup>-/-</sup> regulatory T-cell populations compared with WT Tregs (Mammadli et al., Clinical and Translational Medicine, 2021).

      Thus, the advance of the present study is not simply increased Treg abundance after loss of ITK, but the demonstration that purified Itk<sup>-/-</sup> Tregs provide greater protection than WT Tregs in an ITK-sufficient host, accumulate more prominently in disease-relevant tissues, and exhibit increased AREG expression. We nevertheless acknowledge that a Treg-specific conditional Itk knockout will ultimately be required to establish Treg-specific necessity in the intact disease model.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      Major concerns

      (1) The authors demonstrate that the frequency of memory-like T cells is elevated in the spleens of Itk-/- mice, but the absolute cellular numbers are notably absent. This proportional observation lacks conceptual novelty, as highly similar findings regarding the baseline expansion of memory-like/innate-like T cells under ITK-deficient conditions have been extensively established, most notably by the Schwartzberg laboratory (PMID: 16860760, 16860760). These early reports should be cited in the introduction and not presented as novel findings. More critically, the direct relevance of this baseline phenotype to the active autoimmune disease model remains unaddressed. The frequencies of these effector and memory-like compartments are evaluated exclusively in unperturbed, naïve animals and are never tracked or revisited during the subsequent kinetics of the pristane-induced lung injury model.

      We thank Reviewer #1 for this important critique and for highlighting the foundational studies describing memory-like/innate-like T-cell development in ITK-deficient mice. We agree that this phenotype is well established and should not be presented as a novel finding. We have therefore incorporated the relevant literature, including PMID: 16860760, and now present Figures 1 and 2 as baseline characterization of the established Itk<sup>-/-</sup> T-cell phenotype. We also agree that the frequency measurements in these figures do not demonstrate expansion in absolute cellular terms. Accordingly, we have removed the term “expansion” for this baseline naïve, central-memory, and effector-memory populations and now describe the findings as differences in their relative frequencies or distribution. Importantly, these analyses were performed in unchallenged mice, and we did not longitudinally track these memory-associated CD4<sup>+</sup> and CD8<sup>+</sup> populations during pristane-induced disease. We therefore no longer suggest that this baseline phenotype directly mediates protection from pulmonary hemorrhage. The revised manuscript now clearly separates this established baseline ITK phenotype from the disease-focused findings, with the mechanistic emphasis placed on the regulatory T-cell compartment, for which we provide direct functional and tissue-level analyses during pulmonary injury.

      (2) This memory-like cell population expansion is observed strictly within naïve, SPF mice that have had no prior exposure to foreign antigens; it raises an important question of whether these are bona fide, antigen-experienced memory cells, or do they represent a "virtual memory" population (CD44+CD122+CD49d-) that typically arises from aberrant T cell development and homeostatic dysregulation? Prior work has already demonstrated that compromised TCR signal strength via ITK deficiency alters critical aspects of homeostatic proliferation, metabolic programming, and non-conventional effector differentiation in unexposed environments (Huang et al., 2018; bioRxiv, https://doi.org/10.1101/359604). Without providing absolute counts during active disease and ruling out a virtual memory phenotype, the authors' conclusion that this baseline skewing directly orchestrates active protection against pathogenic inflammation is currently unsupported.

      We thank Reviewer #1 for this important comment. We agree that the CD44<sup>+</sup>CD122<sup>+</sup> phenotype observed in naïve SPF Itk<sup>-/-</sup> mice cannot be assumed to represent conventional antigen-experienced memory. Prior studies have shown that reduced ITK-dependent TCR signaling can promote innate-like or virtual-memory-associated T-cell populations under antigen-naïve conditions, and we have incorporated the relevant literature, including Huang et al., into the revised Introduction and Discussion. Because our experiments did not include CD49d or other markers required to distinguish conventional memory from virtual-memory cells, we have avoided assigning a definitive origin to these populations and now refer to them as memory-phenotype or memory-associated T cells. We also agree that these baseline measurements were obtained from unchallenged mice and that we did not determine absolute numbers or longitudinally track these populations during pristane-induced disease. We have therefore removed the interpretation that baseline memory-associated skewing directly promotes protection from pulmonary inflammation. Accordingly, Figures 1 and 2 are now presented as characterization of an established consequence of ITK deficiency, while our disease-focused mechanistic conclusions are based on the Treg experiments performed during pulmonary injury.

      (3) The manuscript relies predominantly on qualitative histological representations to assess autoimmune tissue pathology. To substantiate the study's claims, the authors should provide standardized quantification of the histological changes. Additionally, direct measurement of autoimmune T cell responses, rather than descriptive tissue overviews, is required to definitively prove that ITK deficiency suppresses pathogenic autoimmunity.

      We thank Reviewer #1 for these important comments. Regarding tissue pathology, the lung histology was evaluated using standardized semi-quantitative scoring performed by a board-certified pathologist blinded to genotype and treatment group. These quantitative scores are presented in Figure 3 and described in the Methods. We have revised the manuscript to make this analysis more explicit. The histopathologic findings are further supported by quantitative measurements of pulmonary CD11b<sup>+</sup>Ly6C<sup>+</sup> inflammatory monocytes and CD11b<sup>+</sup>Ly6G<sup>+</sup> neutrophils, as well as proteinuria as a measure of renal involvement (Figures 3 and 4). We also agree that direct analysis of antigen-specific pathogenic T-cell responses would provide additional mechanistic information. Such populations were not directly measured in the present study, and we have therefore revised the manuscript to avoid implying that ITK deficiency specifically suppresses autoreactive conventional T cells. Instead, our data support the conclusion that ITK deficiency is associated with reduced inflammatory tissue injury and that purified Itk<sup>-/-</sup> Tregs are sufficient to confer enhanced protection in WT recipients. This is supported by reduced pulmonary pathology, decreased inflammatory-cell accumulation, improved proteinuria, and the adoptive-transfer experiments. We have revised the Discussion accordingly to distinguish these directly demonstrated effects from the broader question of how ITK regulates antigen-specific autoimmune T-cell responses.

      (4) While the adoptive transfer experiments suggest that Tregs from injured ITK-deficient animals possess enhanced protective capacity, the interpretation of these data is heavily confounded by a lack of absolute cellular quantification. Prior literature establishes that while ITK deficiency increases Treg frequency, the absolute number of Tregs remains unchanged due to concurrent reductions in global T cell cellularity (PMID: 25063868). Consequently, the authors must provide the absolute numbers of Tregs infiltrating the lungs both at baseline and post-injury. Since the authors adoptively transfer matched numbers of WT and KO Tregs, they are testing an artificial cellular ratio that may completely bypass the actual physiological abundance, contraction, or recruitment dynamics operating within the lung tissue in vivo. Furthermore, the current experimental design is insufficient to establish whether this protection depends specifically on injury-primed effector Treg programming or whether naïve ITK-deficient Tregs are sufficient.

      We thank Reviewer #1 for this important critique. We agree that Treg frequencies alone do not establish physiological abundance, particularly because previous studies have shown that increased Treg frequency in Itk<sup>-/-</sup> mice may occur without a proportional increase in absolute Treg number.

      To address this concern, we have added absolute quantification of canonical (CD4<sup>+</sup>CD25<sup>+</sup>Foxp3<sup>+</sup>) and non-canonical (CD4<sup>+</sup>CD25<sup>-</sup>Foxp3<sup>+</sup>) Tregs in the lung at baseline and following adoptive transfer. Absolute numbers were determined from the total viable cellular recovery from each individual tissue together with the complete sequential flow-cytometric gating hierarchy. These analyses provide both frequency and absolute cellular abundance and demonstrate greater recovery of donor-derived Itk<sup>-/-</sup> Tregs in the inflamed lung and draining lymph nodes following transfer (Figure 5E–I).

      We also agree that equal-dose adoptive transfer does not reproduce the endogenous WT: Itk<sup>-/-</sup> Treg ratio. Rather, this experiment was intentionally designed as a controlled functional comparison in which identical numbers of purified WT or Itk<sup>-/-</sup> Tregs were introduced into the same ITK-sufficient recipient environment. The greater protection and tissue accumulation observed with Itk<sup>-/-</sup> Tregs therefore reflect differences between the transferred populations under equivalent starting conditions, rather than differences in the number of cells administered. Importantly, the donor Tregs used for these experiments were isolated from unchallenged WT and Itk<sup>-/-</sup> Foxp3-reporter mice. Thus, prior pristane-induced injury was not required for the enhanced protective activity of Itk<sup>-/-</sup> Tregs. We have clarified this point in the revised manuscript.

      Together, these analyses distinguish Treg frequency from physiological abundance, provide quantitative assessment of donor-cell recovery in disease-relevant tissues, and demonstrate that the enhanced protective capacity of Itk<sup>-/-</sup> Tregs does not require prior injury-dependent priming.

      (5) The transcriptomic analyses suggest metabolic and functional reprogramming of ITK-deficient Tregs. However, the interpretation of these findings currently remains speculative, as it relies on pathway analysis and no key genes involved in any of these programs were identified/highlighted as key differentially expressed genes. Lastly, there is no functional validation to suggest that these transcriptional changes are functionally relevant.

      We thank Reviewer #1 for this important critique. We agree that pathway-level enrichment alone does not establish functional metabolic reprogramming and that the genes underlying these signatures should be provided more clearly. To address this concern, we have expanded the transcriptomic analysis to identify the individual differentially expressed genes contributing to the major pathways observed in Itk<sup>-/-</sup> Tregs, including mTORC1, oxidative phosphorylation, MYC/E2F, glycolytic, and regulatory programs. We have revised Figure 8 and added supplementary tables providing the gene-level differential-expression data for the canonical and non-canonical Treg comparisons, allowing the underlying molecular changes to be evaluated directly rather than relying solely on pathway enrichment scores. We also agree that these transcriptional signatures do not demonstrate enhanced metabolic fitness. Direct functional assays, such as extracellular flux analysis, mitochondrial mass or membrane-potential measurements, would be required to establish altered metabolic function. We have therefore revised the Results and Discussion to describe Itk<sup>-/-</sup> Tregs as exhibiting a distinct transcriptional state enriched for metabolic, proliferative, and regulatory programs, while acknowledging that some pathways may reflect proliferation or activation.

      Separately, lung-derived Itk<sup>-/-</sup> Tregs showed increased AREG protein expression (Figure 5K), which we interpret as a tissue-repair-associated phenotype rather than functional validation of the metabolic pathways.

      Thus, we have added gene-level resolution to the RNA-seq analysis while narrowing our mechanistic interpretation to what is directly supported by the data. Accordingly, we have revised the Results and Discussion to describe these data as a distinct transcriptional state enriched for metabolic and proliferative programs, rather than direct evidence of enhanced metabolic fitness.

      Minor concerns

      (1) The introduction is structurally imbalanced, with three extensive paragraphs dedicated to describing and discussing the study's results. On the contrary, critical historical studies are missing from this section.

      We thank Reviewer #1 for this constructive comment. We agree that the original Introduction devoted excessive space to summarizing our findings while providing insufficient historical context for ITK biology. We have therefore substantially shortened and reorganized the Introduction. The revised version now incorporates the foundational studies defining ITK function in TCR signaling and T-cell development, as well as the work establishing ITK as a regulator of Foxp3<sup>+</sup> Treg differentiation and expansion. We also removed the extended discussion of our results and now conclude the Introduction with a concise statement of the knowledge gap and objective of the present study.

      (2) In Figure 1A and 1E, a substantial CD44-CD62L- population is present in both WT and ITK KO mice, potentially reflecting gating-related issues or loss of CD62L staining.

      We thank Reviewer #1 for this careful observation. We agree that the CD44<sup>-</sup>CD62L<sup>-</sup> population should be interpreted cautiously, as reduced CD62L staining may reflect biological variability or loss/shedding during tissue processing. To improve transparency, we have added the complete flow-cytometric gating strategy to the revised manuscript (Supplementary Figure 1; page 50, lines 845–855), including sequential exclusion of debris, doublets, and non-viable cells before identification of CD3<sup>+</sup>, CD4<sup>+</sup>, and CD8<sup>+</sup> T-cell populations. WT and Itk<sup>-/-</sup> samples were processed and analyzed under identical conditions. Importantly, we do not assign biological significance to the CD44<sup>-</sup>CD62L<sup>-</sup> population. Our conclusions are restricted to the conventionally defined naïve (CD44^lo^CD62L^hi^), central-memory (CD44^hi^CD62L^hi^), and effector memory (CD44^hi^CD62L^lo^) populations.

      (3) The characterization of the myeloid compartment is limited given the highly complex nature of pulmonary inflammation in small vessel vasculitis models. To rigorously evaluate the local immune microenvironment, the authors must provide a detailed profiling of key populations within the affected tissues, including alveolar macrophages, interstitial macrophages, neutrophils, and eosinophils.

      We thank Reviewer #1 for this important comment. We agree that pulmonary inflammation involves a heterogeneous myeloid compartment and that more comprehensive profiling of alveolar macrophages, interstitial macrophages, eosinophils, and other subsets would provide additional insight. In the present study, our myeloid analysis focused on two populations strongly associated with acute inflammatory lung injury: CD11b<sup>+</sup>Ly6C<sup>+</sup> inflammatory monocytes and CD11b<sup>+</sup>Ly6G<sup>+</sup> neutrophils. Quantitative flow cytometry demonstrated significantly reduced accumulation of both populations in the lungs of pristane-treated Itk<sup>-/-</sup> mice compared with WT controls (Figure 3H–I). We acknowledge that this does not represent comprehensive profiling of the pulmonary myeloid compartment, and we have revised the manuscript to make this limitation explicit and to avoid broader claims of global myeloid remodeling. We also note in the Discussion that detailed analysis of macrophage and granulocyte subsets will be important for determining how ITK-dependent regulatory responses influence the broader pulmonary inflammatory environment.

      (4) Although the study focuses on suppression of autoimmunity, chronic ITK deficiency may plausibly impair protective immunity against infection or malignancy. Some discussion of these potential tradeoffs would improve the translational interpretation of the findings.

      We thank Reviewer #1 for raising this important translational consideration. We agree that chronic or systemic inhibition of ITK could impair protective immunity, particularly against infection and potentially malignancy. We have expanded the Discussion to address these potential trade-offs. In particular, we now note that inherited ITK deficiency in humans has been associated with impaired protective immune responses and increased susceptibility to infection, emphasizing that prolonged systemic ITK suppression cannot be assumed to be without consequence. At the same time, our previous studies in alloimmunity demonstrated that attenuation of ITK signaling can markedly reduce graft-versus-host disease while preserving substantial graft-versus-leukaemia activity (PMIDs: 33324410, 33851101, and 34919342). These findings suggest that pathogenic and protective immune responses may differ in their dependence on ITK signaling. We therefore emphasize that the translational effects of ITK modulation will likely depend on the magnitude, duration, and cellular context of inhibition. Future studies will be needed to determine whether partial, transient, or cell-selective ITK targeting can retain anti-inflammatory and Treg-associated benefits while preserving antimicrobial and antitumor immunity.

      Reviewer #3 (Recommendations for the authors):

      The manuscript by Hossain et al investigates the role of ITK as a central regulator of autoimmune lung injury, using the pristane-induced pulmonary hemorrhage (PH) model.

      The authors claim that the deficiency of ITK confers complete protection primarily by marked remodeling of the T cell compartment, including expansion of CD44<sup>+</sup>, CD122<sup>+</sup>, Eomes<sup>+</sup>, T-bet<sup>+</sup> memory-like subsets, and significant enrichment of Foxp3<sup>+</sup> regulatory T cells (Tregs). However, they have used the ITK global KO mouse model, which undermines their claim. Adoptive transfer of Treg cells to suppress autoimmunity has been shown before in various studies. The authors have performed an adoptive transfer of ITK-deficient Tregs, which they claim are more efficient at suppressing autoimmunity, based solely on two cytokine levels in systemic circulation. Although the authors identified the ITK-deficient Treg as key mediators of tissue protection, they have not provided any functional characterization of ITK-deficient Treg cells as compared to WT Treg cells. There are a few comments that will help to strengthen the findings and establish the importance of ITK regarding autoimmune PH.

      We sincerely thank Reviewer #3 for this rigorous and constructive critique. We agree that experiments performed in global Itk<sup>-/-</sup> mice alone cannot establish that protection is specifically mediated by Tregs, because other ITK-deficient immune populations may also contribute. We have revised the manuscript to make this limitation explicit.

      Importantly, the functional comparison between WT and Itk<sup>-/-</sup> Tregs in the revised study extends beyond circulating cytokines. Equal numbers of FACS-purified WT or Itk<sup>-/-</sup> CD4<sup>+</sup>CD25<sup>+</sup>Foxp3<sup>+</sup> Tregs were transferred into pristane-challenged WT recipients, in which all endogenous immune and stromal compartments remained ITK-sufficient. Under these conditions, Itk<sup>-/-</sup> Tregs provided substantially greater protection than WT Tregs, including reduced pulmonary pathology and proteinuria, a more regulatory systemic cytokine profile, and improved survival (Figures 5 and 6).

      These experiments demonstrate enhanced protective activity of purified Itk<sup>-/-</sup> Tregs in an ITK-sufficient host. We further performed CD45.1/CD45.2 congenic tracking and observed greater accumulation of donor-derived Itk<sup>-/-</sup> Tregs in the lungs and draining lymph nodes compared with WT donor Tregs (Figure 5F–J). In addition, lung-derived Itk<sup>-/-</sup> Tregs expressed substantially higher levels of Amphiregulin (AREG), identifying a tissue-repair-associated phenotype (Figure 5K). We have also more clearly incorporated our previous functional study demonstrating enhanced suppressive activity of Itk<sup>-/-</sup> regulatory T-cell populations compared with WT Tregs (PMID: 34919342).

      Together, these findings extend previous work by demonstrating that Itk<sup>-/-</sup> Tregs exhibit enhanced protective activity and distinct tissue-associated properties during autoimmune pulmonary haemorrhage. We nevertheless acknowledge that a Treg-specific conditional Itk knockout will ultimately be required to establish Treg-specific necessity in the intact disease model.

      Major comments:

      (1) In Figure 1, the authors have shown the T cell profile in the spleen from WT vs ITK-KO mice under homeostatic conditions. But it will be important to show the immune cell population, both innate and adaptive, in the lung, as it is the organ of focus for their study.

      We sincerely thank Reviewer #3 for this important suggestion. We agree that because the lung is the primary site of injury in this model, characterization of the local pulmonary immune compartment is important.

      In the revised manuscript, we have expanded our lung-focused analyses. We now directly quantify canonical (CD4<sup>+</sup>CD25<sup>+</sup>Foxp3<sup>+</sup>) and non-canonical (CD4<sup>+</sup>CD25<sup>-</sup>Foxp3<sup>+</sup>) Tregs in the lungs of WT and Itk<sup>-/-</sup> mice (Figure 5E), demonstrating that the altered regulatory phenotype associated with ITK deficiency is also evident locally within the lung.

      During pristane-induced disease, we additionally quantified key inflammatory innate populations and found significantly reduced accumulation of CD11b<sup>+</sup>Ly6C<sup>+</sup> inflammatory monocytes and CD11b<sup>+</sup>Ly6G<sup>+</sup> neutrophils in Itk<sup>-/-</sup> lungs compared with WT controls (Figure 3H–I). Furthermore, using CD45.1/CD45.2 congenic adoptive transfer, we directly tracked WT and Itk<sup>-/-</sup> donor Tregs and observed greater accumulation of Itk<sup>-/-</sup> Tregs in the lungs and draining lymph nodes (Figure 5F–J).

      We acknowledge that the present study does not provide comprehensive profiling of all pulmonary immune populations, including macrophage subsets, eosinophils, and conventional effector T-cell populations. We have therefore revised the manuscript to make the scope of our lung immune analysis explicit and identify broader pulmonary immune profiling as an important area for future study

      (2) The authors need to show the status of Treg cells in the spleen and lung of ITK KO mice under homeostatic conditions.

      We thank Reviewer #3 for this important suggestion. We agree that defining the homeostatic Treg compartment in both the spleen and lung is important for interpreting the disease-associated changes.

      In the revised manuscript, we now provide baseline characterization of canonical (CD4<sup>+</sup>CD25<sup>+</sup>Foxp3<sup>+</sup>) and non-canonical (CD4<sup>+</sup>CD25<sup>-</sup>Foxp3<sup>+</sup>) Tregs in naïve, unchallenged WT and Itk<sup>-/-</sup> mice. Homeostatic splenic Tregs are shown in Supplementary Figure 7, demonstrating the established increase in the non-canonical Treg compartment in Itk<sup>-/-</sup> mice. We also added direct analysis of lung Tregs under homeostatic conditions (Figure 5E), demonstrating that the altered regulatory phenotype associated with ITK deficiency is also present locally in the lung prior to pristane challenge.

      These analyses establish the baseline Treg phenotype in both systemic and pulmonary compartments and provide an appropriate reference for interpreting the subsequent disease and adoptive-transfer experiments.

      (3) The authors claim ITK deficiency shifts the memory T cell phenotype based on surface markers and transcription factors TBET and Eomes. It is well established that the memory T cell phenotype depends on a fine balance between TBET and Eomes (Cárdenas et al., Nature, 2024; Kar et al., Science Advances, 2026). Therefore, to support the claim, authors need to co-stain TBET and Eomes to show the relative balance of the TFs.

      We thank Reviewer #3 for this important comment and for highlighting the literature emphasizing that memory T-cell differentiation is influenced by the relative balance of T-bet and Eomes. We agree that because T-bet and Eomes were measured independently in our experiments, our data do not establish their relative balance or co-expression at the single-cell level. Definitive analysis would require simultaneous co-staining of these transcription factors.

      Accordingly, we have revised the manuscript to avoid interpreting T-bet and Eomes expression as evidence of a specific memory differentiation program. Figures 1 and 2 are now presented as baseline characterization of the established Itk<sup>-/-</sup> T-cell phenotype. We describe the CD44/CD62L data as showing altered relative frequencies of naïve and memory-phenotype populations, while increased T-bet, Eomes, CD44, and CD122 expression is reported separately as a differentiation-associated phenotype.

      We no longer infer that a specific T-bet/Eomes balance contributes to the memory phenotype or to protection from pulmonary hemorrhage, and we have incorporated the literature cited by the reviewer into the revised Discussion.

      (4) A higher expression of TBET and Eomes could also lead to enhanced production of Th1 cytokines. Have the authors measured the CD4 T cell cytokines or CD8 T cell granzyme/perforin production in ITK KO mice?

      We thank Reviewer #3 for this important point. We agree that increased T-bet and Eomes expression may be associated with altered CD4<sup>+</sup> and CD8<sup>+</sup> T-cell effector function and that direct functional measurements would be required to establish this.

      In the present study, we did not directly measure cytokine production by conventional CD4<sup>+</sup> or CD8<sup>+</sup> T cells, nor did we quantify granzyme or perforin expression. Although systemic IFN-γ, TNF-α, IL-6, and IL-17 were measured during pristane-induced disease, these serum measurements do not identify the cellular source of the cytokines.

      We have therefore revised the Results and Discussion to avoid inferring enhanced Th1 or cytotoxic function from increased T-bet and Eomes expression. Figures 1 and 2 are now presented as baseline phenotypic characterization of the conventional T-cell compartment, while the mechanistic conclusions of the study remain focused on the regulatory T-cell response during pulmonary hemorrhage.

      We have also acknowledged that direct functional analysis of conventional CD4<sup>+</sup> and CD8<sup>+</sup> T cells will be required to define the consequences of altered T-bet and Eomes expression in this model.

      (5) The authors have shown that ITK KO mice significantly restrict the pulmonary hemorrhage after 14 days post-pristane injection. Have the authors evaluated the findings at a longer time point, such as 6-8 weeks post-pristane, which is considered the optimal time point for disease progression? This will clarify whether ITK deficiency completely inhibits the autoimmunity or delays its progression.

      We thank Reviewer #3 for raising this important point regarding disease kinetics. We agree that later time points, such as 6–8 weeks after pristane administration, are commonly used to evaluate chronic manifestations of pristane-induced systemic autoimmunity.

      However, the pulmonary hemorrhage phenotype examined in our study follows a much more acute and severe course. We therefore extended our analysis to include survival and added these data to the revised manuscript (Figure 3—figure supplement 2). All pristane-treated WT mice died within approximately 20 days, whereas Itk<sup>-/-</sup> mice exhibited significantly prolonged survival.

      Because WT mice do not survive to the 6–8-week time point in this model, a direct WT versus Itk<sup>-/-</sup> comparison at these later stages is not feasible without substantial survivor-selection bias. We have therefore clarified that the present study addresses the acute, severe phase of pristane-induced pulmonary hemorrhage.

      Importantly, the survival data demonstrate that ITK deficiency protects against the early lethal phase of disease rather than simply delaying the day-14 pulmonary phenotype. However, these findings do not establish that ITK deficiency completely prevents later chronic manifestations of pristane-induced autoimmunity. We have added this limitation to the Discussion and identify longer-term analysis of surviving Itk<sup>-/-</sup> mice as an important future direction.

      (6) In Figure 3, the authors have shown that ITK KO mice show less monocyte infiltration in pristane-injected mice. However, they have not shown effector T cell percentages, such as Th1 and Th17, which are important drivers of disease progression. Given their focus on Treg cells, it will be important to show the effector T-cell population in the lung.

      We thank Reviewer #3 for this important comment. We agree that direct quantification of pulmonary Th1 and Th17 populations would provide additional insight into the balance between pathogenic effector T cells and Tregs during pulmonary hemorrhage.

      In the present study, we did not directly quantify lung Th1 or Th17 cells by intracellular cytokine or transcription-factor staining. We have therefore revised the manuscript to avoid implying that our experiments demonstrate direct suppression of these effector T-cell populations.

      Our lung analysis instead demonstrated significantly reduced accumulation of CD11b<sup>+</sup>Ly6C<sup>+</sup> inflammatory monocytes and CD11b<sup>+</sup>Ly6G<sup>+</sup> neutrophils in Itk<sup>-/-</sup> mice (Figure 3), together with increased pulmonary Treg populations (Figure 5). We also observed reduced systemic IFN-γ, TNF-α, IL-6, and IL-17 during disease (Figure 4); however, we recognize that these serum measurements do not establish the cellular source of these cytokines. Accordingly, we now distinguish the directly measured pulmonary cellular changes from broader Th1/Th17-associated inflammatory responses and identify direct profiling of lung effector T-cell populations as an important area for future investigation.

      (7) In Figure 4, the authors have shown several plasma cytokine levels in KO vs WT mice to support their hypothesis. However, as their focus is on alveolar hemorrhage, they have also mentioned that these cytokines influence the pulmonary damage by altering neutrophil infiltration and vascular permeability. Showing data on neutrophil and vascular damage will strengthen their claim.

      We thank Reviewer #3 for this constructive suggestion. We agree that direct assessment of pulmonary neutrophil accumulation and tissue injury provides important context for interpreting the systemic cytokine changes observed during pulmonary hemorrhage.

      To address this concern, we added quantitative flow-cytometric analysis of pulmonary neutrophils. CD11b<sup>+</sup>Ly6G<sup>+</sup> neutrophils were significantly reduced in the lungs of pristane-treated Itk<sup>-/-</sup> mice compared with WT controls (Figure 3I). Together with the reduced CD11b<sup>+</sup>Ly6C<sup>+</sup> inflammatory monocytes, these findings demonstrate decreased accumulation of major inflammatory innate-cell populations in the injured lung.

      Pulmonary injury was also evaluated using blinded, standardized histopathologic scoring. WT mice exhibited extensive intra-alveolar hemorrhage, erythrocyte accumulation, and disruption of alveolar architecture, whereas Itk<sup>-/-</sup> mice showed markedly reduced hemorrhage and preserved lung architecture (Figure 3B–E). We acknowledge that the present study does not include a direct assay of vascular permeability or endothelial barrier function. We have therefore revised the manuscript to describe these findings as evidence of reduced alveolarcapillary injury and pulmonary hemorrhage rather than as a direct demonstration of improved vascular permeability.

      (8) The authors mentioned non-canonical Treg cells without proper characterization. These Treg cells are reported to lack CD25 and, in some cases, FOXP3, and to have reduced suppressive function. Therefore, if ITK KO mice show that both canonical and non-canonical Treg cells are increased, this raises the question of how that balance leads to less pulmonary hemorrhage. The authors need to clarify their findings and discuss the relevance.

      We sincerely thank Reviewer #3 for raising this important point. In the present study, we define non-canonical Tregs specifically as CD3<sup>+</sup>CD4<sup>+</sup>CD25<sup>-</sup>Foxp3<sup>+</sup> cells. These cells were identified using Foxp3-RFP reporter mice, and therefore the population analyzed here is Foxp3<sup>+</sup>CD25 but lacks CD25.

      We agree that CD25<sup>-</sup>Foxp3<sup>+</sup> Tregs may exhibit reduced stability or suppressive function in some settings. However, in our previous study, we performed dedicated phenotypic and functional analyses of this population and demonstrated that Itk<sup>-/-</sup> CD4<sup>+</sup>CD25<sup>-</sup>Foxp3<sup>+</sup> Tregs possess substantial suppressive activity in both in vitro and in vivo assays (Mammadli et al., Clinical and Translational Medicine, 2021; PMID: 34919342). We have revised the manuscript to more clearly incorporate this prior work.

      In the present study, both canonical CD25<sup>+</sup>Foxp3<sup>+</sup> and non-canonical CD25<sup>-</sup>Foxp3<sup>+</sup> Treg populations were increased in Itk<sup>-/-</sup> mice, including in the lung. However, we did not independently test the protective function of the non-canonical subset. Importantly, the adoptive-transfer experiments were initiated with purified canonical CD25<sup>+</sup>Foxp3<sup>+</sup> Tregs.

      We have therefore revised the manuscript to avoid implying that non-canonical Tregs independently mediate protection from pulmonary hemorrhage. Instead, we interpret their increase as an additional feature of the altered regulatory T-cell compartment associated with ITK deficiency, while restricting the direct functional conclusion to the enhanced protective activity of purified Itk<sup>-/-</sup> canonical Tregs.

      (9) Do the ITK KO mice have non-canonical Treg in the homeostatic lung?

      We thank Reviewer #3 for this specific question. Yes, Itk<sup>-/-</sup> mice contain noncanonical CD4<sup>+</sup>CD25<sup>-</sup>Foxp3<sup>+</sup> Tregs in the lung under homeostatic conditions.

      To directly address this point, we added flow-cytometric analysis of canonical CD4<sup>+</sup>CD25<sup>+</sup>Foxp3<sup>+</sup> and non-canonical CD4<sup>+</sup>CD25<sup>-</sup>Foxp3<sup>+</sup> Tregs in the lungs of naïve, unchallenged WT and Itk<sup>-/-</sup> mice. These data demonstrate that non-canonical Tregs are present in the homeostatic lung and are increased in Itk<sup>-/-</sup> mice compared with WT controls (Figure 5E).

      Thus, the non-canonical Treg population observed during pulmonary hemorrhage is not exclusively induced by disease but is already present as part of the baseline regulatory T-cell phenotype associated with ITK deficiency

      (10) The authors stated that ITK-/- Tregs confer enhanced protection against PH by shifting the cytokine balance from a proinflammatory toward a pro-resolving state. However, the adoptive transfer of ITK KO Treg results in differences only in IFNγ and IL10 levels compared with WT Treg. The authors need to clearly discuss this.

      We thank Reviewer #3 for this careful observation. We agree that our original wording overstated the extent of the cytokine differences between recipients of WT and Itk<sup>-/-</sup> Tregs. Upon direct comparison of the two Treg-treated groups, the clearest statistically significant differences were observed for IFN-γ and IL-10. Although Itk<sup>-/-</sup> Treg treatment was associated with reductions in additional proinflammatory cytokines, these changes should not be interpreted as demonstrating significant superiority over WT Tregs for every cytokine measured.

      We have therefore revised the Results and Discussion to emphasize that, compared with WT Tregs, Itk<sup>-/-</sup> Tregs produced a greater reduction in IFN-γ together with increased IL-10, and we have removed the broader statement that they uniformly shift the entire systemic cytokine profile from a proinflammatory to a pro-resolving state.

      Importantly, the enhanced protective activity of Itk<sup>-/-</sup> Tregs is supported not only by cytokine measurements, but also by reduced pulmonary pathology and proteinuria, improved survival, and greater accumulation of donor-derived Itk<sup>-/-</sup> Tregs in the lungs and draining lymph nodes.

      (11) The claim that ITK-deficient Treg is better than WT Treg is the novelty of the study. Therefore, the functional characterization, such as cytokine profile and suppressive functions, could be shown to support their claim. Adoptive transfer of WT-Treg cells provides significant protection, as shown by Dall'Era et al. (2019, Arthritis Rheumatol) and by the authors in Figure 5. Providing supporting data on the advantages of ITK-KO Treg will be important for strengthening the study's novelty.

      We sincerely thank Reviewer #3 for this important comment. We agree that the novelty of the present study is not simply that Tregs can protect against pulmonary hemorrhage, which has been previously demonstrated, but that Itk<sup>-/-</sup> Tregs exhibit enhanced protective activity compared with WT Tregs in this disease setting.

      To directly address this point, we compared equal numbers (1 × 10<sup>6</sup> cells per recipient) of FACS-purified WT or Itk<sup>-/-</sup> CD4<sup>+</sup>CD25<sup>+</sup>Foxp3<sup>+</sup> Tregs following transfer into pristane-challenged WT recipients. WT Tregs provided measurable protection, consistent with previous studies. Importantly, however, Itk<sup>-/-</sup> Tregs provided substantially greater protection, including reduced pulmonary pathology and proteinuria and improved survival (Figures 5 and 6). Thus, the functional advantage of Itk<sup>-/-</sup> Tregs is supported by disease outcomes beyond systemic cytokine measurements.

      We further performed CD45.1/CD45.2 congenic tracking and observed greater accumulation/recovery of donor-derived Itk<sup>-/-</sup> Tregs in the lungs and draining lymph nodes compared with WT donor Tregs (Figure 5F–J). In addition, Itk<sup>-/-</sup> Treg-treated recipients showed a greater reduction in IFN-γ and increased IL-10 compared with WT Treg-treated recipients. Canonical Tregs isolated directly from Itk<sup>-/-</sup> lungs also expressed substantially higher levels of AREG, identifying a tissue-repair-associated phenotype (Figure 5K).

      We have also more clearly incorporated our previous functional study demonstrating enhanced suppressive activity of Itk<sup>-/-</sup> regulatory T-cell populations in in vitro and in vivo assays (Mammadli et al., Clinical and Translational Medicine, 2021; PMID: 34919342).

      Together, these findings demonstrate that the advantage of Itk<sup>-/-</sup> Tregs over WT Tregs is supported by greater protection after equal-dose transfer, enhanced accumulation in disease-relevant tissues, differential regulation of IFN-γ and IL-10, and increased AREG expression. We have clarified that AREG is associated with this protective phenotype but has not been shown here to be required for protection.

      Minor comments

      (1) In Figure 3, the authors need to provide important experimental control as H & E lung and spleen images under homeostatic conditions, without pristane.

      We thank Reviewer #3 for this important suggestion. We agree that homeostatic histological controls are necessary to determine whether the differences observed after pristane challenge reflect pre-existing tissue abnormalities. In the revised manuscript, we have added H&E analyses of lungs and spleens from naïve, unchallenged WT and Itk<sup>-/-</sup> mice. Both genotypes exhibited normal baseline tissue architecture, with no evidence of pulmonary hemorrhage or abnormal splenic pathology (Figure 3—figure supplement 1A–D and Figure 3—figure supplement 3A–C). These controls confirm that the pulmonary and splenic abnormalities observed after pristane administration arise during disease rather than from pre-existing histological differences between WT and Itk<sup>-/-</sup> mice.

      (2) In Supplementary Figure 6, the axis legend needs correction.

      We sincerely thank Reviewer #3 for the careful review and for identifying this error. We have corrected the axis legend accordingly. The corrected graph is now presented as Supplementary Figure 7 (page 56) in the revised manuscript.

    1. Author response:

      The following is the authors’ response to the previous reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      The authors investigate whether the brain uses the same neural representations for "absence" when it comes to seeing nothing versus thinking of zero. To do this, they recorded MEG while participants performed two types of tasks: (1) a perceptual detection task where subjects reported the presence or absence of a faint visual stimulus, and (2) numerical comparison tasks where subjects saw streams of numbers or dot patterns (both including "0" or empty sets) and decided which of two color-coded streams had a larger average. Multivariate decoders were trained to distinguish "present" vs "absent" in the detection task and "zero" vs "non-zero" in the numerical tasks. As a sanity check, the authors first replicate that symbolic (digit "0") and non-symbolic (empty dot sets) zeros share a common neural code (cross-format generalization). Crucially, they find that this numerical "zero" code does not overlap with the code for perceptual absence: cross-decoding between the detection task and number tasks yields Bayes factors strongly favoring distinct representations. In other words, the brain's pattern for "no grating was seen" cannot decode the pattern for "the number zero was shown," and vice versa. A small brief cross-decoding effect around 300 ms was observed, which the authors attribute to low-level visual confounds (and which they test with an additional control decoder for stimulus presence), but overall the evidence supports a dissociation.

      Strengths:

      The authors investigate whether the brain uses the same neural representations for "absence" when it comes to seeing nothing versus thinking of zero. To do this, they recorded MEG while participants performed two types of tasks: (1) a perceptual detection task where subjects reported the presence or absence of a faint visual stimulus, and (2) numerical comparison tasks where subjects saw streams of numbers or dot patterns (both including "0" or empty sets) and decided which of two color-coded streams had a larger average. Multivariate decoders were trained to distinguish "present" vs "absent" in the detection task and "zero" vs "non-zero" in the numerical tasks. As a sanity check, the authors first replicate that symbolic (digit "0") and non-symbolic (empty dot sets) zeros share a common neural code (cross-format generalization). Crucially, they find that this numerical "zero" code does not overlap with the code for perceptual absence: cross-decoding between the detection task and number tasks yields Bayes factors strongly favoring distinct representations. In other words, the brain's pattern for "no grating was seen" cannot decode the pattern for "the number zero was shown," and vice versa. A small brief cross-decoding effect around 300 ms was observed, which the authors attribute to low-level visual confounds (and which they test with an additional control decoder for stimulus presence), but overall the evidence supports a dissociation.

      We thank the reviewer for their careful reading of our work and their helpful comments and suggestions. Below, we respond to each of the reviewer’s concerns and highlight the relevant changes we have made in accordance with their suggestions.

      Weaknesses:

      R1C1. My main concern is whether the perceptual and numerical tasks are truly matched aside from their "absence" content. The perceptual task is a simple yes/no detection of a faint grating, whereas the numerical tasks involve holding two streams of 5 items in working memory and comparing their average. These tasks differ in many ways (stimulus complexity, decision rule, cognitive load), so it is possible that the lack of cross-decoding is due to general task differences rather than a fundamental "absence vs zero" dissociation. The authors do partially address this by showing that other shared aspects (like color) can cross-generalize, but one might still worry that an "absence" decision in a detection task engages different attentional or decisional mechanisms than a "zero" decision in a numerical context.

      We thank the reviewer for prompting us to expand on this aspect of the design. We in fact deliberately chose to examine distinct perceptual and numerical tasks because we wanted to create a strict test of whether absence representations generalise. Having two closely-matched tasks would have led to a converse difficulty in interpreting any successful cross-decoding, had it been obtained. This is because it would have been difficult to ascertain whether cross-stimulus generalisation was because of a true domain-general representation of absence, or whether it was driven by other features of task design and stimulus-response contingencies. We employed the same strategy (of employing different tasks) in our previous work to identify cross-format representations numerical zero (Barnett & Fleming, 2024, Current Biology). Indeed, we think this was one of that study’s strengths, since the generalisation of ‘zero representations’ across numerical formats could not be explained by task similarity.

      We appreciate though that our null findings shift the burden of proof to ensuring that this design choice has not resulted in a type 2 error. We think this is unlikely for several reasons: first, we focus on stimulus-triggered responses, and within each task, we are able to robustly decode stimulus-triggered absence; second, in our previous work we obtained robust generalisation of absence representations even when tasks are distinct, a finding we now replicate here with more closely matched tasks; and finally, as the reviewer indicates, our control analyses of colour do show positive generalisation across task format.

      To make the motivation behind this design choice clearer to the reader, we have modified the following passage (p. 6):

      Importantly, we used numerical and perceptual tasks that differed with respect to their structure and temporal dynamics. This ensured that any successful cross-decoding of absence could not be attributed to low-level or structural similarities between tasks, and instead would indicate a domain-general representation of absence. This approach builds on our previous work in which we identified a shared representation of numerical absence across non-symbolic and symbolic stimuli that generalised across task formats (Barnett & Fleming, 2024).

      However, the reviewer is correct that this approach does not allow us to test whether unmeasured variables (such as cognitive load, decision making, etc) could interfere with cross-decoding, thus eliciting false negatives in our analyses. To elaborate on this limitation, and to suggest possible extensions to this work that could begin to help resolve this issue, we have added the following passage to the discussion (p. 19):

      The tasks we employed in this study were dissimilar by design. This offered a strict test of the hypothesis that absences share representational currency across perceptual and numerical domains, because successful cross-decoding could not be artificially inflated by low-level task similarities across domains (Barnett & Fleming, 2024). However, this approach also carries the risk that task dissimilarity reduced our sensitivity to shared representations of absence. We think this is unlikely for several reasons: first, we focus on stimulus-triggered responses, and within each task, we are able to robustly decode stimulus-triggered absence representations; second, in our previous work we obtained robust generalisation of absence representations even when tasks are distinct, a finding we now replicate here with more closely matched tasks (Barnett & Fleming, 2024); and finally, our control analyses of colour do indicate positive generalisation across task format. Future work could explore the relationship between absences across domains using factorial designs that vary both domain and task independently, thus exposing possible interactions between absence representations and task context.

      R1C2. The numerical averaging task closely resembles that used by Spitzer et al. (2017), who reported that both behavioral weighting and neural representational geometry exhibit anti-compression, with disproportionately stronger representations for larger numerosities. In contrast, the present manuscript interprets its decoding results as reflecting an ordered numerical continuum. It is therefore unclear whether the current analyses are sensitive only to ordinal structure or whether they also preserve the nonlinear representational geometry reported previously. This distinction is important because the interpretation of zero as part of a numerical continuum depends on the geometry of that continuum. The authors should clarify whether their representational analyses are compatible with the anti-compressed neural number line described by Spitzer et al., or explain why the two studies yield different conclusions.

      We thank the reviewer for raising this interesting point. To address this question, we fitted the same model from Spitzer et al. (2017) to both numerical tasks in our data. The model fits two free parameters of interest: b, which controls the disproportionate bias to larger numbers and k, which controls the anti-compression (overweighting of extreme values) mentioned by the reviewer.

      We found no difference in k values across any combination of tasks (Spitzer et al (2017) vs our non-Symbolic task; Spitzer et al (2017) vs our symbolic task; our non-symbolic vs symbolic task (all ps > .74)). The b parameter also did not differ significantly between any of the tasks (all ps > .06). Author response image 1 plots the decision values for each of the three tasks, illustrating the comparable weighting of extreme values and a consistent tendency to overweight larger values.

      Author response image 1.

      Model fits to data from Spitzer et al., (2017) and our two numerical tasks. Parameter values were consistent across all three tasks, replicating Spitzer et al.’s original finding of an anti-compressed number line with a bias towards larger numbers in both of our tasks (non-symbolic and symbolic) that extend the number line to include zero.

      Seeing as our focus in the main paper is specifically on the representation of absence, we would prefer to retain these analyses in the publicly viewable response to reviewers rather than in the manuscript itself.

      R1C3. The authors attempt to account for non-numerical visual information by controlling for Total Dot Area and Density. While this is an important control, these two variables do not exhaust the visual dimensions that covary with numerosity in dot displays. A large body of work has demonstrated that multiple continuous features, including average item area, total surface area, convex hull (field area), and density, are inherently intercorrelated and cannot all be independently controlled simultaneously (e.g., Piazza et al., 2004; Gebuis & Reynvoet, 2004; Castaldi et al., 2019; Karami et al., 2025). Consequently, controlling only two features does not fully establish that the decoded signal specifically reflects numerosity. To better characterize the stimulus space, I encourage the authors to report the correlation matrix among the principal visual features of the dot arrays (average item area, total surface area, convex hull/field area, density, and numerosity). In addition, it would be informative to quantify the unique contribution of each feature to the neural data using a multiple-regression RSA or semi-partial correlations RSA, similar to the analyses employed by Castaldi et al. (2019) and more recently by Karami et al. (2025). Such analyses would provide a more rigorous assessment of whether the decoded representations uniquely reflect numerosity after accounting for correlated visual properties.

      We thank the reviewer for raising this point. We agree that a range of low-level visual properties of non-symbolic dot stimuli may covary with numerosity, and that it’s important to consider whether these properties may affect our results. As the reviewer points out, our original stimulus set was constructed with the aim of ensuring numerosity was uncorrelated with total dot area and dot density. We have followed the reviewer’s suggestion and now expand our correlation matrix to include not only the total dot area and density of dots, but also the convex hull and average dot area. We note that the empty set stimuli that are the focus of our analyses of absence remain unaffected by visual properties covarying with numerosities above zero.

      To highlight these new analyses we have added the following sentence to our methods (p. 22):

      “Numerical dot stimuli were created using custom MATLAB 2021b (Mathworks) scripts and consisted of different numbers of dots (from zero to five) on grey backgrounds. Total dot area was controlled for by systematically reducing the size of the dots as the number of dots increased, such that the total number of pixels included in a stimulus were constant across numerosities. In both stimulus sets, 50% of dots were black and 50% were white, such that the contrast of the dot patterns did not increase with numerosity (the increase in contrast generated by an increasing number of black dots was cancelled out by the increased number of white dots). Figure S1 reports the correlation between total dot area, density, luminance, convex hull area, average dot size, and numerosity in the non-symbolic stimulus set, highlighting how our stimulus-generating procedure successfully controlled for the association between certain low-level visual properties and numerosity. Given that various low-level visual features naturally covary with one another, it is difficult to control for all features in one stimulus set. However, the empty set stimuli that are the focus of our analyses of absence remain unaffected by visual properties covarying with numerosities above zero.”

      The reviewer also suggests we perform RSA analyses to correlate visual features of our non-symbolic dot stimuli with the neural data to quantify the extent to which low-level visual features of the non-symbolic stimuli may be driving the ordered representations we observe in this task. While this analysis may help contextualise our findings on numerosities above zero, we think it is less relevant for understanding the degree to which absence representations are shared between numerical and perceptual domains. Indeed, for the empty set stimuli denoting absences in the non-symbolic task, many of the low-level visual properties discussed above cannot be computed. Here, instead, the primary visual confound of interest is that of similarities between empty sets and noise patches in the detection task, which we now tackle in response to the reviewer’s comment R1C6 below.

      R1C4. The manuscript reports predominantly diagonal temporal generalization for non-symbolic numerosity, implying a rapidly evolving neural code. However, a recent study using time-resolved decoding of numerical representations (Karami et al., 2025) reported substantial off-diagonal temporal generalization, consistent with a temporally stable representational format. Although methodological differences between the studies may account for this discrepancy, the apparent contrast deserves discussion. In particular, it would be useful for the authors to clarify whether the differences arise from task demands, stimulus characteristics, preprocessing and decoding procedures, or from theoretical differences in what is being decoded. More generally, these findings raise the possibility that the temporal stability of numerical representations is task-dependent rather than fixed. If so, it would be interesting to discuss whether task demands might also influence the relationship between perceptual and conceptual representations of absence. Such a possibility could help explain why cross-decoding was not observed in the present study and suggests an interesting direction for future research.

      We thank the reviewer for prompting us to consider differences in our results and those of Karami et al (2025). The reviewer is correct that, in the present manuscript, our decoding exhibits a diagonal pattern. However, the critical difference between these analyses and those in Karami et al (2025) are that we are decoding across numerical format and perceptual domain, while Karami et al decode within a single non-symbolic format. Indeed, in our previous work (Figure 2B, Barnett and Fleming, 2024), when we perform decoding analyses within format, we can identify a similar off-diagonal pattern shown as that found in Karami et al.. As such, it appears to be a difference between the within- and cross-format decoding of number that underlies this change in temporal structure. Indeed, when we run the same, within-format analyses in our current MEG data, we also observe a stronger off-diagonal pattern, particularly in the first 400ms after stimulus presentation:

      Author response image 2.

      Within and Cross-Format Decoding of Empty Sets vs Dot Patterns and Symbolic Zero vs Positive Numbers.

      Other factors may play a role in differences between the studies. Stimulus presentation was twice as long in Karami et al’s study compared to our experiment. Only one stimulus format was used by Karami et al, increasing the number of repetitions per non-symbolic numerosity and thus statistical power. Indeed, in Barnett and Fleming (2024), when we used a slower non-symbolic task and restricted the experiment to include two tasks (compared to three in the present study), we can identify non-symbolic numerosity decoding which is very similar to that of Karami et al.

      We agree with the reviewer that the temporal structure of domain-general and domain-specific representations deserves further study, and in our previous Current Biology paper we speculated on some reasons for these differences. In the current manuscript for space reasons, we prefer to restrict the discussion to issues specific to the question of representations of absence.

      R1C5. Throughout the manuscript, the authors appear to treat non-symbolic numerosity as a conceptual representation and contrast it with perceptual absence. I find this interpretation insufficiently justified. A substantial body of behavioral (Anobile et al., 2013; Cicchini et al., 2016) and neuroimaging (Piazza et al., 2004; Castaldi et al., 2019; Karami et al., 2025) research has argued that non-symbolic numerosity is represented as a perceptual attribute extracted relatively early in the visual processing hierarchy, even if its precise computational origin remains debated. Consequently, it is not immediately clear why non-symbolic numerosity should be regarded as a conceptual representation comparable to symbolic number or the concept of zero. This distinction is important because it directly affects the interpretation of the negative cross-decoding results. If both perceptual absence and non-symbolic numerosity are primarily perceptual representations, the absence of cross-decoding cannot be taken as evidence that perceptual and conceptual absence are represented differently. Rather, it may simply indicate that these two perceptual representations encode different visual attributes. I therefore encourage the authors to clarify their theoretical position regarding the representational status of non-symbolic numerosity and to discuss how their interpretation relates to influential theories of numerical cognition that conceptualize non-symbolic numerosity as an early perceptual representation rather than an abstract conceptual one.

      This is a critical point and we thank the reviewer for encouraging us to clarify our position here. We agree that there is good evidence to suggest that the extraction of non-symbolic numerosity depends in part on perceptual representations. Indeed, we did not intend for our non-symbolic numerosity stimuli to strictly probe for conceptual representations. Rather, the primary aim of the experiment was to test for representations of absence across numerical and non-numerical domains, with detection of low-level visual stimuli being most clearly perceptual, and symbolic numerals most clearly conceptual. To ensure clarity here, we have reworded several passages in the abstract and introduction and introduced a new paragraph in the discussion:

      Abstract (p. 2):

      “The ability to represent absences is fundamental to human perception and cognition. Sensitivity to non-numerical perceptual absences depends on inferring a lack of sensory evidence, enabling the recognition of a lack of environmental resources or other objects. In turn, encoding numerical absence as a concept – in the form of the number zero – has enabled a multitude of technological and mathematical advances.”

      “In contrast, we show that these representations of numerical absence are distinct to those evoked by non-numerical perceptual absences.”

      Introduction (p. 5):

      “Neural representations of the number zero show similarly distinct properties. Like non-numerical perceptual absences, numerical absences are actively represented in higher-order brain regions of non-human primates (Okuyama et al., 2015; Ramirez-Cardenas et al., 2016) and crows (Kirschhock et al., 2021). “

      “Finding that conceptualisation of zero overlaps with representations of sensory absence in a detection task would offer support to accounts that propose the evolutionary and developmental trajectory of zero concepts emerge from a more basic ability to track an absence of sensation (Nieder, 2016; Barton, 2020). On the other hand, finding that neural representations of non-numerical and numerical absences are distinct would support an extension of a boundary between perception and cognition into the domain of absence perception (Block, 2023; Firestone & Scholl, 2016).”

      Discussion (p. 17):

      “In order to interpret the lack of generalisation of absence representations between the detection and non-symbolic numerosity tasks, it is useful to consider the representational status of non-symbolic numerosities. A large body of both behavioural (Burr et al., 2018; Burr & Ross, 2008; Cicchini et al., 2016) and neuroimaging (Castaldi et al., 2019; Park et al., 2016; Piazza et al., 2004) work has suggested that non-symbolic numerosities are represented as a primary perceptual attribute in the visual system, on a par with properties such as contrast, size, and orientation. In this light, a lack of absence generalisation between the detection and non-symbolic numerosity tasks would not delimit a boundary between perceptual and conceptual absences, but rather support a boundary between numerical and non-numerical perceptual absences. Such a divide may be due to perceptual-numerical absence representations requiring additional processes mapping non-symbolic empty sets onto a neural number line (Barnett & Fleming, 2024; Kutter et al., 2024), which is not required – and, as the present results seem to indicate, not instantiated – by non-numerical perceptual representations. “

      R1C6a: I have two related concerns regarding the discussion of Paul et al. (2022). First, I think it would be helpful to describe more explicitly what was measured in that study. To my understanding, Paul et al. quantified the aggregate Fourier power (AFP) of the stimuli.

      We agree that the methodology of Paul et al. (2022) could be made clearer. We have edited the following passage introducing the study (p. 13):

      “One possibility is that the spatial frequency profile of non-symbolic dot patterns covaries with numerosity and can drive early visual responses to non-symbolic stimuli in numerical tasks. This has been shown in previous work where the aggregate Fourier power of dot-stimuli correlates with numerosity (Paul et al., 2022).”

      R1c6b: Moreover, AFP has primarily been discussed in the context of dot arrays with constant dot size within each stimulus. In the current manuscript, it is not entirely clear from the Methods whether dot sizes vary within displays. I therefore encourage the authors to explicitly describe how dot sizes were generated and varied across stimuli. If AFP is correlated with numerosity in the present stimulus set, it would also be helpful to explain how the analyses dissociate neural representations of numerosity from those potentially driven by AFP.

      We apologise for omitting this information in our initial submission. To be clear, dot size did not vary within each stimulus display. We have now made this explicit in the Methods section describing stimuli (p. 21):

      “Low-level visual properties of the stimuli (total dot area, density, luminance) did not covary with numerosity (Figure S1). Total dot area was controlled for by systematically reducing the size of the dots as the number of dots increased, such that the total number of pixels included in a stimulus were constant across numerosities. Dot sizes were held constant within each individual stimulus display.

      R1C6c: Second, I am not entirely convinced by the argument that training a classifier to distinguish Hits from Correct Rejections is sensitive to aggregate Fourier power. It would be helpful if the authors could explain more explicitly why this decoding contrast should be expected to be sensitive to AFP. As currently written, the logical connection between the AFP hypothesis and the proposed control analysis is not entirely clear.

      We thank the reviewer for the opportunity to clarify why we ran this control analysis. The purpose of this analysis was to demonstrate that low-level visual properties could in principle drive spurious generalisation between the detection and non-symbolic task. Showing this is important for two reasons. First, it provides a potential explanation for the small cluster of generalisation between the detection and non-symbolic tasks. Second, it bolsters our main analysis (Figure 2), by showing that even in the context of residual stimulus-related drivers of cross-decoding, we can still find very strong evidence for an absence of shared representations between the two tasks.

      More generally, the grating stimuli and empty noise patches naturally vary in a variety of low-level visual properties, not only of their spatial frequency profiles, but their contrast, density, and so forth. Even though our main analysis controlled for stimulus presence in the detection task (equal number of stimulus present trials in ‘seen’ and ‘unseen’ responses), we reasoned that it was still possible that these stimulus features may covary with participants’ decisions on a trial-by-trial basis. It would therefore be possible for our Presence vs. Absence decoder to pick up on a difference in low-level visual features, such as spatial frequency, AFP, contrast, etc.

      To ascertain whether any of these low-level visual properties could in principle drive spurious generalisation between the detection and non-symbolic task, we performed an analysis where a decoder was trained to classify empty noise patches from high-contrast gratings (Misses vs. Hits), thus enabling it to rely on differences in stimulus information when classifying the neural data. We then tested this on neural data collected during Empty Set vs. Non-Zero Dot stimuli, reasoning that any above-chance decoding would reflect low-level visual similarities between the two stimulus sets that were distinct from the representations of absence we were interested in. We feel comfortable making this assertion because, in our main analysis, we controlled for stimulus visual information, and saw very little generalisation. Thus, any additional cross-generalisation in the present analysis must be due to the added stimulus confounds.

      To make this reasoning more explicit in the manuscript, we have reworded the Results section that motivates and introduces this control analysis (p. 13-15):

      “Taken together, our analyses indicate strong evidence (as derived from BFs) that neural representations of perceptual and numerical absence can be robustly identified in patterns of MEG activity, and that these representations are distinct rather than shared. As noted above, the one exception to this pattern was a small but significant cluster of activity around 300ms that indicated some shared representation of non-symbolic and perceptual absences (Figure 2A; Figure 2B). We considered that this exception may have been driven by uncontrolled shared variance in lower-level visual features of our detection and empty-set stimuli. One possibility is that the spatial frequency profile of non-symbolic dot patterns covaries with numerosity and can drive early visual responses to non-symbolic stimuli in numerical tasks. This has been shown in previous work where the aggregate Fourier power of dot-stimuli correlates with numerosity (Paul et al., 2022). Additionally, stimuli containing dots naturally possess higher contrast than blank empty-set stimuli. Crucially, similar visual properties may also characterise our detection stimuli, with spatial frequency and contrast profiles differing between grating stimuli and noise patches. It is possible that these, or other, stimulus-related visual confounds may contribute to the brief cluster of generalisation observed between perceptual and non-symbolic stimuli. By explicitly attempting to decode the physical presence or absence of the grating (which up until now was controlled for in our analysis) we aimed to further characterise this component of visually-driven shared variance.

      To evaluate this possibility, we trained a decoder to classify Hits vs. Correct Rejections within the detection task (Figure 3A). This decoder should be not only sensitive to the ‘present’ or ‘absent’ decision made by a participant, but also the physical presence (or absence) of a grating. To maximise sensitivity in this analysis, only trials within the supra-threshold contrast level were used to define Hits. We then tested this decoder on empty sets vs. non-zero dot patterns and found a cluster of significant generalisation between 100ms and 300ms, with the peak BF indicating evidence for shared neural signatures across the two tasks (peak log10(BF) = 3.25; time averaged log10(BF) [0.05s, 0.3s] = -0.82; Figure 3B, left). When decoding in the alternative direction (training on empty sets vs. non-zero dot patterns and testing on Hits vs. Correct Rejections), we observed similar patterns of generalisation, with evidence in favour of shared neural signatures between the two stimulus sets (peak log10(BF) = 4.45; time averaged log10(BF) [0.05s, 0.3s] = 0.82; Figure 4B, right). Taken together, this result suggests that visual features may spuriously drive cross-decoding of absence in perceptual and non-symbolic numerical domains, unless stimulus contrast is appropriately controlled for. Indeed, when such properties are controlled for, generalisation across detection and non-symbolic tasks is almost entirely abolished (Figure 2). It is therefore all the more striking that, despite the potential for uncontrolled stimulus driven contributions to cross-decoding, we find strong evidence against shared neural representations of perceptual and numerical absence (Figure 3B).”

      Reviewer #2 (Public review):

      The authors tackle the question of whether conceptual absence is neurally encoded in the same way as perceptual absence. On one hand, the neural bases of perceptual absence have been largely investigated, as exemplified by the study of neural correlates of perception of aware vs. unaware stimuli, and on the other hand, the overlapping neural encoding of symbolic ('0') and non-symbolic (number of dots) formats of numerical absence has been previously established (Barnett & Fleming, 2024). However, the direct comparison of neural representations between numerical and perceptual absences remained to be investigated.

      This article fills this gap by designing a Magneto-EncephaloGraphy (MEG) study using multi-voxel pattern analysis (MVPA) and temporal generalization to probe the similarity of neural patterns across the representation of perceptual absence (lack of stimuli), symbolic ('0'), and non-symbolic (number of dots) formats of numerical absence. They confirmed previously obtained evidence for shared neural representation across both formats of numerical absence. They report evidence for an absence of shared representation between both formats of numerical absence on one hand and perceptual absence on the other hand, while controlling for the confounding effect of low-level visual features. Their results overall support the conclusion that conceptual and perceptual absence are neurally encoded in a distinct way and speak in favour of a boundary between the representation of the concepts and the percept of absence.

      Major strengths:

      (1) Behavioral and neuroimaging results convincingly demonstrate that neural encoding of symbolic and non-symbolic absences is shared and situated on a graded, abstract neural number line, replicating previous results, notably from the authors themselves (Barnett & Fleming, 2024).

      (2) They show that neural encoding of perceptual and numerical absence do not generalise across each other, while controlling for spurious confounds due to visual stimuli that are commonly shared in the cases of non-symbolic numerical absence and perceptual absences.

      (3) They adequately use Bayesian analysis to distinguish absence of evidence vs. evidence of absence to support their claim.

      (4) The interpretation of numerical absence as a representation of the concept of "nothingness" is adequate, although it might be further discussed by distinguishing the concept of "zero" on a number line from the concept of nothingness and that of an empty set (Nieder, 2016).

      (5) The discussion about development and metacognition paves an interesting road for further investigation on the acquisition of the concept of zero, especially in light of debates on the progressive development of metacognitive abilities in children (Goupil & Kouider, 2019).

      (6) Data and code are published with open-source access, allowing the community to further investigate the points as major weaknesses evoked below, if desired.

      We thank the reviewer for their careful reading of our manuscript and this positive appraisal of features of our work. Below we provide point-by-point responses to the reviewer’s comments and suggestions.

      Major weaknesses:

      R2C1: Interestingly, restricting the neural decoding method to the alpha band shows distinct representations across formats of numerical absence. This begs for providing more details on how neural representations of perceptual, symbolic, and non-symbolic absences differ at the source and frequency level and to report the decoding weights to better assess what drives the performance of the neural decoding algorithm in each case and whether they overlap with each other.

      We thank the reviewer for encouraging us to explore this question. We conducted new analyses to source-localise the decoder weights for the three different decoders (Perceptual Misses vs. Perceptual Hits; Empty Sets vs. Dot Stimuli; Symbolic Zero vs. Positive Numerals). Since the decoder used was a binary LDA, the appropriate transformation of classification weights for localisation purposes simplifies to a subtraction of mean activity in one class from that of the other class (Haufe et al., 2014; NeuroImage). As such, we computed the difference in mean source-level activity between each of the two classes per decoder. We have added Supplemental Figure 4 to the Supplemental Figures to highlight the brain regions the classifier relied upon to decode representations of absence.

      P.31:

      “Both FieldTrip’s template single shell head model and its standard volumetric grid (8mm resolution) were warped to participants’ individual fiducial points, generating a subject-specific forward model aligned in MNI space. Source reconstruction was performed using a linearly constrained minimum variance (lcmv) beamformer which applies spatial filters to the MEG data to generate source-level time courses. To reduce the impact of noise on the source estimates, we used a regularization parameter of lambda = 5%. For each task, spatial filters were calculated by combining the leadfield matrix with the data covariance matrix across all stimuli and the timepoints 100 – 450ms. These spatial filters were then applied to absence trials and presence/non-zero trials separately, generating reconstructed maps of source activity for different trial types. The maps can then be contrasted to reveal the source-level decoding weights associated with binary LDA decoding (Haufe et al., 2014; Supplemental Figure 4).”

      R2C2: Task-demands between perceptual (present vs absent) and numerical (lower vs higher) are different, raising concerns about whether these aspects of experimental design could drive, at least partially, the shared representational patterns across numerical representation of absence and their distinction from perceptual representation of absence.

      We agree with the reviewer that our motivation for this design should be clearer in the manuscript. As we explained in response to R1C1, we deliberately chose to employ distinct perceptual and numerical tasks because we wanted to create a strict test of whether absence representations generalise. Having two closely-matched tasks would have led to a converse difficulty in interpreting any successful cross-decoding because it would have been difficult to ascertain whether generalisation occurred because of a true domain-general representation of absence, or whether it was driven by other features of task design and stimulus-response contingencies.

      We appreciate though that our null findings require us to ensure that this design choice has not resulted in a type 2 error. We think this is unlikely for several reasons: first, we focus on stimulus-triggered responses, and within each task, we are able to robustly decode stimulus-triggered absence; second, in our previous work we obtained robust generalisation of absence representations even when tasks are distinct, a finding we now replicate here with more closely matched tasks; and finally, our control analyses of colour do show positive generalisation across task format.

      As we noted in response to R1C1, to make the motivation behind this design choice clearer to the reader, we have modified the following passage (p. 6):

      “Importantly, we used numerical and perceptual tasks that differed with respect to their structure and temporal dynamics. This ensured that any successful cross-decoding of absence could not be attributed to low-level or structural similarities between tasks, and instead would indicate a domain-general representation of absence. This approach builds on our previous work in which we identified a shared representation of numerical absence across non-symbolic and symbolic stimuli that generalised across task formats (Barnett & Fleming, 2024).”

      However, the reviewer is correct that this approach does not allow us to test whether unmeasured variables (such as cognitive load, decision making, etc) could interfere with cross-decoding, thus eliciting false negatives in our analyses. To elaborate on this limitation, and to suggest possible extensions to this work that could begin to help resolve this issue, we have added the following passage to the discussion (p. 19):

      “The tasks we employed in this study were dissimilar by design. This offered a strict test of the hypothesis that absences share representational currency across perceptual and numerical domains, because successful cross-decoding could not be artificially inflated by low-level task similarities across domains (Barnett & Fleming, 2024). However, this approach also carries the risk that task dissimilarity reduced our sensitivity to shared representations of absence. We think this is unlikely for several reasons: first, we focus on stimulus-triggered responses, and within each task, we are able to robustly decode stimulus-triggered absence representations; second, in our previous work we obtained robust generalisation of absence representations even when tasks are distinct, a finding we now replicate here with more closely matched tasks (Barnett & Fleming, 2024); and finally, our control analyses of colour do indicate positive generalisation across task format. Future work could explore the relationship between absences across domains using factorial designs that vary both domain and task independently, thus exposing possible interactions between absence representations and task context.”

      R2C3: The same argument can also be raised for the way that the neural decoders of perceptual and numerical absences are trained and tested. Both formats of numerical absence are built using the same procedure (zero vs. rest) and differ from the way the decoder is built for perceptual absence (hits vs misses), which might possibly drive the difference observed here.

      We are confident that the neural decoders for perceptual and numerical absence are near-identical and highly unlikely to drive the lack of cross-decoding. The essential features of the neural data fed into the decoders are matched across tasks. These two classification schemes – [zero vs. rest] and [hits vs. misses] – are both balanced with respect to the classes of interest. There are an equal number of ‘non-zero’ trials in the [zero vs. rest] decoder, and an equal number of each of the non-zero numbers within the set of non-zero trials. Similarly, the [hits vs. misses] decoder is balanced between hits and misses, and is balanced within each stimulus intensity level. Thus, both decoders are trained and tested on similarly balanced and matched stimulus sets. We note also that the cross-validation scheme used to train the decoders was identical across the two classification schemes. The primary difference between the two decoding schemes is the type of absence that they are seeking to decode.

      R2C4: It is thus unknown whether the claim supporting the evidence of absence holds as long as other counterfactual hypotheses that might drive these results are not excluded, such as the nature of the decoded features, the effect of task demands, or the way the neural decoder is trained, as mentioned above.

      We fully agree with the reviewer that it is important to mention and discuss the different features that may have contributed to our failure to cross-decode absence representations. We hope that by responding to R2C2 and R2C3 above, we have satisfied the reviewer’s concerns regarding these alternative explanations.

      Overall, I was pleased by the quality of the methods and the clarity with which the question of the boundary between cognition and perception is addressed for the case of numerous and perceptual absence. While the methods used are well established in the field, the choice and rigor of their analysis and the controls provided stand as a convincing methodology to test their hypotheses, although they do not fully exclude alternative interpretations nor explore the wider extent of possibilities that may provide exhaustive evidence for showing that perceptual and numerical absences are distinctly encoded in the brain.

      This work will be of great appeal to neuroscientists interested in comparing the representation of percepts and concepts across different formats, to psychologists interested in the origin of number representation, and to philosophers interested in debates on the boundary between cognition and perception.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      (1) In your previous work (Barnett & Fleming, 2024), you reported a curved representation of both symbolic and non-symbolic numerical representations in MDS space. Similarly, Karami et al. (2025) observed a curved representational geometry in both parietal fMRI activity and later MEG representations. Through simulations, they argued that a curved MDS geometry is consistent with numerosity-tuned population codes, whereas a more linear organization is expected from summation-code representations. Given these converging observations, I wonder whether you can examine the geometry of the representational space and whether it evolves over time from a more linear to a more curved organization. It could provide additional insight into the underlying coding scheme. Even if no such transition is observed, reporting the MDS geometry would strengthen the manuscript by helping readers relate the present findings to previous work and by providing a richer characterization of the neural representations beyond decoding accuracy alone.

      We agree that the coding scheme and representational space for numerosities is an interesting question. As the reviewer points out, these analyses were a focus of our previous Current Biology paper, and we now explore similar plots in the current data.

      P. 9:

      “Multidimensional scaling of sensor-level data similarly revealed numerosities to be arranged along a single dimension encoding numerical magnitude that is shared between both numerical formats (Supplementary Figure 2). These analyses confirm a graded representation of numerical absence that is evoked by both non-symbolic empty sets and symbolic zero (Barnett & Fleming, 2024), and establish that we are able to robustly recover neural representations of numerical absence in our paradigm using MEG.”

      (2) In Results, clarify whether RTs (figure 1E) are 0.32 s for absent and 0.28 s for present (lines 144-146) - it currently reads "0.28 ms" which must be a typo (should be s).

      We have fixed the typo in lines 144-146:

      “Replicating previous findings, participants took longer to report stimulus absence (mean RT = 0.32s, SD = 0.14s) compared to stimulus presence (mean RT = 0.28s, SD = 0.11s, t(28) = -3.0176, p = .0054, Figure 1E).”

      (3) When describing Bayes factors, the text could define what "time averaged log10(BF)" means in simpler terms, to help readers interpret Figure 2B.

      We thank the reviewer for this suggestion. To make this clear to the reader, the manuscript now states (p. 11):

      “To allow us to obtain evidence for or against shared representations of numerical and perceptual absence, we computed Bayes factors (BF) – with positive BFs indicating evidence in favour of generalised representations, and negative BFs indicating evidence in favour of distinct neural representations. To assist in visualisation, we plot log10 transformation of BFs such that BFs supporting either distinct or generalised representations are symmetric around zero. Interpretation of log10 BFs follows standard convention for interpreting BFs, with log10(BF) in the range [0, ±0.5] offering weak evidence, [±0.5, ±1] moderate evidence, [±1, ±1.5] strong evidence, [±1, ±2] very strong evidence, and [±2, ±inf] being decisive (Jeffreys, 1998). To report log10 BFs in the text, we average BFs over the 0.2s – 0.8s time window shown in Figure 2C to report a time-averaged log10 BF. In our plots, we indicate the timepoints when evidence for either hypothesis exceeds the threshold for strong evidence.”

      Reviewer #2 (Recommendations for the authors):

      I enjoyed how clear the question of the boundary between cognition and perception was formulated and how the use of temporal generalisability elegantly provides a convincing way to test it.

      To address the first major weakness, I would like to suggest providing the decoding features, and how they relate to the neural correlates of absence to strengthen the claim and reassure both reviewers and readers that the MVPA analysis does not pick up on other neural features than those previously established in relation to the neural encoding of absence in each of those formats.

      We have now added a supplementary figure displaying the decoding weights in source space in response to the reviewer’s comment R2C1.

      Although Figure 2C (top) provides a nice argument in favour of the MVPA actually picking up information related to numerosity, it might also be theoretically explained by the task demands of identifying which number is higher. Although I am aware that the decoder was trained on absence vs rest, the dimension tested (distance from zero) might be confounded with the task to compare which number is higher, while an orthogonal task to numerosity would exclude such potential confound of a task effect on the way zero is represented in the brain. The contextual effect of the task on the neural encoding of numerical absence is perhaps far-fetched, but it seemed to me to be a reasonable concern.

      We agree that similarities in task design between the two numerical tasks may contribute to the generalisation of across format observed in our decoding analysis. Indeed, this is precisely why we designed a perceptual (detection) task that shared minimal structure with the numerical tasks, to ensure that task demands would not confound interpretation of findings of absence generalisation (see also our responses to reviewers R2C2 and R1C1). Similarly, in our previous paper in Current Biology (2024) we employed tasks with distinct formats, and found similar results. We therefore think that it’s unlikely that the similarity in task format here is the primary driver of cross-format generalisation, but we cannot rule it out. We believe that our answer to R2C2 addresses this concern and makes the reasoning behind our design choice explicit to the reader.

      I became aware, including in my own experiments, that the choice of parameters might be crucial in interpretations of decoding when it comes to neuroimaging results. One of the strengths of MVPA is to be data-driven, reducing the potential selection bias, but it also raises other concerns due to the poor controllability of the relevant features this technique grasps depending on the task and experimental set-up. This begs the question whether the results here obtained are generalisable, taking into account other potential confounds and at least acknowledging such potential limitations in the discussion.

      We thank the reviewer for this comment, and agree that chosen parameters can sometimes influence neuroimaging decoding results. To better justify why we chose the parameters we did, we have added the following sentence to the Methods (p. 29):

      “All decoding hyperparameters were chosen to match those of our previous work on numerical absence decoding (Barnett & Fleming, 2024), such that results would be directly comparable across the two studies.”

      My overall uptake is that the authors make an inference to the best explanation by having designed the most convincing analysis possible to provide a crucial test on the distinction between the neural representation of perceptual and conceptual absence. They rightly exclude the false positive case of low-visual features driving the similarity between perceptual and non-symbolic representation. However, providing the evidence of absence also needs to address possible cases of false negatives that might be a result of their experimental and analytical choices.

      Even if proving the evidence of absence for this reason is inherently difficult, if not almost impossible to achieve, it seems reasonable that further insights such as for example comparing the neural correlates of absence as done by the authors in their Current Biology paper based on empirical findings and the possible limitations of their approach might be addressed at least in the discussion to frame their conclusion in regard to the context of their experiment and analysis. This would enrich the paper by providing better hindsight about the origin and the evidence at hand on what might drive the reported distinction in the neural representation of perceptual vs. numerical absence.

      We thank the reviewer for their careful reading of our paper, which prompted further considerations of the limitations of different design choices. We have now included new sections of the discussion to ensure these are appropriately highlighted to the reader.

      I would like to thank the authors and editors for this opportunity of reviewing this stimulating paper, enriching our perspective on the important debate on the boundary of perception and cognition.

      Matthieu Koroma

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      This study integrates Xenium spatial transcriptomics of paired inflamed and uninvolved Crohn's disease tissues with functional analyses in a csf2rb-/- larval zebrafish DSS intestinal injury model to investigate the spatial and cell-type-specific roles of GM-CSF. The work is limited mechanistically and adds little to an already disputed field: GM-CSF's role in intestinal inflammation is context-dependent and extensively studied in mice and humans, and this study does not resolve these controversies. The zebrafish appears to be a poor model for these questions: it lacks mammalian intestinal architecture, complex microbiota, and clearly validated functional ILC populations. Putative ILC1s are poorly defined based on stress-response gene modules, while ILC3s are somewhat better characterized, but overall, the system does not allow mechanistic insights into GM-CSF regulation of ILCs. The DSS experiments largely recapitulate the known protective effects of GM-CSF in epithelial injury without clarifying underlying mechanisms.

      Figure 1

      GM-CSF expression is extremely sparse, rarely exceeding 0.005 frequency even in inflamed regions. The authors should acknowledge this and discuss why. Xenium could be used to characterize the niche around GM-CSF-producing cells, but no new cellular circuit is revealed beyond known myeloid-lymphoid interactions.

      We thank the reviewer for this important observation. We agree that GM-CSF-expressing cells represent a very small fraction of all cells within the tissue, even in inflamed regions. We have now explicitly acknowledged this in both the Results (Line 300-304) and Discussion (Line 539-547). The low abundance of GM-CSF-producing cells is consistent with previous studies demonstrating that GM-CSF is not constitutively expressed in the intestinal mucosa but is induced only in activated immune cells during inflammation. Moreover, GM-CSF functions primarily as a locally acting cytokine with paracrine activity rather than as a broadly expressed tissue factor. Consequently, even a small number of GM-CSF-producing lymphocytes can establish localized signaling niches that activate neighboring CSF2RA/CSF2RB-expressing myeloid cells. This localized mode of signaling is also consistent with the low circulating concentrations of GM-CSF reported in both healthy individuals and patients with inflammatory diseases. We have revised the manuscript to better emphasize that the biological significance of GM-CSF lies in its spatially restricted expression and signaling rather than its overall abundance.

      Figure 2

      Colon length in DSS colitis is not decreased in Csf2rb-/- versus wild-type zebrafish under untreated conditions, suggesting endogenous GM-CSF has minimal impact. In Figure 2E, Tg(mpeg1:mCherry) larvae show staining in vessel- or epithelial-like structures expressing Csf2rb, which does not resemble macrophages and requires clarification. pSTAT5 is upregulated with GM-CSF treatment, but the responding cell types are unclear.

      We thank the reviewer for this observation. We agree that intestinal length is comparable between wild-type and csf2rb<sup>-/-</sup> larvae under homeostatic conditions. This finding is consistent with the established biology of GM-CSF, which is largely dispensable during steady-state tissue homeostasis but becomes functionally important during inflammatory challenge. Accordingly, the protective effect of GM-CSF became apparent only following DSS-induced intestinal injury, where recombinant human GM-CSF significantly rescued epithelial damage and gut shortening in wild-type but not csf2rb<sup>-/-</sup> larvae. We have clarified this point in the Discussion (Line 563-571).

      As for 2E comments, we apologize that the previous version of Figure 2 inadvertently omitted the panel labels and annotations for Figure 2E, making it difficult to interpret the image. We have corrected this oversight by restoring the panel label, adding arrows and higher-magnification insets that highlight representative csf2rb+ mpeg1:mCherry+ macrophages in the retina, intestine, and midbody. The purpose of this experiment was to demonstrate that intestinal macrophages express csf2rb, rather than to suggest that csf2rb expression is restricted to macrophages. We agree that additional csf2rb-positive elongated structures are present that do not colocalize with mpeg1:mCherry. This observation is consistent with our human Xenium data, which show that CSF2RB is broadly expressed across multiple cell types, whereas signaling specificity is determined by the more restricted expression of CSF2RA. We have revised both the Results (Line 358-365) and the figure legend (Line 694-699) to clarify this point and avoid implying macrophage-exclusive expression.

      Figure 3

      Putative ILC1s are defined by stress-response gene modules rather than canonical markers. Overlapping genes with human (HSP90AA1, UBB, MCL1, DOK2) do not indicate ILC1 identity, which is described by IL7R, KLRB1, or TBX21 expression in the human Xenium dataset. ILC2s were not detected, and Ifng expression is broadly distributed, making attribution to ILC1s uncertain. ILC3s are somewhat better defined, but overall, the data do not support mechanistic conclusions about GM-CSF regulation of ILC populations.

      We thank the reviewer for this thoughtful comment and agree that annotation of innate lymphoid cell populations in zebrafish remains more challenging than in mammals due to the limited availability of validated lineage-specific markers. We have therefore revised the manuscript to more clearly describe these populations as putative ILC1- and ILC3-like cells identified using the currently available zebrafish ILC markers together with conserved transcriptional programs, rather than implying complete equivalence to mammalian ILC subsets.

      Our annotation was not based solely on stress-response genes or IFNG expression. Instead, we first identified the lymphocyte population using established zebrafish ILC markers (il7r, nitr4a, nitr5, nitr9, and ccl20a.3) reported by Hernández et al. (2018), followed by subtype annotation using multiple complementary features. The putative ILC3 cluster expressed canonical regulators of ILC3 identity, including rorc, il23r, tcf7, and mafb, while the putative ILC1 cluster demonstrated enrichment of tbx21, an IFN-associated transcriptional program, and a conserved stress-response module that has likewise been reported in human intestinal ILC1 datasets. IFNG expression was therefore interpreted together with the overall transcriptional program rather than used as a defining marker.

      We also agree that the zebrafish model does not currently permit identification of all mammalian ILC subsets. Accordingly, we have revised the Discussion to explicitly acknowledge this limitation and have moderated our conclusions throughout the manuscript (Line 381-388 and Line 588-593). Rather than concluding that GM-CSF directly regulates definitive mammalian ILC subsets, we conclude that GM-CSF regulates conserved ILC-like transcriptional states during intestinal inflammation (Title). Importantly, this interpretation is further supported by independent RNAscope validation of tbx21, rorc, ifng1.1, and il22, together with the concordant expansion of IL7R+KLRB1+TBX21+ cells and contraction of IL7R+KLRB1+RORC+ cells observed in the human Xenium dataset.

      Reviewer #2 (Public review):

      The authors show that GM-CSF prevents the loss of ILC3 populations and inhibits pro-inflammatory cytokine production during gut inflammation. They combine a preclinical model of gut inflammation in zebrafish with spatial transcriptomic analysis of samples from Crohn's disease patients. The data show that GM-CSF ameliorates gut inflammation by (1) curtailing the differentiation of disease-associated ILC1 and (2) by "boosting" the tissue repair function of ILC3.

      The topic of the manuscript is interesting. However, there are various limitations that are summarized below.

      We thank the reviewer for these thoughtful comments. We agree that, because GM-CSF receptors are predominantly expressed by myeloid cells rather than ILCs, understanding the myeloid response to GM-CSF is important for interpreting the mechanism by which GM-CSF preserves ILC3 function. In response to the reviewer's suggestions, we performed additional analyses of both our human scRNA dataset (Martin et. al., 2019, PMID: 31474370) and zebrafish macrophage transcriptomes. Together, these new analyses support a model in which GM-CSF acts primarily on macrophages to establish a tissue-repair and ILC3-supportive microenvironment, thereby indirectly maintaining ILC3 identity during intestinal inflammation.

      (1) The main finding of the manuscript, that GM-CSF maintains ILC3 populations, is not analyzed in depth. Since the authors' own data and other publications show that the receptors for GM-CSF are expressed in myeloid cells, a better analysis of the transcriptional changes of these populations upon GM-CSF administration is needed.

      To better characterize the cellular targets of GM-CSF, we performed differential expression analysis of macrophages and monocytes. In our previous human scRNA-seq dataset (Martin et al.), STAT5-high macrophages were enriched for canonical GM-CSF-responsive genes, including STAT5A, STAT5B, JUNB, and HIF1A, confirming activation of the GM-CSF/STAT5 signaling axis. These macrophages additionally expressed regulatory and tissue-remodeling genes including LGALS1 (Galectin-1), TGFBI, and GPNMB, consistent with an immunoregulatory macrophage phenotype. Notably, LGALS1 has been reported to suppress type 1 inflammatory responses and modulate innate lymphoid cell function, whereas TGFBI is associated with tissue remodeling and immune regulation.

      To further investigate the downstream effects of GM-CSF signaling, we analyzed macrophage transcriptomes from zebrafish treated with DSS plus GM-CSF. We observed enrichment of genes involved in retinoic acid and tissue-homeostatic signaling, including rarab, rdh12l, and vhl. Retinoic acid signaling is well established in promoting intestinal immune homeostasis and supporting ILC3 differentiation and maintenance, while HIF signaling has been implicated in intestinal barrier integrity and ILC3 survival. Additional changes in YBX1 and SLC7A7 further suggest modulation of cytokine translation and macrophage immunometabolism that could influence the intestinal immune niche. Consistent with this interpretation, expression of rarab and vhl was reduced in csf2rb-/- macrophages, indicating that activation of this tissue-homeostatic program depends on GM-CSF receptor signaling. Together, these findings support a model in which GM-CSF primarily acts on macrophages to induce a regulatory, tissue-supportive program that creates an environment favorable for maintenance of protective ILC3 responses while limiting excessive type 1 inflammation.

      (2) The authors could compare the transcriptome of macrophages and monocytes from inflamed and uninvolved sections in their Xenium dataset. In addition, investigating how zebrafish macrophages change due to the lack of GM-CSF and comparing them with the human findings would add to the data.

      We thank the reviewer for this valuable suggestion. While comparison of macrophages and monocytes between inflamed and uninvolved regions using the Xenium dataset is conceptually appealing, the Xenium platform is designed for spatially resolved targeted transcriptomics and is limited to a predefined panel of 468 genes. In addition, transcript detection from FFPE tissue is inherently sparser than whole-transcriptome single-cell RNA sequencing due to probe-based hybridization and RNA fragmentation. Consequently, Xenium provides excellent spatial resolution but is less suited for comprehensive transcriptional profiling of macrophage and monocyte states.

      To more comprehensively characterize myeloid transcriptional programs, we therefore analyzed our previously generated human scRNA-seq dataset from inflamed Crohn's disease intestine, which captures the full transcriptome at single-cell resolution. This analysis identified a STAT5-high macrophage population enriched for genes associated with GM-CSF signaling (STAT5A, STAT5B, JUNB), immune regulation (LGALS1, TGFBI, GPNMB), and tissue remodeling, providing a more complete characterization of macrophage responses than could be achieved with the targeted Xenium panel.

      In addition, as suggested by the reviewer, we investigated the consequences of impaired GM-CSF signaling in zebrafish by comparing macrophages from WT and csf2rb-/- animals following GM-CSF treatment. These analyses demonstrated that loss of csf2rb attenuated the induction of retinoic acid- and tissue-homeostatic programs, including rarab, rdh12l, and vhl, supporting an evolutionarily conserved role for GM-CSF signaling in establishing a macrophage program associated with intestinal homeostasis. Together, the human scRNA-seq and zebrafish datasets provide complementary evidence that GM-CSF primarily acts through macrophages to promote a regulatory, tissue-supportive phenotype. All these results have been summarized in Results (line 503-513) and Supplementary Figure 7.

      (3) Since the authors developed a novel mutation in zebrafish that is predicted to affect myeloid populations, a detailed characterization of the myeloid immune compartment in these organisms is missing.

      We thank the reviewer for this important suggestion. We agree that characterization of the myeloid compartment is essential for understanding the consequences of disrupting GM-CSF signaling. To address this, we performed additional transcriptional analyses of macrophages isolated from WT and csf2rb-/- zebrafish following GM-CSF treatment. These analyses revealed that loss of csf2rb markedly attenuated the GM-CSF-dependent macrophage program, including genes involved in retinoic acid signaling (rarab, rdh12l), HIF-associated tissue homeostasis (vhl), cytokine regulation (ybx1), and macrophage immunometabolism (slc7a7). In addition, genes associated with cytoskeletal remodeling, migration, and metabolic adaptation were also reduced in csf2rb-/- macrophages, indicating that GM-CSF receptor signaling is required for full macrophage activation.

      These findings demonstrate that the csf2rb mutation does not simply alter individual downstream genes but broadly impairs the establishment of a macrophage program associated with intestinal tissue homeostasis. Together with our human scRNA-seq analyses, these data support a conserved role for GM-CSF signaling in programming regulatory macrophage states that create an environment favorable for maintenance of protective ILC3 responses. We have incorporated these additional analyses into the revised manuscript to provide a more comprehensive characterization of the myeloid compartment.

      (4) Niche analysis in the Xenium slides could provide direct evidence on how macrophages close to ILC3 are different from those closer to other cell types, like ILC1.

      We thank the reviewer for this insightful suggestion. We agree that spatial niche analysis comparing macrophages associated with ILC3 versus ILC1 would provide valuable mechanistic insight into local immune cell interactions. However, this analysis is technically challenging in our Xenium dataset for several reasons. First, the Xenium platform uses a targeted panel of 468 genes and therefore provides substantially lower transcriptomic depth than whole-transcriptome scRNA-seq. Second, transcript detection in FFPE tissue is inherently sparse due to probe-based hybridization and RNA fragmentation. Finally, ILC populations are relatively rare within the intestinal tissue, limiting the number of macrophages located in close proximity to ILC3 or ILC1 and reducing the statistical power required for robust niche-specific differential expression analyses.

      To instead address the reviewer's mechanistic question, we integrated complementary datasets that are better suited for transcriptional profiling. Specifically, our human scRNA-seq analysis identified a STAT5-high macrophage population enriched for regulatory and tissue-remodeling genes, including LGALS1, TGFBI, and GPNMB, consistent with a macrophage phenotype capable of supporting intestinal homeostasis. Furthermore, zebrafish macrophage transcriptomic analyses demonstrated that GM-CSF signaling induces a conserved tissue-homeostatic program characterized by rarab, rdh12l, and vhl, implicating retinoic acid and HIF-associated pathways that have been linked to ILC3 maintenance and mucosal immunity. Together, these complementary datasets provide molecular evidence that GM-CSF programs macrophages toward an ILC3-supportive phenotype, although we acknowledge that direct spatial comparison of macrophages neighboring ILC3 versus ILC1 will require future studies using higher-complexity spatial transcriptomic approaches.

      Recommendations for the authors:

      Reviewer #2 (Recommendations for the authors):

      (1) Overall/Statistics: The statistical analysis described in the method section (Mann-Whitney-Wilcoxon Test) is not suitable for comparison of more than 2 populations.

      We thank the reviewer for identifying this oversight. We agree that the original description of the statistical analyses was incomplete, as the Mann–Whitney U (Wilcoxon rank-sum) test is appropriate only for comparisons between two groups. We have revised the Quantification and Statistical Analysis section to accurately describe the statistical methods used throughout the manuscript. Specifically, two-group comparisons were analyzed using the Mann–Whitney U (Wilcoxon rank-sum) test, whereas experiments involving more than two groups were analyzed using the Kruskal–Wallis test followed by Dunn's multiple-comparisons test. We have also clarified that differential gene expression analyses were performed using the Wilcoxon rank-sum test implemented in Seurat, and ligand–receptor analyses were performed using permutation testing with Benjamini–Hochberg false discovery rate correction. These revisions ensure that the statistical methods accurately reflect the analyses performed throughout the study.

      (2) Figure 1

      A. A zoomed-in image of the regions expressing GM-CSF and G-CSF could help to visualize the changes between uninvolved and inflamed sections.

      We thank the reviewer for this helpful suggestion. To better visualize the spatial distribution of the CSF cytokines, we have added representative high-magnification Xenium images of paired uninvolved and inflamed ileal tissue to Supplementary Figure 2C. These enlarged views more clearly demonstrate the focal enrichment of GM-CSF (CSF2) within inflamed tissue, whereas CSF1 remains broadly distributed and CSF3 exhibits comparatively sparse expression with minimal changes between uninvolved and inflamed regions. We have also added a reference to this new supplementary panel in the Results section (line 317-320).

      F. Since the expression of the CSF receptors is detectable, it would be interesting to see an analysis of their spatial location.

      We thank the reviewer for this valuable suggestion. We agree that spatial visualization of the CSF receptors provides important context for interpreting ligand–receptor interactions. Accordingly, we have expanded Supplementary Figure 2C to include representative Xenium images showing the spatial localization of CSF1R, CSF2RA, and CSF2RB in paired uninvolved and inflamed ileal tissue sections. These images complement our human scRNA-seq analysis by demonstrating the tissue distribution of the receptors within the intestinal microenvironment. Together with the ligand–receptor interaction analysis, these data further support macrophages and dendritic cells as the principal cellular targets of GM-CSF signaling during intestinal inflammation.

      (3) Figure 2

      A. The experimental setup depicted in the figure does not match the description given in the text (323-324) or the methods (188-191). Importantly, the recovery phase is not detailed in the figure scheme, which complicates result interpretation.

      We thank the reviewer for identifying this inconsistency. We have revised Figure 2A to accurately reflect the experimental design described in both the Methods and Results sections. Specifically, the schematic now clearly distinguishes the two experimental paradigms: (i) co-treatment with DSS and GM-CSF during active intestinal injury, and (ii) the recovery protocol in which DSS was removed prior to GM-CSF treatment. We have also expanded the recovery phase in the schematic to indicate the timing of DSS removal, GM-CSF administration, and sample collection. These revisions provide a clearer representation of the experimental workflow and facilitate interpretation of the corresponding results.

      D. Statistical significance should be revised using ANOVA or a non-parametric test that can compare more than 2 groups.

      We thank the reviewer for this important comment. We agree that comparisons involving more than two groups require an appropriate omnibus statistical test. Accordingly, we have reanalyzed the data using the Kruskal–Wallis test, followed by Dunn's multiple-comparisons test for post hoc pairwise comparisons. The revised statistical analyses have been incorporated into Figure 2D and throughout the manuscript where applicable. In addition, the Quantification and Statistical Analysis section (line 274-284) has been updated to accurately describe the statistical methods used. These revisions do not alter the interpretation or conclusions of the study.

      (4) Figure 3

      C. It is unclear which data were used to generate the dot plot. The data source should be written in the text or the figure panel.

      We thank the reviewer for pointing out this lack of clarity. We have revised the Results section (line 382-385) and Figure 3 legend (line 706) to explicitly state that the dot plot in Figure 3C was generated from the scRNA-seq dataset of FACS-isolated intestinal lck: GFP+ lymphocytes from larval zebrafish. The dot plot shows the expression of established zebrafish ILC markers and conserved ILC-associated genes across the identified lymphocyte clusters and was used, together with additional transcriptional features, to support annotation of the proliferative ILC, putative ILC1-like, and putative ILC3-like populations.

      D. While the heatmap is informative to identify signature genes, it fails to highlight the differentially expressed genes between experimental conditions. The authors should present the DEG for each of the ILC clusters. Doing a pathway enrichment analysis could highlight how ILCs are responding to DSS and GM-CSF treatments. In addition, it would be important to test experimentally how the immune compartment (ILC and myeloid populations) is affected by CSF2RB deficiency.

      We thank the reviewer for these valuable suggestions. We agree that differential expression analyses provide additional insight into how GM-CSF modulates immune cell states during intestinal inflammation. To address this, we have expanded our analyses in the revised manuscript.

      First, we performed differential gene expression analyses of macrophages and incorporated these data into the revised manuscript. Comparative analyses of human STAT5-high macrophages and zebrafish GM-CSF-responsive macrophages identified conserved transcriptional programs associated with regulatory macrophage function, tissue remodeling, and establishment of an ILC3-supportive niche. Furthermore, comparison of WT and csf2rb-/- zebrafish macrophages demonstrated that disruption of GM-CSF receptor signaling attenuates these macrophage programs, providing a molecular characterization of the myeloid compartment in the mutant animals.

      Second, pathway enrichment analyses of ILC1 and ILC3 marker genes were already included in the original manuscript (Figure 3F) using Ingenuity Pathway Analysis (IPA), demonstrating conserved transcriptional regulators and signaling pathways between zebrafish and human ILC populations. Rather than performing pathway analysis across treatment conditions, our study focused on identifying conserved lineage-defining programs and experimentally validating the functional consequences of GM-CSF signaling through changes in ILC abundance, lineage marker expression, RNA velocity, and effector cytokine production.

      Finally, to directly address the reviewer's concern regarding the impact of csf2rb deficiency on the immune compartment, we have added additional analyses characterizing macrophage transcriptional responses in WT and csf2rb-/- zebrafish following GM-CSF treatment. Together with our existing analyses of ILC population dynamics and lineage-specific marker expression in WT and csf2rb-/- animals, these data provide a more comprehensive characterization of how loss of GM-CSF signaling alters both the myeloid and ILC compartments during intestinal inflammation.

      (5) Figure 4

      D. The genes used to define the "ILC1 gene module" are not detailed. Importantly, maintaining the scale of the violin plots would allow a better interpretation of the results.

      We thank the reviewer for pointing out this lack of detail. We have revised the Figure 4 legend (line 724-727) to explicitly describe the genes included in the putative ILC1-like gene module. This module was derived from differentially expressed genes enriched in the zebrafish putative ILC1-like cluster identified in our scRNA-seq dataset, rather than from IFNG expression alone. The module includes genes associated with the ILC1-like transcriptional state identified in our dataset (Figure 3E). As discussed above, because several of these genes represent a conserved stress-response program rather than canonical lineage-defining ILC1 markers, we have revised the terminology throughout the manuscript from “ILC1 gene module” to “putative ILC1-like gene module” and have moderated our interpretation accordingly.

      F-H. The naming of RNA signal is not consistent: Il22 particles vs. Ifng1-1 foci.

      We thank the reviewer for noting this inconsistency. We have revised the terminology throughout the manuscript and figure legends to use consistent nomenclature when referring to RNAscope signals. Specifically, all RNAscope transcript signals are now described uniformly as RNA foci.

      (6) Figure 5

      C. It is unclear if the color code and the y-axis are 2 different measurements or just 2 ways of showing the same. A similar calculation on the ILC3 and ILC1 subsets could give insights into their differentiation potential.

      We thank the reviewer for pointing out this lack of clarity. The color coding and y-axis provide complementary representations of the RNA velocity analysis. The y-axis quantitatively represents the proportion of unspliced relative to spliced transcripts, whereas the color scale was included to facilitate visualization of the relative transcriptional/differentiation state of individual cells. We have revised the figure legend (line 739) to clearly distinguish these two representations and retained the color scale because it provides an intuitive visualization of changes in cellular transcriptional state.

      D. The authors do not describe how the 'Relative ILC Ratio' was calculated.

      We thank the reviewer for pointing out this omission. We have revised the Methods (line 148-153) and the corresponding figure legend to clarify how the relative ILC ratio was calculated. Briefly, we first calculated the densities (cells/μm²) of ILC1s (IL7R<sup>+</sup>TBX21<sup>+</sup>) and ILC3s (IL7R<sup>+</sup>RORC<sup>+</sup>) from the Xenium dataset. The relative ILC ratio was then determined by calculating the proportion of each ILC subset relative to the total IL7R<sup>+</sup> ILC population identified in each sample following single-cell clustering and cell-type annotation. Finally, these proportions were normalized to the control condition to enable comparison across treatment groups.

      (7) Figure 6

      B. The colors used obscure CD14 expression. Changing the background intensity (as done later in 5G) could fix this problem.

      We thank the reviewer for pointing out this potential source of confusion. In Figure 6B, the green cells represent epithelial cells and are therefore not part of the ulcer exudate/macrophage aggregates being highlighted in this analysis. The macrophage-rich ulcer exudate is identified by the accumulation of CD14-positive cells adjacent to the disrupted epithelial compartment. We have revised the figure legend (line 746-749) to more clearly define the color coding and distinguish the epithelial compartment from the CD14-positive macrophage aggregates.

      C. Since the Xenium slides group were selected by inflammation status, is it expected to have any ulcer in an 'Uninvolved' tissue section?

      We thank the reviewer for raising this important point. The classification of Xenium sections as inflamed or uninvolved was determined by pathological evaluation of the resection specimens, and the inflammation status of the analyzed regions was confirmed by a pathologist. Importantly, this classification is distinct from the morphological criteria used to identify ulceration. Histologically, an ulcer is defined primarily by disruption or loss of the epithelial barrier rather than by the presence of inflammatory immune-cell infiltration. Therefore, focal epithelial breaks can occasionally be identified even within tissue sections classified as uninvolved, without the prominent inflammatory infiltrates characteristic of ulcerated regions in inflamed tissue. This distinction explains the small number of epithelial disruptions identified in the uninvolved sections. We have revised the Results (line 473-480) and figure legend (line 750-751) to clarify the distinction between pathologist-defined inflammation status and the morphological identification of ulcerated/epithelial-disrupted regions.

      E. The macrophage density measurement contradicts the previous panel (6E), which shows no macrophage infiltration in uninvolved ulcers. The authors should clarify how both analyses differ.

      We thank the reviewer for pointing out this potential confusion. The two analyses quantify different aspects of macrophage distribution and therefore are not directly comparable. Figure 6D quantifies the number of pro-inflammatory macrophage aggregates associated with ulcer exudate, which are present only in inflamed tissue and absent from uninvolved sections because uninvolved tissues do not contain ulcers. In contrast, Figure 6E measures the overall density of CD14<sup>+</sup> macrophages within the defined tissue compartments, independent of whether the macrophages form inflammatory aggregates. Thus, Figure 6D evaluates the presence of organized inflammatory macrophage clusters, whereas Figure 6E quantifies the abundance of macrophages throughout the analyzed tissue regions. We have revised the figure legend (line 748-753) to clearly distinguish these complementary analyses and avoid confusion.

      In addition to cytokine (6G) localization and signaling (6J-K) colocalization, analysis of ILC-Macrophage colocalization in the Xenium slides or by immunofluorescence could highlight the point that macrophages and ILC interactions change based on disease activity.

      We thank the reviewer for this thoughtful suggestion. We agree that direct visualization of ILC–macrophage interactions would further strengthen the mechanistic framework of the study. However, because ILCs are relatively rare within the Xenium dataset and the targeted 468-gene panel provides limited transcriptomic depth, robust quantitative colocalization analyses between ILC subsets and neighboring macrophages were not feasible. Instead, we combined complementary approaches to address this question. Xenium spatial transcriptomics established the localization of GM-CSF signaling within macrophage-rich inflammatory niches, while our human scRNA-seq and zebrafish macrophage transcriptomic analyses demonstrated that GM-CSF induces conserved regulatory and tissue-homeostatic macrophage programs associated with maintenance of protective ILC3 responses. We have expanded the Result (line 503-513) and Discussion (line 575-581) to acknowledge that future studies employing higher-complexity spatial transcriptomic or multiplex imaging approaches will be valuable for directly defining macrophage–ILC niche interactions during intestinal inflammation.

      (8) Figure 7

      The graphical abstract does not clearly depict the interactions that occur in homeostasis. ILCs and the GM-CSF signaling are lacking. It is also unclear if the left part (Crohn's disease inflammation) depicts the inflamed situation or the consequences of GM-CSF addition in the inflammatory environment. It is also unclear that GM-CSF is acting on macrophages (and other myeloid subsets) and that the ILC3 maintenance and inhibition of ILC1 proliferation are indirect consequences.

      We thank the reviewer for this thoughtful suggestion. We agree that the original graphical summary did not sufficiently distinguish the homeostatic and inflammatory states or clearly illustrate the mechanism by which GM-CSF regulates intestinal immunity. We have therefore revised Figure 7 to better depict the proposed model.

      Specifically, the revised schematic now illustrates: (i) the homeostatic state, in which ILC3-derived GM-CSF supports resident macrophage homeostasis through CSF2RA/CSF2RB signaling; (ii) the inflammatory state in Crohn's disease, characterized by expansion of ILC1s, contraction of ILC3s, and increased pro-inflammatory cytokine production; and (iii) the protective effects of GM-CSF during inflammation. Importantly, we now explicitly indicate that GM-CSF acts primarily on macrophages and other CSF2RA/CSF2RB-expressing myeloid cells, rather than directly on ILCs. The revised model illustrates that maintenance of ILC3s, suppression of disease-associated ILC1 expansion, and enhanced IL-22 production are indirect consequences of GM-CSF-mediated macrophage reprogramming toward a regulatory, tissue-supportive phenotype. These revisions more accurately reflect the mechanistic conclusions supported by our human spatial transcriptomic, human scRNA-seq, and zebrafish studies.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      In this manuscript, the authors aimed to clarify the transcriptional changes across murine postnatal small intestinal development (0 days to 1 month) in both the duodenum and ileum, a period that shows morphological similarity to 20-30 week old fetal humans. This is an especially critical stage in human intestinal development, as necrotizing enterocolitis (NEC) usually manifests during these stages.

      Strengths:

      The authors assessed numerous timepoints between 0 days and 1 month in the postnatal mouse duodenum and ileum using bulk RNA transcriptomics of bulk-isolated tissues. Cellular deconvolution, based on relative marker expression, was used to clarify immune cell proportions in the bulk RNA sequencing data. They confirmed some transcriptional targets found in vivo primarily in mouse via qrtPCR and immunohistochemistry, but also in human fetal tissues and isolated organoids, and are of decent quality.

      Weaknesses:

      The overall weakness of this study, as mentioned by the authors themselves, is that the bulk transcriptomic data generated for the study were isolated from non-fractionated bulk intestinal tissue. This makes it difficult to interpret much of this data regarding cellular fractions found across developmental time. It is difficult to rationalize the approach here, as even isolation protocols of epithelial-only or mesenchyme-only tissues for bulk RNA sequencing are well established. The authors address some of these concerns using cellular deconvolution for immune cell populations, which I think might be helpful if they expanded this analysis to other cell types (mesenchyme, endothelium, glia). However, I would assume that bulk isolations across developmental time are going to be influenced primarily by the bulk of tissue-type found at each time point - primarily epithelium. But this is also confirmed by the immune transcripts becoming more apparent later in their time series, as this system becomes more established during weaning. This study might also be strengthened by comparison with data that is publicly available for early fetal stage development in humans. Comparisons between the duodenum and ileum could be strengthened by what we already know from adult data, from both epithelial- and mesenchyme-isolated fractions. The rationale of using the postnatal mouse as a comparison to NEC is also a little unclear- perhaps some of the developmental processes are similar, however, the environments are completely different. For example, even in early postnatal mouse development, you would find microbial activity and milk.

      Reviewer #2 (Public review):

      Summary:

      This work presents a valuable resource by generating a comprehensive bulk RNA sequencing catalogue of gene expression in the mouse duodenum and ileum during the first postnatal month. The central findings of this work are based on an analysis of this dataset. Specifically, the authors characterized molecular shifts that occur as the intestine matures from an immature to an adult-like state, investigating both temporal changes and regional differences between the proximal and distal small intestine. A key objective was to identify gene expression patterns relevant to understanding the region-specific susceptibility and resistance to necrotizing enterocolitis (NEC) observed in humans during the postnatal period. They also sought to validate key findings through complementary methods and to provide comparative context with human intestinal samples. This study will provide a solid reference dataset for the community of researchers studying postnatal gastrointestinal development and diseases that arise during these stages. However, the study lacks functional validation of the interpretations.

      Strengths:

      (1) The inclusion of numerous time points (day 0 through 4 weeks) and comparative analyses throughout the first postnatal month.

      (2) Validation of key interpretations of RNA-seq data by other methods.

      (3) Linking mouse postnatal development to human premature infant development, enhancing its clinical relevance, particularly for NEC research. The inclusion of human intestinal biopsy and organoid data for comparison further strengthens this link.

      (4) The investigation covers a wide array of developmental gene categories with known significance, including epithelial differentiation markers (e.g., Vil1, Muc2, Lyz1), intestinal stem cell markers (e.g., Lgr5, Olfm4, Ascl2), mesenchymal markers (e.g., Pdgfra, Vim), Wnt signaling components (e.g., Wnt3, Wnt5a, Ctnnb1), and various immune genes (e.g., defensins, T cell, B cell, ILC, macrophage markers).

      Weaknesses:

      (1) The primary limitation is that there is no functional validation. The study primarily focuses on the interpretation of RNA expression. This is a common limitation of transcriptomic "atlas" studies, but the functional and mechanistic relevance of these interpretations remains to be determined.

      (2) The data are derived from bulk RNA-Seq of full-thickness intestinal tissue. While this approach helps capture rare cell types and both epithelial and mesenchymal components simultaneously, it does not provide cell-type-specific gene expression profiles, which might obscure important nuances. Future investigations using single-cell sequencing would be a logical follow-up.

      (3) The day 4 samples were omitted due to quality issues, which might have led to missing some dynamic changes, especially given that some ISC genes show dynamic changes around day 6.

      Reviewer #3 (Public review):

      Summary:

      This study uses bulk mRNA sequencing to profile transcriptional changes in intestinal cells during the early postnatal period in mice - a developmental window that has received relatively little attention despite its importance. This developmental stage is particularly significant because it parallels late gestation in humans, a time when premature infants are highly vulnerable to necrotizing enterocolitis (NEC). By sampling closely spaced timepoints from birth through postnatal week four, the authors generate a resource that helps define transcriptional trajectories during this phase. Although the primary focus is on murine tissue, the authors also present limited data from human fetal intestinal biopsy samples and organoids. In addition, they discuss potential links between observed gene expression changes and factors that may contribute to NEC.

      Strengths:

      The close temporal sampling in mice offers a detailed view of dynamic transcriptional changes across the first four weeks after birth. The authors leverage these close timepoints to perform hierarchical clustering to define relationships between developmental stages. This is a useful approach, as it highlights when transcriptional states shift most dramatically and allows for functional predictions about classes of genes that vary over time. This high-level analysis provides an effective entry point into the dataset and will be useful for future investigations. The inclusion of human fetal intestinal samples, although limited, is especially notable given the scarcity of data from late fetal timepoints. The authors are generally careful in their presentation of results, acknowledging the limitations of their approach and avoiding over-interpretation. As they note, this dataset is intended as a foundation for their lab and others, with secondary approaches required to more fully explore the biological questions raised.

      Weaknesses:

      One limitation of the study is the use of bulk mRNA sequencing to draw conclusions about individual cell types. It has been documented that a few genes are exclusively expressed in single cell types. For instance, markers such as Lgr5 and Olfm4 are enriched in intestinal stem cells (ISCs), but they are also expressed at lower levels in other lineages and in differentiating cells. Using these markers as proxies for specific cell populations lowers confidence in the conclusions, particularly without complementary validation to confirm cell type-specific dynamics.

      Validation of the sequencing data was itself limited, relying primarily on qPCR, which measures expression at the same modality rather than providing orthogonal support. It is unclear how the authors selected the subset of genes for validation; many key genes highlighted in the sequencing data were not assessed. Moreover, the regional differences reported in Lgr5, Olfm4, and Ascl2, appearing much higher in proximal samples than in distal ones, were not recapitulated by qPCR validation of Olfm4, and this discrepancy was not addressed. Resolving such inconsistencies will be important for interpreting the dataset.

      The basis for linking particular gene sets to NEC susceptibility rests largely on their spatial restriction to the distal intestine and their temporal regulation between early (day 0-14) and later (weeks 3-4) developmental stages. While this is a reasonable approach for generating hypotheses, the correlations have limited interpretive power without experimental validation, which is not provided here. Many factors beyond NEC may drive regional and temporal differences in intestinal development.

      Finally, the contribution of human fetal biopsy samples is minimal. The central figure presenting these data (Figure 4A) shows immunofluorescence for LGR5, a single stem cell marker. The staining at day 35 is not convincing, and the conclusions that can be drawn are limited to confirming the localization of LGR5-positive cells to crypts as early as 26 weeks.

      We have added additional figures and significantly edited the manuscript based on the insightful suggestions of the reviewers. We added epithelial and mesenchymal deconvolutions as well as additional protein-based analyses using IF. We are very pleased with the improvements since then initial submission, and hope the reviewers will feel similarly.

      Recommendations for the authors:

      Reviewing Editor Comments:

      Two of the reviewers mentioned that the correlations with NEC may be speculative and/or hypothesis-generating. For example, as noted by Reviewer 3, "While this is a reasonable approach for generating hypotheses, the correlations have limited interpretive power without experimental validation, which is not provided here." Based on this, I would recommend that the authors remove the correlations between NEC susceptibility and gene expression changes from the results section and include this only in the discussion section. All reviewers felt that some additional validation of major findings from bulk RNA-seq is warranted. Reviewer 1 suggested additional comparisons with single-cell data or isolated populations; however, as noted by other reviewers, some additional validation using protein markers (i.e., immunofluorescence) would suffice to bolster findings and claims. Reviewers 2 and 3 provide several specific, detailed suggestions below that will improve the clarity of the manuscript through text revisions.

      Thank you to the editor and reviewers for critically evaluating the manuscript and suggesting these changes to strengthen the work.

      We agree that linking the study to NEC was overly theoretical, and have revised the focus of the paper to focus on early postnatal development, removing the speculative links to NEC susceptibility.

      We have added additional antibody-based immunofluorescence data to consider cognate protein expression in Figure 10. We expanded the evaluation of the mesenchymal cell populations, which is particularly poorly characterized in this period.

      Reviewer #1 (Recommendations for the authors):

      My primary concern is for the authors to adequately deconvolute their bulk RNA datasets and to perform additional comparison analyses with either bulk or single-cell isolated epithelium and/or mesenchyme from either adult mice (for regionality) or human fetal data.

      We thank the reviewer for this suggestion. We performed an epithelial cell deconvolution and a mesenchymal cell deconvolution using published datasets and add this information as figure 4. We were unable to perform the mesenchymal deconvolution at the time of submission, because this compartment is understudied, however a recent preprint published mouse single-cell data that we were able to use for this analysis.

      Reviewer #2 (Recommendations for the authors):

      I think that this study will serve as a solid reference for those interested in postnatal intestinal development, and currently, there is a key lack of studies during these stages. I'd strongly suggest making some of the figures more "readable". For example, the font size along many axes and figure legends is very challenging to read when printed out. There are also some minor errors that I caught, but the authors should probably look through more thoroughly:

      We appreciate the reviewer’s enthusiasm for the study. We have attempted to make the figure text more legible.

      (1) In the Results section, the text states "stained tissue sections for CD19 (Fig. 5, column 4)". This should be Fig. 8.

      Corrected, thank you.

      (2) In the abbreviations section, MHCII is misspelled.

      Corrected, thank you.

      (3) The abstract has an extra period after ileum.

      Corrected, thank you.

      Reviewer #3 (Recommendations for the authors):

      (1) Some elements lack precise language that could lead to misconceptions. For example, I disagree with the use of the term duodenum to designate samples taken from the entire proximal half of the small intestine. The duodenum is well established to represent only a small portion of the proximal-most intestine.

      I think this may be a misunderstanding? The RNA samples were taken from the first 2cm of small bowel and the ileal samples form the last 2cm, so for any RNA work these labels are appropriate. For the histology, we prepped the samples initially by bisecting the SI, however the images presented are only from the duodenum or ileum, which we could determine by standardizing the Swiss roll orientation during the prep as we describe in the methods. We have added text to clarify this to the reader in the methods: “We analyzed only the segments that corresponded to the duodenum and ileum for the histology, in order to maintain consistency with the RNA data.”

      (2) At the start of the Results section, it would be helpful to emphasize that the initial data presented are from murine tissue rather than human (this is stated in the introduction, but it is easy to lose track since both mouse and human tissue are used throughout). A graphic overview of all samples obtained would also aid clarity. The species should be clearly noted in each figure legend to avoid confusion.

      Thank you for these great suggestions. We added language in the results section, added a logo designating mouse or human to each figure, and also added a graphical overview of the samples (Fig. --).

      (3) The statement "PCA of all samples showed that duodenal samples and ileal samples intermixed and did not segregate by tissue type in early development but segregated more at later time points (Supp. Fig. 1C)" is not clearly supported by the data as presented; this panel requires timepoint annotations.

      Thank you for pointing this out. We have added this data as a new panel in this figure, 1D.

      (4) The heatmaps in Figure 1C-D could be moved to the supplement, with main-figure heatmaps showing the subset of samples actually used for downstream analyses (e.g., with days 4 and 6 removed).

      We have removed Fig. 1 C-D to the supplement, thank you for the suggestion. Fig. 1 E-F now become C-D and contain the heatmap of the samples actually used.

      (5) Two batches are labeled in Figures 1C-D but are not mentioned in the text. Batches should be described in the Methods and noted in figures. Please clarify how batch effects in the sequencing data were assessed.

      Thank you for asking us to clarify this for readers. We have added a section to the methods to explain the need for the batches (too many samples for one run on the sequencer we were using at the time) and how they were handled in the data analysis.

      (6) While the rationale for focusing on specific timepoints and regions potentially relevant to NEC susceptibility is appreciated, the interpretation that these transcriptional changes directly relate to NEC pathology is highly speculative. In my view, these points could be minimized in the Results and moved to the Discussion.

      We agree that linking the study to NEC was overly theoretical, and have revised the focus of the paper to focus on early postnatal development, removing the speculative links to NEC susceptibility.

      (7) Figure 3A: Could EpCAM be included as a canonical epithelial marker?

      We have included EpCAM in the epithelial cell markers (Fig. 3A).

      (8) The use of the word 'expansion' in the phrase "suggesting that epithelial expansion is represented by cluster 2" is unclear and should be clarified or better supported.

      Thank you, this word was imprecise. We have revised the text to: “suggesting that epithelial villus growth, potentially in the form of increased length or increased density, is represented by cluster 2.”

      (9) Please consider incorporating the newly identified intestinal stem cell marker Fgfbp1 (Capdevila et al. and Malagola et al., Cell 2024) in the ISC marker panel.

      We have now included Fgfbp1 (removed Ascl2 to make space given it was redundant with Olfm4 and Lgr5), however we note that the paper referenced by the reviewer suggests that Fgfbp1 marks a distinct population of stem cells, rather than redundantly marking the Lgr5+ISC we previously sought to highlight in this panel.

      (10) The conclusions that can be drawn from the human organoid data in Figure 4B are unclear. In the Methods, please note when cells were collected (i.e., days post-passage) and whether this was consistent across samples.

      Thank you. The samples were consistently grown to confluence, collected 5 days after the most recent passage to allow the organoids to recover. We have added this to the details on this experiment’s methodology.

      (11) In discussing regional Wnt regulation, consider citing and relating findings to Maimets et al., Nat Commun 2022. Other relevant literature on zonation could also be included in the discussion.

      Thank you for this suggestion. We pulled some of the genes indicated in this Maimets study to associate with zonation and discussed them in the context of the Wnt figure (Fig. 5D) and added some discussion on this.

      (12) More precise language and references would strengthen descriptions of analysis approaches. For example: "We sought to confirm some of these findings using the newer RNAseq immune cell deconvolution approach that combines key genes..." - is this a published method that can be explicitly cited?

      Thank you for noting this. We have changed the language introducing this section and added references for deconvolution.

      (13) The figure callout in "the proportion of CD19+ increased over time as a percentage of the total PP lesions (Supplementary Figure 3C), indicating enlargement of the germinal centers of time" appears incorrect. The conclusion that this reflects germinal center enlargement is not, in my view, supported by the data.

      We acknowledge the reviewer’s point that relative proportionality of the PP may not be strictly a function of size, and have removed this conclusion statement accordingly.

      (14) Phrases such as "the data was very messy and hard to interpret" could be replaced with more precise language appropriate to a scientific report (though I sympathize!).

      Thank you for pointing out this overly informal language, we have revised.

      (15) Ensure consistent lettering conventions across figure legends.

      Corrected for consistency, thank you.

      (15) In Figure 2, larger axis text and an indication of the developmental timeline would improve clarity. The meaning of the x-axis label "GeneRatio" should also be clarified.

      Given the amount of text in this figure, it is impossible to enlarge the text more, unfortunately. We wanted to show more the family names and cluster patterns. Persons uses an e-version (majority of readers today) can easily zoom in to see more detail if desired. We added text to the figure legend “Gene ratio on the y-axis indicates the proportion of your significantly altered genes that are involved in a specific biological pathway or function.”

      (16) In Figure 3 (and other similar mRNAseq/validation panels), maintaining a consistent color code between mRNAseq and qPCR validation would aid interpretation. In panel F, the key's colors should align with the graph.

      We adjusted the qPCR figures to correspond with the RNASeq.

      (17) In Figure 4, please specify which intestinal region the samples are from, as this is especially relevant given the regional differences observed in the murine data.

      Thank you, these are from ileum, we have designated this more clearly in the figure.

    1. Author response:

      Reviewer #1 (Public review):

      Summary:

      This study presents a workflow for nanoscale imaging of endogenous synaptic receptors in intact adult brain tissue. By combining live-tissue chemical labeling of native surface AMPA receptors (AMPARs) using the CAM2 probe, two-color 3D super-resolution microscopy, adaptive optics, in situ point spread function retrieval, and chromatic aberration correction, the authors establish a platform for quantitative super-resolution mapping of synaptic architecture deep within brain tissue.

      The authors provide convincing evidence that AMPAR organization differs between the hippocampus and cortex and demonstrate that early tauopathy is associated with selective disruption of extrasynaptic and synaptic nanodomain receptor organization in the hippocampus prior to overt neurodegeneration.

      Beyond the specific biological findings, the work represents a significant technical advance that enables quantitative investigation of endogenous synaptic receptor architecture in native brain tissue and will be of broad interest to researchers in synaptic biology, super-resolution microscopy, and neurodegeneration.

      Strengths:

      (1) Introduces and validates a strategy for nanoscale imaging of endogenous surface AMPARs in adult brain slices using CAM2 labeling and two-color 3D super-resolution imaging.

      (2) Achieves 10s of nanometers localization precision in thick tissue and validates synaptic structural measurements against previous literature benchmarks.

      (3) Reveals regional differences in AMPAR organization, including a larger extrasynaptic receptor pool in hippocampal regions compared with neighboring cortical regions.

      (4) Identifies early, region-specific alterations in AMPAR distribution and nanodomain organization in the PS19 tauopathy model.

      We thank the reviewer for reviewing our manuscript and appreciating both the neurological findings, as well as the broader technological advance.

      Weaknesses:

      (1) Statistical power is limited by the relatively small number of animals analyzed, although large numbers of synaptic structures were sampled within each mouse.

      We agree that despite sampling a large number of synaptic structures and imaging fields per mouse, a sample size of n=3 mice per genotype is a limitation of the study. We will highlight this point in the discussion section.

      (2) Synaptic classification relies on PSD-95 cluster detection criteria that may bias analysis toward more strongly enriched synapses, as acknowledged by the authors.

      We do agree and acknowledge in the manuscript that PSD-95 cluster detection may bias the synaptic fraction analysis towards more enriched synapses. In addition, we will also compare PSD-95 cluster detection across brain regions and genotypes.

      Reviewer #2 (Public review):

      Summary:

      This is a technically sophisticated effort to visualize the nanoscale organization of native surface AMPA receptors in adult mouse brain. The authors combine chemical labeling of endogenous AMPARs with 3D, 2-color super-resolution microscopy. They use this to compare hippocampal and cortical AMPAR organization and to characterize changes in a P301S mutant mouse tauopathy model. The authors report a greater density of surface AMPAR localizations in hippocampal CA1 than in two examined cortical regions, as well as a smaller fraction of AMPARs organized in synaptic clusters. They report that PS19 tauopathy is associated with reduced hippocampal AMPAR localization density, a relative depletion of the population classified as extrasynaptic, and reduced organization of receptors within synaptic nanodomains.

      Strengths:

      The methodological contribution is substantial. The authors developed a valuable set of methods for examining endogenous surface AMPAR organization in brain tissue. The imaging methodology could be useful across many questions in synaptic neuroscience.

      We thank the reviewer for reviewing our manuscript and appreciating the imaging methodology developed in this manuscript.

      Weaknesses:

      While the biological observations are interesting, several aspects of the neuroscience interpretation require clarification, and some of the biological conclusions should be weakened unless the measurements can better justify them. I provide several comments intended to strengthen this interesting manuscript.

      We thank the reviewer for the in-depth comments which will help strengthen our manuscript. We provide our response to each of them below.

      (1) The authors measure fluorescent localization counts but often interpret these as AMPAR numbers. I believe that individual fluorophores can generate multiple localizations and that labeling efficiency can vary, challenging their frequent interpretation as AMPAR numbers. Importantly, AMPARs are tetrameric complexes with potentially different subunit compositions, so one AMPAR could be observed as 0-4 fluorescent localizations. The uncertainty is particularly important for comparisons of AMPAR abundance per cluster and nanodomain. The authors should consistently distinguish localization density from receptor number and clarify which conclusions depend on assumptions about labeling and the assumptions of photophysical equivalence between experimental conditions. The paper would be more rigorous and the claims more legitimate if the authors were disciplined throughout about using empirical descriptors instead of interpretations.

      We agree that due to the photo-physical behavior of the fluorophore combined with the tetrameric AMPAR composition and labeling efficiency variations, the AMPAR localizations should not be directly interpreted as absolute AMPAR numbers. We will standardize the wording to “AMPAR localizations” instead of “number of AMPARs / receptors” used at times in the Result and Discussion sections. We will also add an explicit statement of the labeling and photophysical assumptions and of which comparisons depend on photophysical equivalence across conditions. Because all samples are prepared, labeled and imaged identically, relative differences in localization density remain valid. We already note the requirements for absolute AMPAR counting in the Discussion section and will expand that caveat.

      (2) The distinction between synaptic and extrasynaptic receptors is central to the manuscript. The authors identify synaptic receptors either through density-based clustering or proximity to PSD-95 clusters. However, neither measure directly establishes anatomical synaptic localization. This is particularly consequential because only ~1/3 of morphologically identified YFP-positive spines contain PSD-95 clusters that meet the detection criteria. It seems to me that AMPARs associated with weakly-labeled or undetected synapses could then be erroneously classified as extrasynaptic. PSD-95 detection should be assessed across regions and genotypes, and a sensitivity analysis undertaken to ensure that the conclusions are robust to the choices of clustering and distance thresholds.

      We agree with the concern and acknowledge in the manuscript that PSD-95 cluster detection may bias the synaptic fraction analysis towards more enriched synapses. We also thank the reviewer for additional analysis suggestions. We will include a comparison of PSD-95 cluster detection across regions and genotypes. We note that in fig. S7, we already compare two AMPAR-PSD-95 distance thresholds used to define the synaptic region, showing that the differences in synaptic fraction across regions and genotypes are insensitive to small changes in the threshold choice. In addition, we will perform a broader sensitivity analysis of the proximity-based synaptic fraction measurement across varying distance thresholds and PSD-95 clustering parameters.

      (3) The authors suggest that the larger extrasynaptic AMPAR population in the hippocampus provides a reserve for rapid synaptic recruitment and that its reduction in tauopathy constrains plasticity. This is plausible, but receptor abundance does not establish receptor mobility or availability for synaptic capture. The importance of AMPAR surface diffusion for hippocampal LTP and contextual learning has been demonstrated (see Penn et al., Nature, 2017), but the current study does not measure diffusion or receptor exchange. The authors should temper their interpretation and explain the caveats.

      We agree. Our data measures spatial distributions and not diffusion or receptor exchange. We will present the reserve-pool interpretation (a pool available for rapid synaptic recruitment) explicitly as a hypothesis motivated by prior work rather than a conclusion, and add the caveat that diffusion or exchange measurements would be needed to test it.

      (4) The authors infer that there has been a preferential extrasynaptic AMPAR loss from the reduced total AMPAR localization density and the increased synaptic fraction they measured. Because both synaptic and extrasynaptic populations could decrease even when the synaptic fraction increases, they should calculate the synaptic and extrasynaptic localization densities separately for each mouse. This would clarify the magnitude and selectivity of the changes that they report and help to reconcile the potentially contradictory increased synaptic fraction with reduced AMPAR localization density within synaptic clusters and nanodomains.

      We thank the reviewer for this suggestion. We will include a comparison of synaptic and extrasynaptic densities calculated separately for each mouse. This will certainly help clarify the magnitude and selectivity of the reported changes.

      (5) The authors adjust DBSCAN parameters for PS19 hippocampus in response to reduced overall localization density. Because the resulting clustering measurements are themselves used to establish genotype differences, it is important to demonstrate that the conclusions are robust to parameter selection. Analyses using identical parameter sets across conditions, together with simulations in which WT localization patterns are subsampled to match PS19 localization density, would help determine whether the reported changes reflect biological reorganization rather than density-dependent detection effects. Similar validation is important for the nanodomain analysis. I found that, in general, the authors should have made a greater effort to ensure that their measurements are robust to the parameter choices.

      We will separate the two requested analysis, which serve different purposes.

      (i) Identical parameters across conditions: we show in Fig. S9 that identical parameters under-detect AMPAR clusters in the lower density PS19 hippocampus, which is precisely why we scaled the DBSCAN parameters for AMPAR cluster analysis in PS19 hippocampus. Moreover, the proximity-based synaptic fraction measurement, which is independent of any AMPAR cluster analysis, was performed with identical distance thresholds and PSD-95 cluster detection parameters across regions and genotypes. It shows an increase in synaptic fraction in PS19 hippocampus (Fig. 4f).

      (ii) Density-matched subsampling: we agree this is a key control. We will randomly down-sample AMPAR localization in wild-type hippocampus to match the localization density with PS19 hippocampus, and then re-run AMPAR cluster analysis. This will help identify PS19 changes that reflect genuine reorganization and those that reflect density-dependent effects.

      (6) CA1 comparisons with motor/somatosensory cortex require more precise anatomical characterization. What cortical layers and hippocampal dendritic compartments are being compared? These are not homogeneous structures in almost any regard. AMPAR or, more empirically, fluorescence localization density per imaging field is not necessarily equivalent to AMPAR density per dendritic membrane area or per synapse. Differences in neuropil composition, spine density, and synapse density could contribute to the observed differences when there is, in fact, no AMPAR density per dendritic membrane area. Proper anatomical normalization or a stricter comparison of equivalent neuronal compartments would strengthen the interpretation. I believe that the authors are aware of the issue, as they did an analysis along a single dendrite, but this has to be done more thoroughly for them to justify the conclusions they assert.

      We thank the reviewer for highlighting this important concern. We agree that CA1 hippocampus and cortex are not homogeneous structures. We will state the compartments explicitly in the revision. Stratum radiatum layer was imaged in the CA1 region of the hippocampus. In cortex, layer V pyramidal neurons are labeled with YFP in Thy1-YFP-H mice and their apical dendritic field was imaged in layers II/III and IV.

      In the paper, we show AMPAR cluster analysis across the whole imaging field of view, as well as analysis restricted to the AMPAR localizations along a YFP dendrite for comparison. In addition, we will also report membrane area-normalized AMPAR localization density as well as the spine density across brain regions and genotypes.

      (7) The main comparisons involve three mice per group, and the authors correctly analyze mouse-level averages. Nonetheless, the small number of biological replicates limits the strength of the conclusions about regional specificity and disease effects. The test statistics and degrees of freedom, not just the p-values, should be presented. In addition, effect sizes and individual mouse values should be presented. The absence of a statistically significant cortical effect does not establish that cortex is unaffected. There could be genotype-by-region interactions, which the authors should check.

      We agree that despite sampling a large number of synaptic structures and imaging fields per mouse, a sample size of n=3 mice per genotype is a limitation of the study. We will further highlight this point in the discussion section.

      We already report all the individual mouse values plotted in Fig. 3-4, in Tables S5, S10 and S11. In addition, we will report test statistics, degrees of freedom and effect sizes. We will also test for genotype-by-region interactions.

      (8) The authors describe that 6-mo PS19 mice precede neurodegeneration and they assert that the observed AMPAR-associated changes relate to the onset of synaptic dysfunction. However, Yoshiyama et al., Neuron, 2007 demonstrate hippocampal synapse loss and impaired synaptic function at three months in PS19 mice, before detecting fibrillary tau. The present observations likely occur after synaptic pathology in thePS19 mice. The authors should distinguish structural correlates of established dysfunction from the mechanisms that may have initiated that dysfunction. More importantly, the assertion that neuronal or synaptic anatomy is preserved in the PS19 mice should be supported by appropriate measurements.

      Yoshiyama et al., Neuron, 2007 report a decline of synaptophysin and α-synuclein immunoreactivity at 3 months of age, a decline of GluR2/3 immunoreactivity at 6 months of age and reduced basal synaptic transmission and CA1 LTP at 6 months of age in PS19 mice. Whereas the filamentous tau lesions were reported to be developed at 6 months of age and overt neuron loss and brain atrophy was reported by 9-12 months of age. In our manuscript, we already note that functional deficits have been reported by Yoshiyama et al. and others by the 6-months age and do not wish to claim that our reported changes precede synaptic pathology and dysfunction. Our precedence statement is relative to the overt neurodegeneration and brain atrophy that is reported at later stages. We will make this distinction more explicit and update any wording that could be read as framing the AMPAR changes as preceding synaptic pathology and dysfunction. In addition, we will also compare the YFP-labeled spine density across brain regions and genotypes.

      (9) The reduction of the AMPAR nanodomain organization is potentially important. However, the authors do not measure presynaptic release sites or trans-synaptic alignment. To be rigorous, the data establish altered postsynaptic receptor organization but do not demonstrate disruption of trans-synaptic nanocolumns or establish the functional consequences for quantal transmission. If the authors do not provide evidence for these claims they should not make them and make it clear these are (reasonable) speculations for which they did not collect the data.

      We agree that our data establishes altered postsynaptic receptor organization, but does not directly demonstrate the disruption of trans-synaptic nanocolumn. We will restrict our wording to postsynaptic receptor organization and present any statement about nanocolumns or quantal efficacy explicitly as reasonable speculation for which we did not collect any data.

    1. Author response:

      We thank you and the three anonymous reviewers for your careful evaluation of our manuscript. We here provide a provisional author response to the reviewer’s comments.

      Reviewer #1:

      Major point 1.

      First, the physiological relevance of the TG2-DGP fusion construct should be discussed in greater depth, as the permanently linked fusion protein may not fully recapitulate naturally occurring TG2-gluten complexes.

      We thank the reviewer for this important point and agree. The TG2-DGP fusion protein is an artificial antigen and enforces a fixed linkage between TG2 and a deamidated gluten peptide, whereas naturally occurring TG2-gluten complexes are transient and their abundance and availability to TG2-specific B cells remains uncertain. We will discuss this limitation in greater detail in our revised manuscript.

      Major point 2.

      Second, the proposed mechanism of antigen uptake into Peyer's patches remains largely inferential, and evidence supporting involvement of M cells or other antigen-sampling pathways would strengthen the conclusions. The authors conclude that Peyer's patches are the primary site of priming and propose that luminal TG2-gluten antigen is sampled from the intestinal lumen. However, the study does not directly demonstrate the route of antigen entry (for example, via M cells, dendritic cells, or other pathways). Additional discussion or experimental evidence supporting the proposed antigen trafficking mechanism would strengthen the conclusions. Given the emphasis on Peyer's patches, direct assessment of M-cell involvement would be particularly valuable.

      Suggested experiment: RANKL-induced M-cell expansion (or M-cell depletion) to test whether M-cell-mediated sampling is required for induction of TG2 autoimmunity.

      We thank the reviewer for this excellent suggestion. Assessing M-cell involvement would indeed be very interesting, and M-cell depletion would be a logical way to test whether M-cell-mediated uptake is required for TG2 autoimmunity in our model. These experiments however require breeding our mice and validating M-cell depletion in our HLA-DQ2.5 Tgm2-ω18merEE x Villin1-rtTA transgenic mice, which is a time-consuming endeavor and would be best suited in a follow-up study. To address the reviewer’s concern in the current manuscript, we will discuss that our data identify the Peyer’s patch as an important site for B-cell priming. We will discuss entry routes via M cells as one plausible mechanism alongside other mechanisms such as uptake by dendritic cells.

      Minor point 1.  

      Villin is known to be expressed throughout the whole villus axis; however, the transgenic model described here seems to express the fusion protein in a specific cell type only; the authors should explain the reason for this. It would be better if the authors specified the region used in immunohistochemistry.

      We will address this point and provide additional data on the expression of the TG2-DGP fusion protein in epithelial cells the revised manuscript, as is also recommended by reviewer #3.

      Minor point 2.

      The authors showed that CD4 proliferation holds high until a dilution of 1:24; however, B cells show until 1:2 dilution. In the co-culturing, the author used CD4: B cells approximately in the ratio of 1:10. The reason for this should be explained and justified.

      The CD4 T cell : B cell ratio used here was not specifically optimized for this study, and the choice of ratio, if any, was primarily a result of relatively poor CD4 T cell yields. We agree that the T cell and B cell readouts differ in sensitivity, consistent with our previous publication (PMID 34731200) in which we observed efficient T-cell proliferation in response to recombinant TG2-DGP fusion protein at much lower antigen concentrations then those required to detect B-cell proliferation. Because B-cell proliferation depends on T-cell help, we acknowledge that the ratio can affect the B-cell readout, particularly at low antigen doses. Our conclusion, however, does not concern the antigen threshold required to activate either cell type, but rather that the epithelial cell lysate engages both T cells and B cells.

      Minor point 3.

      The authors showed that TG2-specific B cells were enriched in the PP, accompanied by higher gluten-specific CD4 cells. Recent studies showed that M cells express TGM2 and can indeed present the gliadin peptide to T cells independent of APCs. (Wang et al. 2025 Nature). The authors should discuss this in light of their findings.

      The paper the reviewer refers to demonstrates that human M cells can present antigens to T cells, but importantly the same paper shows that mouse M cells do not have this capacity. This species difference infers that this mechanism does not affect the interpretation of our mouse model. It is also not directly relevant to the question our study addresses as M-cell presentation to T cells does not explain how TG2-specific B cells acquire TG2-gluten antigen, which is the step that drives the autoantibody response in our model.

      Minor point 4.

      Regarding mice, mentioning the gender and age of the mice is important. Please include this information.

      This information will be included in the revised manuscript.

      Minor point 5.

      It would be better if the authors specified the region of tissue used in immunohistochemistry.

      See response to minor point 1.

      Minor point 6.

      Regarding the lysate preparation, the authors should mention whether they used the whole small tissue or a segment. It would be helpful if the author provides the IEC lysate in terms of protein concentration rather than dilution.

      This information will be included in the revised manuscript.

      Reviewer #2:

      Major point 1.

      Physiological relevance of antigen dose and kinetics. The dox-induced pulse of TG2-DGP expression is a bolus-like event, whereas endogenous IEC shedding and TG2 release presumably occur continuously at low levels. The author should discuss more how the kinetics and magnitude of the induced signal compare with estimated physiological TG2 derived from IEC turnover, and whether the strong immunogenicity observed here could overstate the potency of the natural process.

      The reviewer raises a very important and valid point that also relates to major point 1 raised by reviewer #1. We will discuss how our artificial model relates to endogenous TG2-gluten complex formation in greater depth in the revised manuscript.  

      Major point 2.

      The translational value of the model may hinge on epitope relevance. Celiac anti-TG2 antibodies preferentially target a small number of conformational epitopes on open TG2, and this restriction is tied to how TG2 is captured and presented. A central claim of the paper is that IEC-derived TG2 is the relevant source for autoantibody elicitation, rather than extracellular matrix-associated TG2 or other pools. If IEC-derived TG2 only activates non-human-relevant epitopes, that would undermine the claim that this is the mechanism responsible for the actual patient autoantibody repertoire. Whether IEC-derived TG2-DGP would recruit a broader range of TG2 epitopes seen in human disease, or only the subset compatible with this conformational epitope, is worth examining.

      The anti-TG2 B cells in our model carry a B-cell receptor derived from a celiac disease patient, which targets epitope 1 of TG2, a dominant epitope of celiac autoantibodies. This antibody binds mouse and human TG2 with equal affinity (PMID ID 31727780). The response elicited in our model is therefore directed at a human disease-relevant epitope, an epitope that is also present on mouse TG2. We will clarify this in the revised manuscript.

      Reviewer #3:

      Major point 1.

      First, given the importance of the expression of the antigen in IECs into the lumen and the strong responses in Peyer´s patches, the authors should have provided additional information about the expression of the TG2-fusion protein in epithelial cells in the follicular-associated epithelium covering and other epithelia surrounding the structure. Is it possible that even M cells express the antigen, and that it may not need to be in the lumen to reach the Peyer´s patches?

      We will address this point and provide additional data on the expression of the TG2-DGP fusion protein in epithelial cells of the follicular-associated epithelium in the revised manuscript. 

      Major point 2.

      Second, it is not addressed whether antigen-specific pre-activation of T cells using peptide and CT is strictly needed or if CT alone could have created an environment where antigen-specific responses are triggered by the TG2 fusion protein alone (i.e. using CT as an adjuvant for a response to an antigen expressed in IEC). Or even if other inflammatory gut responses, not necessarily triggered by CT but instead by virus, pathogenic bacteria or oral dextran, would have sufficed. Although T cell cross-reactivity to external antigens could play a role in humans developing disease, it would be easier to envision a situation where any gut inflammation, in the presence of antigen-specific B and T cells and a susceptible HLA environment, could trigger a response.

      We thank the reviewer for this important point. We agree that it is relevant to assess whether an inflammatory environment could trigger antigen-specific responses to the TG2-gluten fusion protein. To address this, we will attempt to include new experimental data in the revised manuscript in which the pre-activation of gluten-specific T cells is omitted, and cholera toxin as adjuvant is administered at the time of TG2-gluten protein induction. Testing other inflammatory triggers such as viral or bacterial infection is beyond the scope of the study, but we will discuss it as an important question in the revised version.

      Major point 3.

      Finally, the role of dendritic cells and/or other APCs present in the gut and/or Peyer´s patches in the priming of T cells should probably have been discussed, i.e., whether presentation of antigen by B cells is sufficient or not. If inflammation or CT alone is sufficient for T cell priming (see above), this indirectly supports that direct presentation from B cells may play an important role in T cell activation.

      We will expand the discussion on priming by B cells, dendritic cells and other antigen-presenting cells in light of the new data from Major point 2. We note that these experiments will indicate whether antibody responses can occur without pre-activation of T cells with peptide and cholera toxin, but they will not by themselves identify B cells as the antigen-presenting cells involved in priming of the T cells.

    1. Author response:

      The following is the authors’ response to the previous reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      Hsiung et al. investigated whether the effects of autophagy gene knockdown on the lifespan of long-lived C. elegans mutants depend on experimental conditions. The authors first compiled published data on autophagy-dependent lifespan regulation in daf-2 and wild-type backgrounds, highlighting that prior results are notably inconsistent and likely context-dependent. They then systematically tested the lifespan effects of RNAi knockdown of six autophagy genes (atg-2, atg-4.1, atg-9, atg-13, atg-18, and bec-1) in wild-type (N2), daf-2 (reduced insulin/IGF-1 signalling), and glp-1 (germlineless) animals, while varying temperature, daf-2 allele, FUDR concentration, and bacterial infection status.

      The key findings are as follows. In wild-type animals, lifespan suppression by most autophagy gene knockdowns was more pronounced at 20°C than at 25°C, where little or no effect was observed. In daf-2 mutants, stronger lifespan suppression was seen in the weaker daf-2(e1368) allele at 20°C, but not in the stronger daf-2(e1370) allele, and effects were largely absent at 25°C. In glp-1 mutants, four of six gene knockdowns suppressed lifespan to a greater extent than in N2, though again in a temperature-dependent manner. FUDR at a high concentration (800 µM) abolished the life-shortening effects of most knockdowns and, in the case of atg-9 and atg-13, led to lifespan extension. Kanamycin treatment to eliminate bacterial proliferation did not fully account for the lifespan effects, suggesting that increased susceptibility to infection is not the primary mechanism. The authors also tested the programmed aging hypothesis that autophagy promotes lifespan reduction through biomass repurposing, but found no changes in vitellogenin levels upon knockdown of any of the six genes.

      Altogether, among all genes tested, atg-18 knockdown produced the strongest and most consistent lifespan suppression across nearly all conditions, including both daf-2 and glp-1 backgrounds. The authors probed whether atg-18 acts through the FOXO transcription factor DAF-16 by examining dauer formation and ftn-1 expression, but found no evidence for this, suggesting a DAF-16-independent mechanism.

      Strengths:

      The primary strength of this work lies in its systematic and comprehensive approach to dissecting how experimental variables influence the outcome of autophagy-lifespan epistasis tests. The compilation of prior data alongside the authors' own multi-condition dataset is a genuinely useful resource for the field. The study raises a timely and important point about condition selection bias in interpreting autophagy lifespan relationships, with broader relevance to C. elegans studies. The finding that atg-18 behaves distinctly from other autophagy genes across a range of experimental conditions is particularly noteworthy and provides an interesting direction for future mechanistic investigation.

      Comments on revised version.

      The authors have carefully addressed the concerns raised in the previous review and have incorporated most of the suggested revisions. In particular, the revised manuscript provides greater clarity regarding the effects of glp-1 and FUDR and improves the presentation and interpretation of the experimental findings. The authors have also provided useful clarification regarding the variability between lifespan experiments, the number of biological replicates, and the interpretation of RNAi efficacy.

      I have only two minor suggestions concerning the wording and organization of the manuscript, which I have communicated separately to the authors. These points are intended to further improve clarity and accuracy and do not affect my overall assessment of the study.

      Overall, I am satisfied with the revisions and consider the manuscript to be a valuable contribution to our understanding of the context dependence of autophagy-mediated lifespan regulation.

      Reviewer 1 made several further suggestions for improvements to the text that we agree with.

      Reviewer #2 (Public review):

      Summary:

      This study examines how genes involved in cellular recycling (autophagy) influence lifespan under different experimental conditions. The findings help clarify why previous studies have reported conflicting results about whether blocking autophagy shortens or extends lifespan. The work will be of interest to researchers studying aging and cellular stress responses, particularly those using model organisms.

      Strengths:

      The findings are valuable, as they help resolve inconsistencies within a specific subfield of aging research. The evidence presented is solid, as the data broadly support the primary claims of the study. In addition, the discussion is thorough and thoughtfully integrates the findings within the broader context of the field.

      Weaknesses:

      Additional functional validation would further strengthen the conclusions.

      Comments on revised version.

      I have reviewed the revised manuscript. Overall, the authors have addressed most of my concerns, and the revised manuscript has been improved. The study provides a comprehensive examination of the context-dependent effects of autophagy gene knockdown on lifespan in C. elegans. The data are solid and provide valuable information for understanding the conflicting results currently reported in the literature regarding the role of autophagy in longevity.Recommendations for the authors:

      Reviewer 2 correctly noted that measurements of autophagic flux would strengthen our claims. We had originally planned to include flux measurements in this study, but our experience with the methodologies involved led us to a separate critical study of such methodologies that we are in the process of writing up.

      Recommendations for the authors:

      Reviewing Editor Comments:

      The manuscript could still be strengthened by taking into account the points raised by Reviewer 2, in specific the validation of autophagy with different techniques, such as western blotting and potentially raise the strength of evidence from solid to convincing.

      Reviewer #1 (Recommendations for the authors):

      I would like to thank the authors for carefully addressing most of my previous concerns in their revised manuscript and incorporated most of the suggestions. Most of my concerns have been adequately addressed. However, I have two minor points that, in my opinion would further improve the clarity and accuracy of the manuscript.

      We are glad that our revisions have at least addressed most of the reviewer’s concerns.

      The authors have appropriately incorporated glp-1 into the abstract and have clarified the statement regarding FUDR. However, in the current version, these two statements still feel somewhat disconnected from the overall flow of the abstract, as they are inserted in the middle of the discussion of the effects observed in daf-2. This interrupts the logical progression of the paragraph and may make it slightly more difficult for the reader to follow the main findings regarding daf-2. I would suggest moving these two statements after the main findings concerning daf-2 have been presented. This would allow the abstract to first provide a coherent summary of the daf-2 results and then introduce the additional findings regarding FUDR and glp-1. I believe this would improve the overall readability and narrative flow of the abstract.

      We have revised the abstract along these lines and agree that this improves the flow of the argument. We have used the revised abstract.

      In reply to the 10th point, I appreciate the authors' clarification that their primary focus is on the suppression of class I mutants rather than the effects on N2. However, I believe the revised sentence still remains slightly misleading "These findings are broadly consistent with the earlier observation that bec-1 and vps-34 RNAi shortened the lifespan of the daf-2(mu150) class 1 mutant but not of N2 at 20°C". As presented in the current manuscript, the cumulative dataset indicates that bec-1 RNAi does significantly suppress N2 lifespan. Therefore, the phrase "but not of N2 at 20°C" is not accurate in the context of the present study, even if the authors' main point is that the effect on the class 1 daf-2 mutant is of particular interest. I would therefore suggest rephrasing this sentence to avoid implying that bec-1 RNAi has no effect on N2 lifespan.

      We agree that this account was rather too broad brush, and have corrected it to improve precision, adding the following. “(though in the present study bec-1 RNAi did also reduce N2 lifespan, Table S2)”

      Overall, I am satisfied with the authors' responses and the revisions made to the manuscript. Addressing these two minor points would further improve the clarity and accuracy of the manuscript.

      Reviewer #2 (Recommendations for the authors):

      I have reviewed the revised manuscript. Overall, the authors have addressed most of my concerns, and the revised manuscript has been improved. The study provides a comprehensive examination of the context-dependent effects of autophagy gene knockdown on lifespan in C. elegans. The data are solid and provide valuable information for understanding the conflicting results currently reported in the literature regarding the role of autophagy in longevity.

      We are glad that our revisions have at least addressed most of the reviewer’s concerns.

      One of my major concerns from the first review, however, has not been fully addressed. The authors rely primarily on qPCR to demonstrate the effectiveness of RNAi-mediated knockdown of autophagy genes. Although qPCR data confirm transcriptional knockdown, they do not necessarily demonstrate a corresponding reduction in protein levels or functional inhibition of autophagy. An independent approach, such as Western blot analysis of lipidated LGG-1/ATG-8, would make the conclusions more convincing. Nevertheless, given the overall quality and consistency of the data, I do not consider this issue sufficient to prevent publication.

      Assays of autophagy would indeed have been informative. We did initially plan to test effects of atg RNAi on autophagic flux using a dual fluorescence reporter. However, initial tests identified complex technical issues with the assay that have taken us several years to make sense of (we have almost finished writing up this work). A Western blot approach might have been less problematic, at least in terms of estimating effects on lipidated LGG-1/ATG-8 level. However, any changes could, at least in principle, reflect either decreased or increased autophagic flux.

      The findings of this study also raise an important issue for future studies of autophagy and longevity, particularly when RNAi is used to manipulate autophagy gene expression. RNAi methodology can vary considerably among laboratories, and these differences may contribute to apparently conflicting results. Different laboratories may use different RNAi constructs targeting the same gene. Some investigators generate their own RNAi plasmids using either genomic DNA or cDNA fragments, and the sizes and locations of the targeted sequences can differ. Other laboratories use RNAi clones obtained from established C. elegans RNAi libraries, such as the Ahringer or Vidal libraries. Such differences could affect knockdown efficiency.

      In addition, the method used to deliver RNAi should be considered when comparing results among studies. Most laboratories use feeding RNAi, whereas some studies used injection RNAi. Injection RNAi can produce substantially stronger gene knockdown than feeding RNAi in many experimental settings. Thus, differences in the RNAi delivery method, together with differences in the RNAi constructs themselves, could result in different degrees of gene inhibition and potentially different effects on lifespan. This issue may be particularly important for autophagy genes, for which the biological consequences could depend on the extent of gene inhibition. For these reasons, it would be valuable for future studies in this area to clearly report the source and characteristics of the RNAi constructs used, as well as the method of RNAi delivery.

      This is all correct, and is something that we give little emphasis to in the manuscript, since it relates to possible sources of condition dependency that we did not investigate. Most studies use RNAi by feeding and specify when it is initiated (see Supplementary Table 1). In our tests we opted to initiate RNAi at the end of development, to avoid life shortening effects of disruptions to development.

      Overall, the manuscript presents solid and valuable data that help further our understanding of the role of autophagy in longevity.

    1. Author response:

      We thank the editors and reviewers for their thoughtful and constructive assessment of our manuscript. We appreciate their recognition of the value of investigating oscillatory dynamics during overt picture naming and welcome the opportunity to strengthen the analyses and clarify the interpretation of our findings.

      Functional interpretation and experimental design

      We acknowledge that the contrast between picture naming and scrambled-image rejection does not independently isolate the component processes involved in spoken language production. Although the observed patterns of theta phase coupling and theta–gamma phase-amplitude coupling are consistent with the proposed involvement of visual, semantic and language-related networks, the study was designed to investigate distributed neural dynamics during overt picture naming, rather than to establish a one-to-one correspondence between these coupling patterns and specific psycholinguistic operations.

      We will therefore revise the manuscript to distinguish more clearly between the observed neurophysiological findings and their proposed functional interpretations. We will also broaden the theoretical framework to incorporate alternative accounts of the identified networks and relevant contemporary models of language production, and reconsider claims concerning the right fusiform cortex as an integration hub.

      Temporal alignment and motor-related confounds

      We recognise the reviewers' concerns regarding differences in response latency and articulatory demands between the naming and control conditions. Our analyses were response-locked to capture neural dynamics preceding articulation while accommodating variability in naming latency across trials and participants. We consider this alignment important for investigating language production processes, whose timing relative to stimulus onset may vary considerably.

      Nevertheless, we acknowledge that differences in response latency may result in the two conditions sampling different periods relative to stimulus presentation. We will examine the potential influence of this temporal difference through complementary analyses and clarify the rationale and limitations of the response-locked approach. We will also consider the potential contribution of differences in articulatory preparation between conditions when interpreting the findings.

      Interpretation of low-frequency activity

      We agree that the observed low-frequency effects warrant consideration of an alternative explanation involving transient evoked activity rather than sustained theta oscillations. We will revisit the interpretation of these findings in light of the potential contribution of transient evoked activity, drawing on our existing analyses and considering additional controls where appropriate.

      Statistical modelling and stimulus characteristics

      We will also revisit the statistical modelling of trial-level behavioural associations, including the potential contribution of item-level variability. We recognise the reviewers' suggestion to examine psycholinguistic properties of the naming stimuli and will assess whether the available stimulus characteristics permit informative supplementary analyses, while acknowledging that the task was not designed to independently manipulate these variables.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      This manuscript asks how the uterine lumen is remodeled across the peri-implantation window and whether this remodeling is functionally linked to embryo attachment and subsequent pregnancy establishment. The authors combine whole-organ three dimensional imaging of optically cleared mouse uteri with single-cell and spatial transcriptomic profiling, conditional deletion of p38α at the uterine-wide versus epithelial-restricted level, and rescue experiments using progesterone and leukemia inhibitory factor. Based on these datasets, the authors propose that the luminal epithelium undergoes a previously underappreciated phase of organ-scale architectural reorganization before attachment, and that a p38α-dependent stress responsive program coordinates epithelial remodeling together with epithelial-stromal communication required for implantation competence.

      Strengths:

      By moving beyond local attachment-site morphology to a horn-level representation of luminal topology, the work provides anatomical context that is difficult to reconstruct from conventional section-based approaches and should be broadly useful to the implantation community. The integration of organ-scale morphology with single-cell and spatial transcriptomic datasets, together with genetic perturbation and rescue experiments, adds breadth and increases the potential long-term utility of the dataset for investigators interested in uterine receptivity and embryo-uterine interactions.

      We thank the reviewer for the positive comments and constructive suggestions.

      Weaknesses:

      (1) The whole-uterus analysis of luminal folds and creases requires stronger methodological support. Given the mechanical compliance of the uterine lumen, it is difficult to evaluate from the current description whether dissection, fixation, clearing, and/or mounting could influence the observed luminal topography. This issue is particularly important because several key conclusions depend on the spatial distribution of folds across the uterine horn. A fuller account of tissue handling and reconstruction, together with validation that the preparation preserves native morphology, would substantially strengthen confidence in the organ-scale conclusions.

      We thank the reviewer for raising this important methodological concern.

      To address this concern, we have expanded the Methods section to provide a fuller description of tissue preparation, image acquisition, three-dimensional reconstruction, and quantitative analysis. Three-dimensional visualization of the uteri collected on days 1–4 and of implantation sites collected on days 5 and 6 was performed as previously described (PMID: 42022843). We have also clarified how representative cross-sectional images were selected from each reconstructed dataset and how identical analysis parameters were applied across samples.

      Specifically, three representative two-dimensional cross-sectional images were generated from each three-dimensional reconstructed dataset. From day 4 onward, sections were obtained at the position of the embryo and at positions ±500 μm from the embryo. For samples collected at earlier stages, sections were obtained at the midpoint of the image stack and at positions ±500 μm along the longitudinal axis. Epithelial staining area and branching features were then quantified from these cross-sectional images using the same analysis criteria for all samples. These methodological details have been added to the revised Methods section (Page 27, Line 619).

      In addition, to assess whether the whole-mount preparation preserved the overall luminal topography, we added representative transverse and longitudinal sections obtained using conventional two-dimensional histological analysis as Supplementary Fig. 1. The characteristic luminal morphology observed in these sections was comparable to that observed in the corresponding three-dimensional reconstructions. Although this comparison cannot completely exclude all possible effects of tissue processing, it supports the conclusion that the major morphological features identified by whole-organ imaging were not artifacts introduced by clearing, mounting, or reconstruction. The corresponding explanation has been added to the Results section (Page 8, Line 166).

      (2) Several of the central morphological claims are supported primarily only by representative reconstructions. This includes the proposed flattening/creasing dynamics, alternating stretched and shrunken regions, persistence of abnormal folding in the mutant uterus, and the extent of structural rescue following progesterone supplementation. The authors could extract objective measures from the reconstructed luminal surface and provide more statistical analysis to demonstrate the reproducibility of the results.

      We appreciate this constructive suggestion and agree that objective morphometric analyses are necessary to support the conclusions derived from the representative three-dimensional reconstructions.

      Quantitative analyses of luminal epithelial flattening during days 1–4, differences between p38α uterine control and knockout mice, and morphological changes following P4/LIF administration to p38α uterine knockout mice were already included in Figures 1d and 7c. In the revised manuscript, we have expanded the descriptions of these analyses and clarified the experimental units and sample numbers in the figure legends.

      We also performed additional quantitative analyses to characterize the alternating shrunken and stretched regions. We measured the orientation of luminal epithelial folds relative to the mesometrial–antimesometrial axis. In wild-type mice on day 4 at 20:00, folds in the regions surrounding embryos were predominantly vertically oriented, whereas folds at inter-implantation regions were predominantly horizontally oriented. These results provide an objective criterion distinguishing the areas that we refer to as “shrunken” and “stretched” and are now presented in Figure 2e.

      We performed the same analysis in control and p38α-deficient uteri and found that the spatially organized transition between vertically and horizontally oriented folds was disrupted in the mutant uterus. These results are now presented in Figure 7e and quantitatively support the persistence of abnormal luminal folding in p38α-deficient mice.

      In addition, we measured the angle of the luminal epithelium relative to the longitudinal uterine axis at three positions: the embryo center and positions 30 μm on either side of the center. The average of the three measurements was calculated for each biological sample. This analysis revealed a significant difference between day 4 at 20:00, before stable attachment, and day 4 at 24:00, after attachment, and is now presented in Figure 2f.

      Together with the existing measurements of epithelial area and branching features, these additional analyses provide quantitative support for the reproducibility of the luminal flattening, folding, and regional remodeling phenotypes. Nevertheless, we acknowledge that the reconstructed surface contains additional features, such as local curvature and fold depth, that could be examined in greater detail in future studies.

      (3) The manuscript appears to over-reach in concluding that luminal remodeling zones embryos before attachment from day 4 to 5. As presented, the data support a correlation between luminal architecture and embryo position, but do not discriminate between (i) luminal remodeling directing embryo positioning, (ii) embryos locally shaping the lumen, or (iii) parallel regulation of both. The evidence is based on observations of the uterus and the inside blastocysts at certain time points around implantation. Without the time-lapse analysis within the uterus, the dynamic interactions between embryos and the uterus couldn't be determined.

      We agree with the reviewer that our data demonstrate a strong spatial and temporal association between luminal architecture and embryo position but do not establish the direction of causality.

      Our analyses were performed at defined time points during the peri-implantation period and therefore cannot distinguish whether uterine luminal remodeling directs embryo positioning, whether embryos locally induce changes in luminal morphology, or whether both processes are coordinately regulated by common uterine and embryonic signals. As the reviewer correctly notes, direct determination of these dynamic interactions would require longitudinal or time-lapse imaging of embryos and the uterine lumen within the same animal.

      We have therefore revised the manuscript to moderate the causal language concerning embryo “zoning.” We now describe the findings as showing that regional luminal remodeling is associated with, and may contribute to, the spatial organization of embryos before attachment, rather than concluding that luminal remodeling directly determines embryo position. We have also added an explicit statement that the directionality of the interaction between embryo position and luminal remodeling remains unresolved in the present study. The relevant text in the Discussion has been revised accordingly (Page 19, Line 444).

      (4) The key conclusion of the manuscript is that uterine p38α regulates luminal epithelial remodeling required for embryo attachment, as shown in the title. Against this background, the finding that epithelial-restricted loss of p38α does not overtly impair fertility is notable, as it suggests that the major function of p38α may not be epithelial cell-autonomous but instead may arise through other uterine compartments that secondarily influence the epithelium. At present, however, this conclusion remains insufficiently supported: the epithelial-specific model is not characterized in sufficient depth during the peri-implantation period, and the transcriptomic evidence for altered epithelial-stromal communication does not by itself explain the phenotypic difference between uterine-wide and epithelial-specific deletion. If stromal p38α is proposed as the critical upstream regulator, more direct testing, such as stromal-specific deletion, would be needed.

      We thank the reviewer for highlighting this important point. We agree that the mild phenotype observed following epithelial-specific deletion of p38α argues against a solely epithelial cell-autonomous mechanism and that our current data do not directly demonstrate that stromal p38α is the exclusive upstream regulator of luminal epithelial remodeling.

      The uterine p38α knockout mice generated using Pgr-Cre lack p38α in multiple uterine compartments, including epithelial and stromal cells. To assess the contribution of epithelial p38α, we generated epithelial-specific p38α knockout mice using the Ltf-Cre driver. These mice did not exhibit the complete infertility or severe luminal remodeling abnormalities observed in the Pgr-Cre model and showed only mild uterine abnormalities. These results indicate that epithelial deletion alone is insufficient to reproduce the severe phenotype caused by broader uterine deletion of p38α.

      We have revised the Results and Discussion sections to describe the epithelial-specific knockout analysis more clearly and to distinguish between conclusions directly supported by the genetic models and the proposed mechanism of epithelial–stromal communication (Page 15, Line 344; Page 20, Line 459). We also clarify that stromal- or decidual-cell-specific deletion of p38α will be required to directly determine whether stromal p38α is necessary for luminal remodeling, embryo attachment, and subsequent embryo invasion. These experiments represent an important direction for future investigation.

      Reviewer #2 (Public review):

      Summary:

      In this study, the authors aimed to characterize the architectural reorganization of the uterine luminal epithelium during the implantation period. Using 3D histological reconstruction, single-cell RNA sequencing, and spatial transcriptomics, the authors characterize luminal remodeling during the peri-implantation period and employ a mouse model to explore the role of p38α in regulating luminal flattening.

      Strengths:

      This study clearly described the changes in luminal architecture during implantation. Moreover, they also used integration of multiple advanced techniques, including 3D tissue reconstruction, single-cell transcriptomics, and spatial transcriptomics, which together provide a detailed description of the molecular characteristics of the uterine architecture during implantation.

      We thank the reviewer for the positive comments and constructive suggestions.

      Weaknesses:

      The authors used PR-Cre to generate uterine p38α knockout mice. This Cre driver deletes p38α not only in epithelial cells but also in stromal compartments. Therefore, it remains unclear whether the observed phenotype arises from epithelial cells, stromal cells, or a combination of both. Previous studies have shown that p38α regulates epithelial polarity, cytoskeletal organization, and E-cadherin localization. However, the current study does not examine changes in cell adhesion or epithelial junction integrity. Previous studies have reported that uterine fluid absorption during implantation is closely associated with luminal closure and remodeling. It would be important to determine whether epithelial transport-related genes are altered in the mutant uterus. Could dysregulated fluid homeostasis contribute to the implantation defects observed in the p38α-deficient mice?

      We thank the reviewer for identifying these important mechanistic issues. We agree that the Pgr-Cre driver deletes p38α in multiple uterine compartments, including both epithelial and stromal cells, and therefore does not by itself establish which compartment is primarily responsible for the observed phenotype.

      To assess the contribution of epithelial p38α, we generated epithelial-specific p38α knockout mice using the Ltf-Cre driver. These results are presented in Supplementary Fig. S6. In contrast to the complete infertility and severe luminal remodeling defects observed in Pgr-Cre-mediated uterine p38α knockout mice, epithelial-specific deletion of p38α did not critically impair female fertility and caused only mild uterine abnormalities. These findings indicate that epithelial loss of p38α alone is insufficient to reproduce the severe phenotype observed in the Pgr-Cre model.

      We have revised the Results and Discussion sections to describe the Ltf-Cre analysis more clearly and to emphasize that the phenotype of the Pgr-Cre model is unlikely to result solely from epithelial-autonomous loss of p38α (Page 15, Line 344; Page 20, Line 459). Nevertheless, we agree that these findings do not directly establish stromal p38α as the exclusive upstream regulator. The phenotype may reflect the combined effects of p38α deletion in multiple uterine compartments and disrupted communication between epithelial and stromal cells. Direct testing using stromal- or decidual-cell-specific deletion will therefore be required to determine the precise contribution of stromal p38α.

      We also agree that epithelial adhesion, polarity, and cytoskeletal organization are relevant to the luminal remodeling phenotype. In the original study, we examined E-cadherin and β-catenin, which are associated with adherens junctions and epithelial polarity. In the luminal epithelium of day 4 p38α uterine knockout mice, staining for E-cadherin and β-catenin was stronger and more persistent than in control mice. These findings do not suggest a simple loss of epithelial junction integrity. Instead, they are consistent with impaired remodeling of adhesion- and polarity-associated epithelial structures during the peri-implantation period.

      We have revised the Results and Discussion sections to interpret these findings more explicitly in the context of epithelial adhesion and polarity. We now discuss the possibility that defective remodeling of epithelial junctional or cytoskeletal structures contributes to the persistence of abnormal luminal folding. However, because epithelial-specific p38α deletion did not reproduce the severe phenotype of the Pgr-Cre model, these epithelial abnormalities may arise, at least in part, from altered signaling between epithelial and non-epithelial uterine compartments rather than from an exclusively epithelial-autonomous defect.

      Finally, in response to the reviewer’s suggestion concerning uterine fluid homeostasis, we re-examined our RNA-seq dataset with a focus on genes associated with epithelial transport, barrier function, and fluid regulation. Several transport- and barrier-associated genes were altered in the p38α-deficient uterus, including Aqp3, Slc26a6, Cldn10, Gjb2, Trpv6, Trpm6, and Atp6v0a4. These genes are involved in processes such as water transport, ion transport, paracellular permeability, intercellular communication, and pH or ion homeostasis.

      These transcriptomic changes raise the possibility that dysregulated epithelial transport and fluid homeostasis contribute to defective luminal closure and remodeling in p38α-deficient mice. We have added this interpretation to the revised manuscript. However, because gene-expression analysis does not directly measure transporter activity, uterine fluid volume, or fluid absorption, our current data do not establish a causal relationship between altered fluid homeostasis and implantation failure. We have therefore presented this mechanism as a possibility and have added direct functional analysis of uterine fluid absorption and epithelial transport as an important direction for future study.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      The main need for the current manuscript is to apply greater analytical rigor and sharper framing.

      We thank the reviewer for the positive comments and constructive suggestions.

      (1) Provide a fuller description of dissection, orientation, fixation, clearing, mounting, acquisition settings, and reconstruction/segmentation criteria, including quality-control steps and exclusion criteria.

      Thank you for your advice. We added these sentences in the method sections (Page27, Line619). 3D visualization of the days 1–4 uteri or day 5 and 6 implantation sites was performed as previously reported (PMID 42022843).

      To quantitatively evaluate epithelial flattening morphology, three representative 2D cross-sectional images were generated from each 3D reconstructed dataset. Sections were collected at the site of embryo located and its ±500 μm positions on day 4 onwards, otherwise midpoint of the image stack and its ±500 μm positions along the longitudinal (x) axis. Epithelial staining area and epithelial branching features were subsequently quantified from these cross-sectional images using identical analysis parameters across samples.

      These detailed methods are now added into the revised manuscript.

      Add validation that the whole-uterus preparation preserves the luminal original physiological topography.

      We appreciate this advice. Representative transverse and longitudinal sections were added as Supplementary Fig. 1 to confirm that luminal morphology was comparable between conventional two-dimensional section analysis and three-dimensional evaluation. The main text was revised accordingly (Page8, Line 166).

      (2) Strengthen the support for the whole-uterus morphology data by adding quantitative morphometric analysis across biological replicates. Metrics related to fold density, epithelial branching, curvature, surface roughness, or related parameters would make the central morphological conclusions more rigorous.

      Thank you for this advice.

      Quantification of luminal flattening from days 1 to day 4 in wild-type mice, comparisons between p38α uCtrl and uKO mice, and the morphological changes induced by LIF/P4 administration in p38α uKO mice have already been presented in Figures 1d and 7c. We now added detailed explanation about these data.

      To further quantify the transition between shrunken and stretched areas in wild-type mice before and after embryo attachment, we quantified the angle of luminal foldings against M-AM axis, showing shrunken areas have vertical folding (around 0 degree) while stretched areas have horizontal folding (around 90 degree) on day 4 20:00 (Figure 2e), which were dysregulated in p38α-deleted uteri (Figure 7e). We additionally measured the angle of the luminal epithelia against the longitudinal axis at three positions (the embryo center and ±30 μm from the center) using ImageJ. The average of these three measurements was calculated for each sample (n = 3). This analysis revealed a significant difference between day 4 20:00 (pre-attachment) and day 4 24:00 (post-attachment) (Figure 2f), indicating that embryo location is moved in alignment with the time course.

      (3) Define the experimental unit clearly in each quantitative analysis. In several panels, it is not fully clear whether n refers to animals, uterine horns, implantation sites, sections, or embryos.

      Thank you for pointing this out. Now the definition of n has been clarified in the figure legend.

      (4) The causal language around embryo zoning should be moderated unless additional evidence can be provided. As written, the data support a strong association between luminal architecture and embryo position, but not yet a directional mechanism.

      Thank you for this opinion. According to this suggestion, we have revised the Discussion to avoid overstating this conclusion (Page19, Line 444).

      (5) Figure presentation should be revised for consistency and clarity. For example:- Scale bars and their labeling should be standardized throughout.

      - In Figure 4e, the representative uterine photographs do not appear to be shown at a fully matched scale between each other.

      - In Figure 4f, the control and mutant three-dimensional views appear to be displayed from different angles, which makes comparison of crypt formation and depth more difficult. As these are three-dimensional datasets, matched viewpoints should be feasible.

      - Figure 9c appears to be mislabeled. The panel is labeled as β-actin, but based on the main context, this should be β-catenin.

      Thank you for pointing this out. We have corrected Figures 4e, 4f, and 9c as suggested.

      (6) The apparent reuse of the uKO image between Figures 4e and 5h should be clarified. If the same image is intentionally reused, this should be stated explicitly; otherwise, a different representative image would be preferable.

      Thank you for pointing this out. As you indicated, the same image had been inadvertently reused. We sincerely apologize this mistake and have replaced it with an alternative representative image in figure 5h.

      (7) Please check the figure legends and Methods carefully for internal consistency, including panel labels, marker names, genotype names, sampling time points, and nomenclature.

      Thank you for your advice. We have standardized the notation of gene names, protein names, and other terminology throughout the manuscript.

      (8) The Methods should include a clear description of the epithelial-specific p38α deletion model.

      We apologize for the lack of explanation. We have added a description of how the epithelial-specific p38α knockout mice were generated in the Methods section.

      (9) The manuscript requires thorough editing for language and presentation. For example:

      - From line 53 to 5: "In the uterus, proliferation-differentiation switching (PDS), indicating the inhibition of epithelial proliferation with induction of stromal proliferation in the endometrium, is evident on day 4 under the continuous influence of P4, resulting in the endometrium acquiring implantation potential."

      - From lines 257 to 261, the content of two consecutive sentences is repeated: "Based on these results, we examined whether activation of Lif-Stat3 can restore the flawed embryo attachment in p38α uKO. These results prompted us to determine whether supplementation of Lif along with P4 can ameliorate abnormal implantation in p38α uKO.

      Thank you for your valuable advice. We have revised the sentences accordingly and further refined the manuscript through professional English editing.

      Reviewer #2 (Recommendations for the authors):

      (1) The authors used PR-Cre to generate uterine p38α knockout mice. This Cre driver deletes p38α not only in epithelial cells but also in stromal compartments. Therefore, it remains unclear whether the observed phenotype arises from epithelial cells, stromal cells, or a combination of both. An epithelial-specific deletion model would help clarify the cell-type-specific role of p38α in luminal remodeling.

      We thank the reviewer for raising this important point. We agree that Pgr-Cre deletes p38α in multiple uterine compartments, including epithelial and stromal cells, and that this point should be clearly addressed when interpreting the phenotype.

      To clarify the contribution of the epithelial compartment, we have already generated and analyzed epithelial-specific p38α knockout mice using the Ltf-Cre driver. These data are shown in Supplementary Fig. S6. In contrast to the complete infertility and severe luminal remodeling defects observed in Pgr-Cre-mediated uterine p38α knockout mice, epithelial-specific deletion of p38α did not critically impair female fertility and caused only mild uterine abnormalities. Thus, epithelial deletion alone is not sufficient to recapitulate the severe phenotype observed in the Pgr-Cre model.

      We agree that this point was not sufficiently emphasized in the original manuscript. We have therefore revised the Results and Discussion sections to explicitly describe the Ltf-Cre analysis and to clarify that the severe phenotype in Pgr-Cre mutants is unlikely to arise solely from an epithelial-autonomous loss of p38α. Instead, our data support a model in which p38α in non-epithelial uterine compartments, particularly the stroma, contributes to luminal epithelial remodeling through epithelial–stromal communication.

      We have also softened the wording to avoid implying that the Pgr-Cre model alone definitively identifies the stromal compartment as the exclusive source of the phenotype. Rather, the combination of the Pgr-Cre phenotype, the mild Ltf-Cre phenotype, and the single-cell/spatial transcriptomic analyses supports a critical role for p38α-dependent epithelial–stromal crosstalk in establishing implantation-competent luminal architecture.

      We now added explanations regarding eKO in the result sections (Page15, Line344) as well as Discussion sections (Page20, Line459)

      (2) Previous studies have shown that p38α regulates epithelial polarity, cytoskeletal organization, and E-cadherin localization. However, the current study does not examine changes in cell adhesion or epithelial junction integrity. The authors should evaluate markers of cell adhesion and polarity and discuss whether the observed phenotype could result from impaired epithelial junctions or altered cytoskeletal organization.

      We agree with the reviewer that epithelial adhesion, polarity, and cytoskeletal organization are important potential mechanisms underlying the luminal remodeling phenotype. In the original manuscript, we examined E-cadherin and β-catenin, both of which are associated with adherens junctions and epithelial polarity. We observed stronger and more persistent staining of these markers in day 4 p38α uKO luminal epithelium compared with controls, suggesting impaired remodeling of epithelial adhesion/polarity-associated structures rather than a simple loss of epithelial junctions.

      We have revised the Results and Discussion sections to explicitly describe these data in the context of epithelial adhesion and polarity. We further discuss that altered junctional or cytoskeletal remodeling may contribute to the persistent luminal folding phenotype. However, because epithelial-specific p38α deletion using Ltf-Cre did not reproduce the severe phenotype of Pgr-Cre-mediated uterine knockout mice, we interpret these epithelial abnormalities as likely arising, at least in part, from disrupted epithelial–stromal communication rather than from an exclusively epithelial-autonomous junctional defect.

      (3) Previous studies have reported that uterine fluid absorption during implantation is closely associated with luminal closure and remodeling. It would be important to determine whether epithelial transport-related genes are altered in the mutant uterus. Could dysregulated fluid homeostasis contribute to the implantation defects observed in the p38α-deficient mice?

      We thank the reviewer for this thoughtful suggestion. As the reviewer noted, uterine fluid absorption and epithelial transport are important processes associated with luminal closure and remodeling during implantation.

      In response to the reviewer’s suggestion, we re-examined our RNA-seq dataset with a focus on genes related to epithelial transport and fluid homeostasis. We found that several transport- and barrier-associated genes were altered in the P4/LIF-untreated p38a-deficient uterus, including Aqp3, Slc26a6, Cldn10, Gjb2, Trpv6, Trpm6, and Atp6v0a4. These genes are associated with water transport, ion transport, paracellular permeability, epithelial communication, and pH/ion homeostasis. These findings suggest that dysregulated epithelial transport and fluid homeostasis may contribute, at least in part, to impaired luminal closure/remodeling and implantation defects in the mutant uterus.

      We have added this point to the revised manuscript. Nevertheless, because transcriptomic data do not directly measure transporter activity or uterine fluid dynamics, further functional studies will be required to determine whether altered fluid absorption directly contributes to the abnormal luminal architecture. We have revised the Discussion to acknowledge this limitation and to propose direct functional analysis of uterine fluid absorption and epithelial transport as an important future direction.

      (4) It is intriguing that P4 plus LIF supplementation rescues embryo attachment, but pregnancy still fails at later stages. The authors should discuss whether this defect might result from p38α deletion in stromal cells or from persistent abnormalities in luminal remodeling.

      Thank you for your advice. It is difficult to determine from the current study whether the observed phenotype is primarily caused by persistent luminal epithelial abnormalities or by stromal p38α deficiency. In the present study, P4 and LIF supplementation restored embryo attachment in p38α uKO mice; however, embryo invasion remained completely absent, resulting in subsequent pregnancy failure. Previous studies from our group have shown that uterine deficiency of Hif2α, Rb1, Ezh2, or Lox impairs embryo invasion and leads to pregnancy failure, highlighting the importance of coordinated epithelial–stromal remodeling during implantation (PMID: 41803091, 3719814, 2012472, 33399260). In the p38α uKO uterus, although P4 and LIF supplementation restored key molecular signals required for attachment, abnormalities in luminal morphology persisted. Therefore, persistent defects in luminal remodeling may contribute to the failure of embryo invasion and subsequent pregnancy progression. However, because embryo attachment is severely impaired in untreated p38α uKO mice, the post-attachment role of stromal p38α cannot be directly assessed in the current model. Further studies using decidual cell-specific genetic approaches will be required to clarify the contribution of stromal p38α to embryo invasion. We added these sentences in the discussion sections.

      (5) The terminology describing luminal morphogenesis requires clarification, particularly the definitions of "shrunken areas" and "stretched areas." These terms should be clearly defined and, if possible, supported by quantitative criteria

      Thank you for your suggestion. To quantify the transition between shrunken and stretched areas in wild-type mice, we measured the angle of luminal folding around the embryo (±500 µm) as well as inter-implantation sites on day 4 2000h using ImageJ. This analysis revealed the epithelia around the embryos are more shrunken with vertically oriented folding compared to inter-implantation sites (Figure 2e). We similarly analyzed uteri from control and p38α uKO, and found uKO poorly formed shrunken and stretched areas, which may compromise embryo implantation in this milieu (Figure 7e).

      (6) The exact collection time points for day 4 and day 5 uteri should be clearly specified (Line 169), as implantation-related changes are highly time-dependent.

      Thank you for your advice. We have added “10:00” to both day 4 and day 5.

      (7) The manuscript relies heavily on qualitative visual comparisons of luminal morphology. The authors should provide quantitative morphometric analyses, such as measurements of lumen width, epithelial curvature, or fold depth, to support their conclusions.

      Thank you for your suggestion. To quantify the transition between shrunken and stretched areas in wild-type mice before and after embryo attachment, we measured the angle between the LE folding adjacent to the embryo and inter-implantation sites against the M-AM axis. The corresponding results have been added to the manuscript (Figure 2e and 7e).

    1. Author response:

      We thank the editors and reviewers for their careful evaluation of our manuscript and their constructive comments. We are pleased that the reviewers found the identification of a sterol-binding cavity in ABCG5/G8, the stronger stimulation of ATPase activity by ergosterol, and the role of ABCG5<sub>Y432</sub> in differential sterol activation to be of interest to the greater transporter community.

      Reviewer #1:

      (1) We agree that cholate should be considered, as it was present throughout protein purification. We acknowledge that at the current resolution, the identity of the bound ligand cannot be determined unambiguously from the cryo-EM density alone, particularly among sterol-like molecules of similar size and shape. For this reason, we described the cavity as a potential sterol-binding site and ergosterol as the most likely ligand and did not rely on the structure alone to define sterol-protein interactions through this cavity. Here, we combined ligand fitting, molecular dynamics simulations, site-directed mutagenesis, and in vitro functional assays to evaluate the role of this cavity in sterol selectivity. In the revision, we will fit cholate into the density, compare its fit with those of ergosterol, cholesterol, and CHS, and include MD simulation data for cholate as described for these molecules. Furthermore, previous studies showed that cholate only contributed to the basal ATPase activity [1, 2], so we will include ATPase data for the ABCG5<sub>Y432F</sub> mutant under sterol-free conditions and compare it with WT under the same conditions, since our assays included cholate.

      (2) In the current manuscript, we discuss how the hydroxyl group of Y432 may provide an additional interaction capability within the binding cavity. In the revision, we will add a discussion of the chemical differences between ergosterol and cholesterol, including the double bond in the B ring and the additional double bond and methyl group in the side chain, and how these features may favor interactions with the Y432 hydroxyl and aromatic ring.

      (3) We agree that the overall fold is similar to previous ABCG5/G8 structures. We want to clarify that this is the first structural evidence showing a non-cholesterol bound to the central cavity and its link to sterol-specific activation of the transporter’s catalysis.

      (4) The ligand RMSD values were calculated relative to the docked starting poses. Because the systems underwent equilibration and the first 25 ns of each production simulation were excluded from analysis, the ligands had already relaxed from their initial poses at the start of the analyzed trajectories, which explains why the values do not start at zero and differ among sterols. We will clarify this in the Methods and figure legend in the revision.

      (5) We thank the reviewer for this suggestion. The basal activity of WT ABCG5/G8 is currently shown in Figure 3A. In the revision, we will measure the basal activity of ABCG5<sub>Y432F</sub> under the same sterol-free conditions and add both WT and Y432F sterol-free controls to Figure 3B for direct comparison.

      (6) We agree that sterol acts as an activator rather than the directly measured substrate in this assay. In the revision, we will describe these data (Figure 3D and Table 1) as sterol-dependent activation curves and report apparent EC50 and maximal activity values in place of Km and Vmax.

      (7) We thank the reviewer for bringing up this important point. In the original submission, Fig. 2C shows per-residue MMGBSA decomposition as the mean +/- SD of three independent replicates. We performed a Welch’s t-test for all three pairs with a Benjamini-Hochberg FDR for all 48 comparisons, the residues which had mentioned were in direction but were not statistically significant. This remains relevant since our simulations showed that in all replicates, CHS would move away from the docked site which explains why the standard deviations for the MMGBSA calculations were so large. We equally re-analyzed each trajectory from the point where CHS’s RMSD stabilized which equally yielded large SD binding free energy decomposition, however, no residues passed the BH FDR. For this reason, we will modify our language within the text to reflect the comparisons between sterol groups as trends rather than significant differences.

      (8) We agree that these side chain differences are small relative to the resolution of the structures. We will revise the text to describe them more cautiously.

      (9) We agree that the proposed role of the surface-exposed site in sterol flip-flop is speculative. The model is based on the cholesterol molecule observed at the ABCG8 to ABCG5 transmembrane interface in our previous crystal structure (PDB ID: 8CUB) [3]. We discuss this site as having a possible role in sterol sensing and regulation or in sterol movement between membrane leaflets, as suggested for other ABC transporters [4]. We acknowledge that neither role is directly tested in this study. In the revision, we will rephrase this section, clearly present both possibilities as hypotheses for future investigation, and revise Figure 4B and its legend to indicate that it represents a proposed model.

      (10) AMPPNP and MgCl<sub>2</sub> were included to match the conditions under which we previously obtained a cholesterol-bound structure of ABCG5/G8 [3]. Our aim was to capture the sterol-bound state of the transporter rather than an ATP hydrolysis or nucleotide-bound closed state. Consistent with our previous structure, no nucleotide density was observed in the nucleotide binding sites, and the transporter adopted an inward-facing conformation. We will clarify this rationale in the Methods of the revised manuscript and discuss possible role of nucleotide in this report.

      Reviewer #2:

      We agree that additional structures and mutants would further strengthen the mechanistic model, and we will discuss these as directions for future work. We will also expand the Discussion on the physiological relevance of differential sterol recognition by ABCG5/G8, including dietary non-cholesterol sterols.

      Reviewer #3:

      (1) We agree that the observed side chain differences should be interpreted with caution given the resolution. We will revise the text to avoid attributing mechanistic significance to these localized variations beyond what is supported by our mutagenesis and functional data.

      (2) We agree that the present study does not provide new experimental or computational evidence that the CRL site represents an intermediate in sterol flip-flop. This model is based on the cholesterol-bound site observed in our previous crystal structure (PDB ID: 8CUB) [3], and in the current manuscript we present it as one of two possible roles for this site, alongside sterol sensing or regulation. In the revision, we will state the basis of the model more clearly, present both possibilities as hypotheses for future investigation, and revise the related text and Figure 4B accordingly (see also our response to Reviewer #1, point 9).

      We look forward to submitting a revised manuscript that addresses these points.

      References:

      (1) B. M. Xavier, A. A. Zein, A. Venes, J. Wang, J. Y. Lee, Transmembrane Polar Relay Drives the Allosteric Regulation for ABCG5/G8 Sterol Transporter. International Journal of Molecular Sciences 2020, Vol. 21, Page 8747 21, 8747 (2020).

      (2) B. J. H. Johnson, J. Y. Lee, A. Pickert, I. L. Urbatsch, Bile acids stimulate ATP hydrolysis in the purified cholesterol transporter ABCG5/G8. Biochemistry 49, 3403–3411 (2010).

      (3) D. Farhat, F. Rezaei, M. Ristovski, Y. Yang, A. Stancescu, L. Dzimkova, S. Samnani, J. F. Couture, J. Y. Lee, Structural Analysis of Cholesterol Binding and Sterol Selectivity by ABCG5/G8. J. Mol. Biol. 434, 167795 (2022).

      (3) S. Thangapandian, K. Kapoor, E. Tajkhorshid, Probing cholesterol binding and translocation in P-glycoprotein. Biochimica et Biophysica Acta (BBA) - Biomembranes 1862, 183090 (2020).

    1. Author response:

      eLife Assessment

      This study presents an open-source reinforcement learning framework for the real-time, closedloop optimization of spatiotemporal electrical stimulation in engineered neuronal networks. Using single-spike-resolution activity as continuous feedback, the authors provide solid evidence that their platform can identify stimulation patterns that drive specific activity motifs within a structurally constrained four-node circuit. While this reproducible system offers a valuable and accessible tool for interacting with biological neural networks in an adaptive manner, further validation is needed to determine how well these stimulation strategies generalize to larger, unstructured, or more conventional network architectures.

      We thank the editors and reviewers for their kind and insightful words, as well as their constructive feedback and assessment. We agree that in its current stage, the manuscript does not convincingly argue, that specific stimulation strategies applied to one network generalise well to other network architectures. We intend to address this problem by adjusting the focus of the manuscript to be more on the platform than on any specific neuroscience claim, as we believe that this is the more useful angle for the community at large. We also intend to discuss the transferability of our results between the presented culture system and other neuroscience systems.

      Based on the reviewer comments, we will further give a more approachable introduction to reinforcement learning to make the concept more accessible to a wider audience. We will also motivate the algorithm selection in more depth.

      In the following, we will discuss the comments put forward by the reviewers and how we intend to adapt our manuscript to address them. In this provisional response, we will only focus on major concerns. Minor comments, where we are following the suggestions made by the reviewers directly, will not yet be discussed.

      Reviewer #1 (Public Review):

      The manuscript appears undecided about whether it wants to be about RL control, about a technical implementation of long-term stimulation in vitro, or about the properties of neuronal networks and interaction with them. The introduction is well written, comprehensive and insightful, focusing on biological aspects. Methods are then extensively about RL algorithms, without explaining why several were used or why these in particular, but with specialist language hard to understand for neuroscientists. The results then quantitatively compare the performance of the RL but do not really explain what this teaches us about neuroscience or what we learn about the networks beyond that they can be stimulated for longer propagation patterns. Extensive supplementary material almost advertises the hardware built by the team. Some figures suggest, though I’m not 100% certain about this, that different algorithms find different optimal stimulation patterns in the same network - which I find puzzling. What then does this tell us about the stimulation patterns and the variability of the responses?

      We thank the reviewer for pointing out these issues with our manuscript. The goal of our work is the hardware framework. We plan to highlight this more in the revised version. The RL part will be revised with less specialist language and will get less emphasis in the next version of our manuscript. We will also discuss why different algorithms seem to find different solutions, which can be traced back to having different networks and agents finding different local maxima.

      By clearly setting the scope of our manuscript on the hardware aspects and revising the RL part to be seen more as one possible closed-loop control paradigm, we further intend to address the concerns put forward by the reviewer regarding our focus on RL in other parts of the manuscript.

      Reviewer #2 (Public Review):

      An important limitation is that the framework was evaluated using a relatively small and highly structured network. Four stimulation electrodes were positioned around a single network, and stimulation was delivered to microchannels in which axons were concentrated. This configuration is well suited to the initial demonstration, but it remains uncertain whether the same approach will perform similarly in conventional monolayer dissociated cultures, larger networks, or systems with different numbers and spatial arrangements of electrodes. Additional validation across a broader range of network structures and experimental configurations would therefore be needed to establish the general applicability of the framework.

      We thank the reviewer for their feedback. They are right to point out that the manuscript here focuses purely on small and highly structured networks. With the presented experiments, our manuscript does not and cannot make any biological claims about how neurons communicate. However, with this manuscript, we also do not intend to do so, as such an endeavour would be out of scope. In the next version of our manuscript, we will better highlight the focus of our manuscript, which lies on the hardware framework itself. Furthermore, we will discuss in the outlook the generalisability and scalability concerns raised by the reviewer in more detail.

      Reviewer #3 (Public Review):

      Several aspects of the analysis and interpretation require further clarification. In particular, the definition and computation of directional propagation and reward are not always clear. The generalizability of the optimized stimulation patterns across cultures also remains unclear.

      We thank the reviewer for their insightful feedback. We agree with them and will discuss (1) the currently implemented reward based on directional propagation of activity and (2) the limitations and aspects influencing reward algorithm selection in more detail in our revised version of the manuscript. We further believe that we cannot make any claims about generalisability between cultures or when changing the experimental paradigm.

    1. Author response:

      The following is the authors’ response to the previous reviews.

      In this revision we have addressed all the reviewer comments, most particularly we acknowledge that our calculations and understanding of calcium levels were incorrect, and have revisited all sections of the paper affected by this. We have performed numerous additional analyses on data, rerun many calculations with low-Calcium versions of models, and have restructured several figures and text. In brief, here is an overview of the changes in this revision:

      Changes regarding Calcium levels.

      (1) We have referred to the literature for short-term plasticity effects over a range of concentrations for bath calcium, both in glutamatergic and GABAergic synapses in the hippocampus. By interpolation, the increase of PPR when going from 2 to 1.35 mM is below ~20%.

      (2) We used 1.35 mM external Calcium in revised presynaptic neurotransmitter release models, and show that both glu and GABA models follow the same direction of change as seen in experiments at lower Calcium.

      (3) We have rerun the key calculations using these updated synaptic models and show that mismatch detection remains intact, but its strength is diminished, at 1.35 mM calcium.

      Changes regarding use-dependent decrease in CA3 field responses:

      (4) We have performed additional analysis on recordings to show that the decline in CA3 field response over the 32 pulses of the mismatch trials is under 30%, and that the mismatch responses are present even when this decline has saturated.

      (5) Additional simulations without ChR2 desensitization show no effect on mismatch selectivity.

      Changes regarding analysis of jitter:

      (6) We have performed extensive additional simulations to better characterize and analyze the effects of jitter on mismatch selectivity.

      Changes regarding reliability of spiking:

      (7) We have added a section referring to our previous work using a similar protocol (Bhatia et al., eLife 2019), where we see a range of spiking probabilities from recorded CA3 neurons. We also refer specifically to our previous analysis which set tight limits to the number of spikes per light pulse. We present our interpretation of how this affects mismatch detection.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      This study uses optogenetics to activate CA3 while recordings from CA1 neurons and characterizing the excitation/inhibition (E/I) balance. They observe use-dependent alterations in the E/I balance as a result of STP and they develop a model to describe these observations. This is a very ambitious paper that deals with many issues using both experimental and modeling approaches.

      Strengths:

      This paper examines important principles regarding the manner in which synaptic circuitry and use-dependent synaptic plasticity can transform inputs and perform computations.

      Weaknesses:

      There are three issues that cause concern regarding the applicability of their slice recordings to physiological conditions and that make some aspects of their results difficult to interpret. First, they state that 2 mM added external calcium mimics calcium levels in CSF, but this is not the case. This will influence the plasticity they observe.

      We agree that our calculations and understanding of calcium levels were incorrect. We have addressed this issue by referring to the literature in which external Ca is varied while measuring PPR.. From experiments by Blatow et al and Kravachenko et al we estimate that the PPR is ~20% higher at 1.35 mM external Ca than at 2mM, both for Glu and GABA synapses, but note that their experiments used a different set of conditions than ours. Based on this, we redid our synaptic plasticity models for Glu and GABA, reran our calculations and confirmed our core prediction of mismatch detection. We have added the following text to the introduction:

      “While most studies on synaptic plasticity utilize 2mM external Ca2+ (extCa) this is substantially higher than physiological Ca2+ (1.2 to 1.5 mM) and has been shown to significantly alter plasticity outcomes. Long-term plasticity is particularly sensitive to elevated extCa levels (Inglebert et al. 2020). There are significant but smaller changes in short-term plasticity in several systems, wherein lower extCa leads to a) higher paired pulse ratio (PPR) and b) lower EPSCs (Rat hippocampal culture: (Sippy et al. 2003), Calyx of Held: (Thanawala and Regehr 2013; Bernal-Correa et al. 2026; Lorteije et al. 2009), Mouse hippocampal slice: (Blatow et al. 2003)). Specifically, in hippocampal CA3->CA1 glutamatergic synapses at 1.5 mM extCa the paired-pulse ratio is 15% larger than at 2mM (Blatow et al. 2003). In primary hippocampal neuronal culture, inhibitory synapses also undergo a 50% increase in paired-pulse ratio at 0.5 mM compared to 2 mM extCa (Kravchenko et al. 2006). By linear extrapolation/interpolation both these results suggest a PPR increase of ~20% at 1.35 mM extCa compared to the conventional 2 mM. In the current study we extend our simulations into the physiological domain of extCa to check consistency of the predicted computational outcomes.”

      Also, from the methods:

      “Model tuning for physiological conditions

      We implemented two sets of changes to build a distinct presynaptic model which more closely matched physiological conditions. First, we increased the rates of all the reaction steps in the E and I presynaptic model by 40%, with the assumption of a 3.5℃ rise in temperature and a doubling of rates every 10℃ (Q10 of 2). Second, we lowered the calcium influx during stimulus by a factor of extCa/defaultCa = 1.35mM/2.0mM, again both for E and I. This effectively halves synaptic release (Figure 4-figure supplement 8, compare panels A and B), which we compensated for by a simple doubling of synaptic weight, both for E and I.

      It also causes an increase in STP levels compared to the reference 2.0 mM extCa model. We confirmed that these changes were qualitatively similar to those expected from experiments over a range of extCa levels (Kravchenko et al. 2006; Blatow et al. 2003). However, several features in these earlier experiments differed from ours: the inter-pulse intervals, the preparation, and the temperature. Accordingly, rather than paste in their numbers of ~20% increase in STP in E and I, we used the 37℃ and 1.35mM extCa variant of our model for additional simulations.”

      Second, they indicate that there is a 2% decrease in activated fibers per stimulus and attribute this to ChR2 desensitization. Such use-dependent decreases in fiber activation are expected to build during their repetitive activation experiments and artifactually influence their results.

      The reviewer correctly points out that there would be a substantial decrease in fiber activation if the 2% decrease per pulse extended linearly over the entire train of ~200 pulses in the Poisson train or 32 pulses in the mismatch experiments/models. Clearly this does not happen, as the EPSPs settle rapidly to a steady range in both cases (Figure 6A, E, Figure 7 E). We acknowledge that the original statement implied a large decrease, and have added the clarificatory line around Figure 1:

      “We attribute this to ChR2 desensitization, however in longer pulse trains this levels out as we discuss below.”

      To quantitatively address the concern about decline of activation, we have performed an additional analysis to estimate how fiber activation evolves over multiple pulses. For the Poisson train experiments, we used our measured field potentials over the entire train (Figure 6-figure supplement 2) and saw that the level flattened out after ~2 seconds (~40 pulses). For the mismatch experiments, the mean fEPSP flattens with a time course of ~0.8 seconds and even at 50Hz the decrement is only about 30% of the initial value (Figure 7-Figure Supplement 2). Thus the field readouts show that the saturating level of use-dependent decrease is small. From the text around Figure 7:

      “We observed this mismatch selectivity despite the reduction in inputs due to ChR2 desensitization over the long 32-pulse train. To estimate this reduction, we measured the field EPSP in the CA3 during the optical stimulation, and fitted an exponential decay function to the peaks (Figure 7-figure supplement 2). We find that the largest decay was ~30% of the initial fEPSP. The fEPSP decayed over a wide range of time courses, with median around 800ms. We estimate that the recovery time from ChR2 desensitization was around 150ms, again highly different between slices (Figure 7-figure supplement 2). Thus the mismatch detection was largely robust to ChR2 desensitization effects over the pulse train.”

      Thus, we do not expect any qualitative effect of ChR2 desensitization on our results for the following reasons. First, the mismatch experiments themselves take place under the conditions of this fibre activation decay, yet yield numerous cases of mismatch selectivity (Figure 7Eiii, Fi). Second, the simulations for mismatch (Figure 7,9) explicitly included ChR2 desensitization, and they too exhibit mismatch selectivity. Third, in this revision we have added a simulation for mismatch selectivity in the absence of ChR2 desensitization (Figure 9 panel E). There is no statistically significant difference from the reference model with ChR2 desensitization.

      Third, they do not know the responses of individual CA3 cells to stimulation. They do not know if each cell fires reliably during repetitive activation and whether each cell only fires once.

      We acknowledge that we collected limited data on this in the current dataset, because this analysis has already been published. In our previous work using a similar preparation we have characterized CA3 pyramidal neuron responses to grid optical stimuli in the CA3 (Figure 1b, e, g, Bhatia, Moza and Bhalla 2019) in response to the light pulse. These recordings show that cells fire with probabilities over a wide range from zero to one, but these firing probabilities are reliable over multiple trials. In this revision we have clarified this point:

      “Notably, the distribution of field amplitudes was tight (Figure 1E, Figure 1-figure supplement 2F), more so than the distribution of the corresponding EPSPs (Figure 1H). Together with previous work using a similar optical stimulus system and intracellular CA3 recordings (Bhatia et al. 2019), we interpret this to say that the spiking responses from CA3 neurons to optical stimuli were consistent from trial to trial.”

      Regarding number of action potentials: In the previous revision we had examined field data from our recordings to characterize the occurrence of multiple spikes (Figure 1-figure supplement 2). Second field peaks were common, at about 40% of the amplitude of the first, and within ~3.5 ms of the first peak. Third peaks were much smaller. From the text adjacent to Figure 1:

      We observed a small amount of ‘ringing’ of the field response which we interpret as either CA3 spiking in a burst, or recurrent activation of the CA3 neurons (Figure 1-figure supplement 2). The second peak was ~40% of the first, within 4 ms of the first. The ringing was down to ~5% by the third peak which occurred within ~9 ms of the flash. This sets an upper bound to any contribution to patterns by recurrence or multiple spikes during a ChR2 flash.

      On the basis of these field responses and previous reports (Bhatia et al. 2019), we infer that the CA3 neuron response to optical input was a brief event, with reliable probability of a spike on any given flash, and typically having one or occasionally two spikes within 6 ms of the light flash.

      Reviewer #3 (Public review):

      Summary:

      This work shows experimentally and computationally that single CA1 neurons can perform mismatch detection on patterned CA3 inputs and that STP and EI balance underlie this detection.

      Strengths:

      It has been known that STP can enhance the EPSP when the corresponding presynaptic input exhibits abrupt changes in firing rate. This work provides experimental evidence and further computational support for the hypothesis that the basic computation through STP is useful for detecting abrupt changes in the spatial pattern of synaptic inputs at the Schaffer collaterals. Further, their results indicate the novel view that mismatch detection is most efficient when gamma-frequency bursting inputs exhibit mismatches between theta cycles. The authors included novel results in the revised manuscript to show that the effective frequency range of gamma oscillation is broad, including both slow and fast gamma bands.

      In the initial submission, the dependence of mismatch detection performance on model parameters and experimental settings, such as pattern overlaps and other network parameters, was not sufficiently explored. In the revised manuscript, the authors extensively studied these points and summarized the novel results in Fig. 9. Furthermore, the authors clarified that jitters in input spikes can improve detection performance in some cases. These results show the robustness of their results against variations in external and internal conditions.

      Weaknesses:

      While this study shows an intriguing example of combined experimental and computational studies, some analytic results, for instance, regarding the complex contributions of jitters to detection performance, could have clarified the underlying mechanism deeper and further strengthened the manuscript.

      We acknowledge that the outcome of the jitter calculations looked complex. We redid this with substantially more repeats (30 simulated networks projecting to a CA1 neuron, rather than the original 6) and performed a cell-wise bootstrap analysis for error estimates for mean selectivity for each condition. This larger sample resulted in a smoother distribution of mismatch selectivity over different frequencies (Figure 7). We have carried out a further set of simulations over a range of jitter widths (Figure 7-figure supplement 3). We have added these findings to the paper:

      “We next asked how sensitive the mismatch detection was to spike jitter, since in-vivo neural activity has a distribution of spike timings. We reran our model with 30 distinct simulated networks projecting to a CA1 neuron, each for a range of jitter values from 0 to 10ms. We performed a cell-wise bootstrap analysis to obtain error estimates for mean selectivity for each condition. We find that for 5-square stimuli selectivity is high at 0 jitter for all frequencies, but surprisingly for 15-square, selectivity is higher when jitter is nonzero (Figure 7-figure supplement 3). We suggest that when synaptic inputs are synchronous their effects add sublinearly, so some degree of jitter causes larger EPSPs when there are many inputs, as in the 15-square case. Consistent with this, the centroid for selectivity was always at a higher jitter level for 15-square than for 5-square (Figure 7-figure supplement 3, bootstrap test, p < 0.001).

      For the 50-Hz stimulus, a 10ms jitter is half the stimulus interval, so the onset of patterns are quite smeared. Thus, as expected, selectivity fell both in 5 (bootstrap p<0.001) and 15-square (bootstrap p=0.005) cases for 50 Hz when jitter was larger than 4 ms. (Figure 7-Figure supplement 3).”

      While we appreciate that a further analytic examination of jitter would be interesting, we feel that it would have to be done on a much reduced system compared to ours, and is therefore outside the scope of the current paper.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      The authors primarily responded with words rather than experiments. Their response has been adequate for some issues, but I remain concerned about their methods and how they could impact their own results, and how they might lead others astray.

      (1) The paper by Klyachko and Stevens (2006) does a good job of addressing the temperature issue.

      (2) The issue of free calcium is important. They provide a calculation that says that 2 mM added calcium corresponds to 1.27 mM free calcium. This seems very low based on the low affinity buffers in their solution. I used a standard and widely used tool (MINTEQ) to calculate the free calcium in their external solution and it says that the levels are 1.6 mM free calcium. It should be noted that most reports of calcium in CSF are for total calcium rather than free, and the total values are in the 1.1-1.4 range. If buffering in CSF is comparable to ACSF than this corresponds to 0.88 to 1.12 free calcium. So either I am wrong (and MINTEQ), or the authors are wrong. If they are incorrect then it makes a big difference for their experiments. It would also be a very bad thing for slice electrophysiology to get this wrong. Also see the paper by Borst at the calyx of Held that says that 2 mM added external calcium typically used in ACSF (as used in the present study) is too high (PMID 2394036). For these reasons I am highly skeptical that their calcium levels match those in vivo.

      We agree that our calculations and understanding of calcium levels were incorrect. We used only two of the constituents of our buffer solution for our calculation of free calcium, which gave our previous low estimate of 1.27mM, whereas MINTEQ is much more complete. We redid our calculations using MINTEQ and obtained the same values as the reviewer, and we thank the reviewer for pointing out this resource. We also looked at a broader range of studies including those suggested by the reviewer and agree that the literature has flagged 2mM total calcium as too high. We have added a new section to the Introduction to reflect this body of work. We have removed our earlier free calcium calculations.

      Please see our detailed response to this point above, including reference to the literature and re-running of many simulations at physiological levels of calcium, to examine the effect on our conclusions. In brief, the mismatch selectivity is weakened at physiological calcium, but is still present.

      (3) The issue of showing a 2% per pulse decrease that they attribute to ChR2 desensitization is important. This would be sufficient to have a major influence on their experiments in which they use repetitive activation. What is the time course of recovery of this inability to stimulate all of the fibers?

      Please see our response to the same point above. In brief, we have looked at the experimental data for field epsp decline over extended stimuli, and have shown that it settles at about 70% of the starting level in the case with the steepest decline (Figure 7-figure supplement 2). The time-course of decline is about 0.8 seconds. From the frequency dependence of the decline, we estimate that the recovery time is around 150 ms (Figure 7 -figure supplement 2). We also point out that our experimental data as well as our simulations of mismatch selectivity were carried out in the presence of ChR2 desensitization, yet we observed clear mismatch responses.

      Can they get around this problem by lowering the stimulus intensity?

      From Mattis et al Figure 2a, ChR2 performance over pulse trains deteriorates with decreasing power. Hence we do not expect that lowering the stimulus intensity would help.

      From the methods:

      “We chose short light pulses for two reasons. First, to decrease jitter in the light-triggered CA3 neuron spike timings. Second, if one is below saturating light intensities, short pulses at higher power give more consistent spiking over multi-pulse trains (Mattis et al. 2012), Figure 2A, using a 2ms pulse width). Note that the Mattis study was done at 20-23℃ as compared to our ~33℃, and the authors state that ChR2 kinetics are strongly temperature dependent.”

      Are their results altered if they lower the illumination intensity by a factor of 2 or increase it by a factor of 2?

      We did not try this, as we were aiming for short light pulses to minimize spike timing jitter, and we needed high intensity stimulation to get strong EPSPs on the postsynaptic cells. Based on the Mattis study we expect that yes, the results would be altered, and we would get more reliable spiking at still higher intensities. However, we used 100% intensity (estimated 100mW/mm<sup>2</sup>) in our optical system, so we could not push it further.

      We did perform one manipulation to mitigate desensitization: For the 1-square illumination we sequenced illumination from one spot to another, before returning to the first spot, so as to minimize desensitization. From the methods:

      “In 1-square stimulation experiments, the CA3 cell layer was illuminated one spot at a time with an interstimulus time of 3 seconds to avoid desensitisation of channelrhodopsin.”

      (4) They base their reliability of stimulation on field recordings. They need to do extracellular measurements from CA3 cells to see how reliably each cell fires and if they only fire once or more that once during stimulation.

      We used prior published work reporting intracellular recordings from CA3 cells, and additional analysis of field data to address this point. In brief, the probability of a cell firing is reliable, but on individual trials it might not fire. Additionally, we estimate that following a light pulse, cells fire twice about 40% of the time but rarely 3 or more times. We provide a more detailed response to this concern above.

      If each cell does not fire reliably once and only once for each stimulus pulse it will alter use-dependent plasticity and call into question the whole result.

      We agree that, at the single synapse level, an accurate account of use-dependent plasticity depends on single reliable spikes. Our recordings from CA1 are a sum over many synapses, and hence we use population CA3 activity measures to characterize our inputs, with the stipulation that these are reliable over multiple trials. Bhatia et al, 2019 showed reliability at the action-potential level, and in the current study we show it at the field potential level (Figure 1-figure supplement 2 panel F). We use our models to bridge the gap between the single-synapse responses to individual trials, to whole-cell readouts (Figures 5, 6, 7), and apply several tests to show that this produces models that fit the data (Table 1).

      Our results, including EI balance and mismatch selectivity, are direct measurements in the presence of distributions of input APs. We point out in the discussion that:

      “In-vivo input activity to this circuit is complex, and on successive stimuli there will be a distribution of exact CA3 pyramidal cell AP timings, number of APs per cell, and number of activated axons. To the extent that model robustness (Figure 9, Figure 7-figure supplement 3) gives insights into the real system we suggest that our small model of network + single neuron model + presynaptic signaling chemistry captures some of the attributes of the biological system, which lead to such robustness. This robustness is almost a necessity in a system where the probability of release for individual synapses is in the range of 20% (Murthy et al 1997): any signal transmission or plasticity-type computation has to accommodate huge stochastic uncertainty on any given trial.”

      I remain highly skeptical of their methods and their experimental results.

      We hope that we have addressed the specific points of concern that have led to this scepticism.

    1. Author response:

      The following is the authors’ response to the original reviews.

      We thank the editors and reviewers for their careful evaluation of our manuscript and for their constructive comments. We appreciate their recognition of the innovative chemoproteomic strategy and the complementary molecular, electrophysiological, and metabolic approaches used to identify voltage-dependent anion channels (VDACs) as mitochondrial targets of STX.

      In response to the reviews, we have revised the manuscript to strengthen the physiological rationale for studying POMC neurons; clarify the potential relevance of STX–VDAC signaling to neuronal mitochondrial function and neurodegeneration; distinguish our experimentally demonstrated mechanism from its potential disease relevance; clarify the contributions of individual VDAC isoforms; and more explicitly acknowledge the limitations of the present study.

      Our revised manuscript emphasizes that the principal finding of this study is the identification and functional characterization of an STX–VDAC mitochondrial mechanism in an estrogen-responsive neuronal system. Its relevance to neurodegenerative disease is presented as an important context and direction for future investigation rather than as a demonstrated disease mechanism.

      Public Reviews:

      Reviewer #1 (Public review):

      Major Concern

      (1) Lack of Rationale

      The study provides no justification for investigating sex-specific aspects of Alzheimer's disease by focusing on VDAC-mediated mitochondrial dysfunction in POMC neurons. These hypothalamic neurons are not recognized as early or primary sites of AD vulnerability, making the biological premise unclear.

      We thank the reviewer for raising this important point. We agree that the original manuscript did not sufficiently explain the rationale for using POMC neurons.

      Our rationale is primarily physiological rather than disease-specific. POMC neurons are a well-characterized, metabolically sensitive, and estrogen-responsive neuronal population in which membrane-initiated estrogen signaling and the actions of STX have been extensively characterized. They therefore provide a physiologically relevant neuronal system for identifying the molecular mechanisms through which STX regulates mitochondrial function.

      The potential relevance to neurodegeneration is supported by evidence that hypothalamic and POMC neuronal function can be disrupted in neurodegenerative disease models. Do and colleagues (2018) reported hypothalamic neurodegeneration, increased inflammatory and apoptotic markers, and reduced POMC neuronal populations in 3xTg-AD mice and further showed that exercise attenuated hypothalamic apoptosis and restored POMC neuronal populations (Do, Laing et al. 2018). In addition, Shen and colleagues (2016) demonstrated disruption of POMC/MC4R signaling in APP/PS1 mice and showed that restoration of this pathway improved synaptic function (Shen, Tian et al. 2016).

      These studies do not establish POMC neurons as a primary site of AD pathology, but they demonstrate that POMC-related neuronal systems can be vulnerable to neurodegenerative processes. This provides a broader biological context for investigating mitochondrial mechanisms in this neuronal population.

      There is also a strong physiological rationale for examining estrogen-sensitive mechanisms in POMC neurons. These neurons are established targets of 17β-estradiol and are highly responsive to metabolic and mitochondrial state. STX is a non-steroidal estrogenic compound that activates membrane-initiated estrogen signaling, and our previous studies demonstrated neuroprotective and mitochondrial effects of STX in a neurodegenerative disease model.

      Thus, POMC neurons were used because they provide a well-defined estrogen-responsive and metabolically sensitive neuronal population in which STX signaling can be mechanistically investigated—not because we consider them an initiating site of AD pathology.

      We have revised the Introduction and Discussion accordingly. The revised manuscript now emphasizes the physiological significance of STX–VDAC signaling for neuronal mitochondrial function and presents its potential relevance to neurodegeneration as an important area for future investigation.

      (2) Weak Link to AD Pathogenesis

      Although mitochondrial dysfunction is well established in AD, the authors do not convincingly demonstrate a mechanistic or pathological connection between VDAC2 and AD. VDACs are not established contributors to AD etiology, and the manuscript does not strengthen this association.

      We agree that the present experiments do not establish VDAC2 as an etiological or pathological driver of AD. This was not the objective of the present study.

      The primary goal was to identify the molecular target(s) through which STX influences mitochondrial function. Using BF-STX chemoproteomic capture and competition experiments together with single-cell gene-expression analysis, planar lipid membrane electrophysiology, and mitochondrial metabolic analyses, we identify VDAC proteins as mitochondrial targets of STX and demonstrate functional effects of STX on VDAC channel properties and mitochondrial bioenergetics.

      Our previous studies demonstrated neuroprotective and mitochondrial effects of STX in the 5xFAD model (Lee, Bostick et al. 2025), providing a neurodegenerative context that motivated the present mechanistic investigation. However, the current findings should not be interpreted as establishing VDAC2 as an AD pathogenic mechanism.

      We have revised the manuscript accordingly. The STX–VDAC interaction is now presented principally as a mitochondrial mechanism with potential relevance to neuronal physiology and neurodegeneration. Whether this pathway contributes to the neuroprotective actions of STX in disease models will require direct experimental testing.

      (3) Unclear Relevance to AD Contexts

      While the data support an interaction between STX and VDAC2 affecting mitochondrial parameters (ATP production, membrane potential, glycolysis, respiration) in POMC neurons, the study does not show whether this mechanism is relevant to mitochondrial dysfunction in AD. No validation is provided in AD-related models or in contexts related to sex-specific AD phenotypes.

      We agree that the present experiments do not directly establish the relevance of the STX–VDAC interaction to mitochondrial dysfunction in AD.

      The current study was designed to identify and characterize the molecular mechanism underlying the mitochondrial actions of STX, rather than to test this pathway in a specific neurodegenerative disease model. Our findings demonstrate that STX interacts with VDAC proteins, modifies VDAC channel properties, and alters mitochondrial bioenergetics.

      The study builds on our previous findings in the 5xFAD model, in which STX reduced amyloid-β-associated pathology and affected mitochondrial function (Lee, Bostick et al. 2025). The identification of VDAC proteins as STX targets therefore provides a mechanistic foundation for future studies examining whether this pathway contributes to neuronal protection under neurodegenerative conditions.

      We have revised the Discussion to acknowledge the absence of direct disease-model validation. Future studies using conditional or neuron-specific manipulation of VDAC isoforms will be important for determining the physiological and neuroprotective significance of STX–VDAC signaling in vivo.

      Accordingly, our conclusions now emphasize what is directly supported by the present experiments: STX interacts with VDAC proteins and modulates VDAC channel function and mitochondrial bioenergetics. The relevance of this mechanism to neurodegenerative disease remains to be established.

      (4) Interpretation of Competitive Binding Data

      The competitive binding results in Figure S4B are not adequately interpreted. The dose-dependent competition observed for VDAC3 suggests it may be a stronger candidate than VDAC2, yet this possibility is not addressed.

      We thank the reviewer for highlighting this important point. We agree that the original manuscript placed too much emphasis on VDAC2 based on the chemoproteomic data.

      Our chemoproteomic experiments identified VDAC1, VDAC2, and VDAC3 as STX-interacting proteins. Competition with unlabeled STX produced a particularly clear reduction in VDAC3 labeling, including complete loss of the VDAC3 signal at three molar equivalents of unlabeled STX. We therefore agree that VDAC3 represents an important candidate STX target.

      We have revised the Results and Discussion so that the competition experiment is no longer interpreted as demonstrating preferential or exclusive binding to VDAC2.

      However, the persistence of VDAC1 and VDAC2 labeling may also be influenced by properties of the BF-STX photoprobe as alkyl diazirine probes can preferentially photolabel membrane proteins (Kleiner, Heydenreuter et al. 2017). We now present this only as a possible technical consideration rather than an explanation established by our data.

      Our subsequent emphasis on VDAC2 was based on the integration of several observations. Single-cell qPCR demonstrated that Vdac2 is the predominant transcript in the native POMC neurons examined (revised Figure 3B), with an approximate expression hierarchy of Vdac2 > Vdac3 >> Vdac1. In addition on a technical note, recombinant VDAC3 is more difficult to reconstitute reliably into artificial membranes because of its lower stability in detergent.

      The revised manuscript therefore recognizes all three VDAC isoforms as candidate STX targets but does not claim that VDAC2 is the exclusive or preferential target. Direct comparisons of STX binding and functional modulation among the three isoforms will be required to establish isoform selectivity.

      Reviewer #2 (Public review):

      (1) Physiological Relevance of Cell-Line Experiments

      Most experiments were performed in immortalized cell lines rather than primary neurons or in vivo models, limiting their physiological relevance.

      We agree that the use of immortalized neuronal cell models represents an important limitation.

      However, these models provided the cellular material, reproducibility, and experimental control required for chemoproteomic target capture and Seahorse metabolic measurements. Importantly, we complemented these studies with single-cell analysis of native POMC neurons and electrophysiological characterization of recombinant VDAC channels.

      Nevertheless, these approaches do not substitute for direct demonstration of STX–VDAC signaling in primary POMC neurons or in vivo. We have therefore revised the Discussion to emphasize that establishing the physiological significance of this mitochondrial pathway will require validation in primary neuronal preparations and whole-animal models.

      (2) Structural Binding Site of STX on VDAC

      The exact structural binding site of STX on VDAC remains unresolved.

      We agree. BF-STX chemoproteomics identifies proteins interacting with STX in a cellular environment but does not resolve the amino acid residues or structural pocket responsible for binding.

      We have clarified this limitation in the Discussion. Determining the STX-binding site will require complementary approaches such as targeted mutagenesis, direct binding measurements with purified VDAC proteins, and structural studies in membrane-like environments, including lipid nanodiscs. Such studies should also determine whether STX recognizes a conserved feature among VDAC isoforms or exhibits isoform selectivity.

      (3) Lack of VDAC2 Loss-of-Function Experiments

      No loss-of-function experiments (e.g., VDAC2 knockdown) were performed to establish a direct causal link between VDAC2 and STX's bioenergetic and neuroprotective effects.

      We agree that VDAC loss-of-function experiments would provide an important additional test of causality.

      Our present evidence is convergent: chemoproteomics identifies VDAC proteins as STX-interacting targets; single-cell analyses demonstrate VDAC expression in POMC neurons; electrophysiological studies show that STX modifies VDAC channel properties; and metabolic analyses demonstrate STX-dependent changes in mitochondrial bioenergetics. Together, these findings support a STX–VDAC mechanism but do not establish that VDAC2 alone is necessary for the mitochondrial or neuroprotective actions of STX.

      We have revised the manuscript accordingly and explicitly identify the absence of loss-of-function experiments as a limitation.

      Because whole-body VDAC2 loss-of-function is associated with severe developmental consequences, future studies will require conditional or neuron-specific approaches. Parallel evaluation of VDAC1 and VDAC3 will also be important because all three isoforms were identified by chemoproteomics and potential functional redundancy may complicate single-isoform manipulations.

      (4) Non-linear Dose-Response at Higher STX Concentrations

      The non-linear dose-response at higher STX concentrations also requires further investigation.

      We agree that the non-linear concentration-response warrants further investigation and have revised the Discussion to avoid interpreting the STX response as a simple monotonic concentration-response relationship.

      One possibility is that STX engages multiple mitochondrial targets with different apparent affinities and opposing effects on respiration. At lower concentrations, STX may preferentially engage a higher-affinity target, potentially VDAC, whereas higher concentrations may recruit lower-affinity targets that constrain this response. Consistent with this possibility, our BF-STX dataset (Supplemental Tables) identified several mitochondrial proteins involved in oxidative phosphorylation and metabolite transport, including ATP5F1C, NNT, SLC25A4, SLC25A5 and SLC25A3. ATP5F1C is required for efficient mitochondrial ATP production (Fiorillo, Scatena et al. 2021), and estrogenic regulation of ATP synthase has been reported (Massart, Paolini et al. 2002, Moreno, Moreira et al. 2013). NNT, SLC25A4, SLC25A5 and SLC25A3 also regulate mitochondrial respiration, redox balance, and ATP production (Mayr, Merkel et al. 2007, Lopert and Patel 2014). However, BF-STX enrichment does not establish direct STX binding, relative affinity, or functional modulation of these proteins. We therefore present the multi-target explanation only as a hypothesis. Direct binding and concentration-dependent target-engagement studies will be required to determine whether the non-linear response reflects recruitment of a lower-affinity mitochondrial target, concentration-dependent effects on VDAC itself, or downstream mitochondrial feedback.

      We thank the editors and reviewers again for their constructive comments. The revised manuscript more clearly defines the physiological rationale for the experimental system, establishes the scope of the STX–VDAC mitochondrial mechanism supported by our data, and places its potential relevance to neurodegeneration in an appropriately forward-looking context.

      We hope that the revised manuscript and our responses satisfactorily address the concerns raised by the editors and reviewers.

      References

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      Fiorillo, M., C. Scatena, A. G. Naccarato, F. Sotgia and M. P. Lisanti (2021). "Bedaquiline, an FDA-approved drug, inhibits mitochondrial ATP production and metastasis in vivo, by targeting the gamma subunit (ATP5F1C) of the ATP synthase." Cell Death Differ 28(9): 2797-2817.

      Kleiner, P., W. Heydenreuter, M. Stahl, V. S. Korotkov and S. A. Sieber (2017). "A Whole Proteome Inventory of Background Photocrosslinker Binding." Angew Chem Int Ed Engl 56(5): 1396-1401.

      Lee, H.-J., Z. Bostick, J. Doherty, T. L. Swanson, M. J. Kelly, J. F. Quinn, N. E. Gray and P. F. Copenhaver (2025). "Neuroprotection against beta-amyloid toxicity by the novel estrogen receptor modulator STX requires convergent signaling pathways." Frontiers in Molecular Neuroscience Volume 18 - 2025.

      Lopert, P. and M. Patel (2014). "Nicotinamide nucleotide transhydrogenase (Nnt) links the substrate requirement in brain mitochondria for hydrogen peroxide removal to the thioredoxin/peroxiredoxin (Trx/Prx) system." J Biol Chem 289(22): 15611-15620.

      Massart, F., S. Paolini, E. Piscitelli, M. L. Brandi and G. Solaini (2002). "Dose-dependent inhibition of mitochondrial ATP synthase by 17 beta-estradiol." Gynecol Endocrinol 16(5): 373-377.

      Mayr, J. A., O. Merkel, S. D. Kohlwein, B. R. Gebhardt, H. Böhles, U. Fötschl, J. Koch, M. Jaksch, H. Lochmüller, R. Horváth, P. Freisinger and W. Sperl (2007). "Mitochondrial phosphate-carrier deficiency: a novel disorder of oxidative phosphorylation." Am J Hum Genet 80(3): 478-484.

      Moreno, A. J., P. I. Moreira, J. B. Custódio and M. S. Santos (2013). "Mechanism of inhibition of mitochondrial ATP synthase by 17β-estradiol." J Bioenerg Biomembr 45(3): 261-270.

      Shen, Y., M. Tian, Y. Zheng, F. Gong, A. K. Y. Fu and N. Y. Ip (2016). "Stimulation of the Hippocampal POMC/MC4R Circuit Alleviates Synaptic Plasticity Impairment in an Alzheimer's Disease Model." Cell Rep 17(7): 1819-1831.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Reviewer #1 (Public review):

      (R1.1) Lack of Overall Effects and Inflated Type I Error for Game-Level Effects For Study 1, to identify condition differences at the game level (i.e., Figure 2), the authors effectively conducted 70 independent t-tests (5 measures × 14 games). While 7 significant results were reported, this large number of independent tests invites an inflated Type I error rate, as no multiple-comparison correction appears to have been applied. A similar inflation is expected in Study 2, where 50 independent t-tests (5 measures × 10 games) yielded 5 significant comparisons (Figure 4). Although the authors might argue the direction of the differences is systematic, implying GVS generally impairs performance, at least one significant comparison shows the opposite effect: tool switching indicates that GVS led to better performance for the 'Table_A' game in Study 2 (Figure 4d), whereas the same variable indicated GVS led to worse performance in Study 1 (Figure 2d). I suspect that none of the significant game-level results would survive a proper statistical correction. If possible, the authors can redo statistical testing with corrections (FDR or Bonferroni) or with LMM using game as a random effect. Before proper statistical analyses, I strongly encourage the authors to refrain from drawing broad conclusions based on these isolated game-level results.

      We thank the reviewer for this important statistical point. We have revised the manuscript to clarify that each game was treated as a distinct physical-reasoning problem, and these were used to localize the games in which the stimulation effect was expressed, not to compare games with one another or to draw broad conclusions from isolated contrasts (and therefore, in this case, no multiple-comparison corrections are required; lines 637-640). That said, to address the reviewer’s concern directly and to strengthen our conclusions in the paper, we also added mixed-effect models using gravity impact level and stimulation type as fixed factors and participant and game as random effects for each study (lines 168-177, 202-207, 257-259, 301-303, 641-651, Tables 2 and 4).

      (R1.2) Furthermore, when analyzing data across all games, the study found no significant effect of GVS on overall performance or strategy measures in either Study 1 or Study 2. This lack of an aggregate effect contradicts the authors' conclusion that participants failed more often or utilized suboptimal strategies under GVS.

      We thank the reviewer for raising this issue. We agree that the analyses collapsed across all games did not reveal significant overall effects. However, this pattern is informative rather than contradictory: the full-game analysis combining gravity-dependent problems with games in which gravity does plays little or no role in the solution (8 low-gravity-impact games in Study 1 and 4 in Study 2; Extended Data Table 1). If GVS had produced a general dizziness-related, physiological, attentional, or arousal effect, we would expect a broad impairment across the task. Instead, the revised mixed-effects models show that the effects were tied to gravity-relevant contexts: in Study 1, GVS was associated with a trend-level increase in attempts for medium-gravity-impact games and a significant increase in placement distance for high-gravity-impact games. These effects were not observed in Study 2. Together with the cross-study Gravity Index analyses, this pattern strengthens the interpretation that GVS did not cause a general impairment, but selectively altered physical reasoning as a function of the gravitational context. We have now clarified this point in the manuscript (lines 398-403).

      (R1.3) Missing Rationale for Classification Analysis.

      It is puzzling why the authors pursued two exploratory analyses on tool placement after revealing that the two related primary measures (tool positioning and switching) did not generate significant condition differences in Study 1. These additional analyses-the Dirichlet Process Gaussian Mixture Model and leave-one-out classification-were not pre-registered. In the absence of overall condition differences, the authors appear to be "doubling down" by applying sophisticated classification tools to the raw data without a clear prior rationale.

      We thank the reviewer for this important comment. We agree that the rationale for these additional analyses needed to be made clearer. Our aim was not to “double down” on the primary measures, but to test a distinct question that the preregistered summary measures cannot address. The distance and tool-switching measures reduce each participant’s behaviour to two averages; they therefore do not capture the multivariate structure of spatial placements, whether participants move between distinct placement strategies across successive attempts, or whether the overall placement distributions differ systematically between stimulation conditions. Our analyses, therefore, included these two complementary analyses, adapted from prior Virtual Tools work (Allen et al., 2024), to characterise the spatial and sequential organisation of tool-use strategies. The Dirichlet Process Gaussian Mixture Model is well suited to this question because it identifies strategy clusters directly from x/y placement coordinates without imposing an a priori number of strategies, allowing us to quantify transitions between spatial strategies across attempts (in relation to the environment in the game which is not taken into account in the more basic measures). The leave-one-out kernel-density analysis then asks a related but independent question: whether the placement patterns contain sufficient condition-specific structure to classify stimulation condition above chance. These analyses therefore add value by testing the organisation of strategy use at a level not captured by the primary summary measures. We have revised the manuscript to clarify this rationale and to present these analyses as complementary evidence about strategy organisation, while keeping the mixed-effects models as the primary inferential basis for the manuscript (lines 216-218, 721-731, 752-753).

      (R1.4) Insufficient Evidence for the Reduced Effect of GVS Under Altered Gravity… To compare Study 1 and Study 2, the authors devised a "gravity-weighted index," but its definition is not sufficiently justified. The index assigns weights of 1, 2, and 3 to low-, medium-, and high-gravity-dependent games, respectively. The choice of these specific weights appears arbitrary, making the quantitative results difficult to interpret. More importantly, there is no citation or explanation regarding how these three levels of "gravity impact" were defined in the first place (Line 468). This index was also not pre-registered.

      We thank the reviewer for this important comment. We agree that the original gravity-weighted index was not sufficiently justified because it combined the three gravity-impact levels, using numerical weights of 1,2, and 3. Although these weights followed the ordinal classification of the games, they were not independently validated and could therefore make the cross-study comparison difficult to interpret. To address this concern directly, we removed the gravity-weighted index entirely. In the revised manuscript, we instead use a Gravity Index that is calculated separately for each measure and each gravity-impact level, as the ratio between performance or strategy outcomes under GVS and Sham. This removes the arbitrary weighting scheme and provides a direct estimate of the stimulation effect within each gravity-impact category.

      We then compared these Gravity Indexes between Study 1 and Study 2 using mixed-effect models that include study and gravity-impact level as fixed factors, rather than collapsing across gravity-impact levels with our defined weights. We used participant as random factor. Because the indexes are bounded and showed clustering at structural values, we analysed them using Bayesian cumulative logit models, which are appropriate for bounded, non-normally distributed outcomes and allow the cross-study contrasts to be estimated without imposing a linear weighting structure. We also clarified how the gravity-impact categories were defined, based on piloting and previous computational modelling work in the lab, and report the classification of each game in Extended Data Table 1. These revisions directly address the reviewer’s concern by replacing the arbitrary weighted composite with a transparent, category-specific analysis of the GVS effect across terrestrial and altered-gravity contexts, in line with frameworks outlined by James et al. (2021), Li et al. (2023), Liu et al. (2017) (lines 140-147, 276-292, 307-317, 588-594, 658-666, 692-717, Table 5, Fig 5, Extended data Fig 3).

      James, N. T., Harrell Jr, F. E., & Shepherd, B. E. (2021). Bayesian cumulative probability models for continuous and mixed outcomes. arXiv preprint arXiv:2102.00330.

      Li, C., Tian, Y., Zeng, D., & Shepherd, B. E. (2023). Asymptotic properties for cumulative probability models for continuous outcomes. Mathematics, 11(24), 4896.

      Liu, Q., Shepherd, B. E., Li, C., & Harrell Jr, F. E. (2017). Modeling continuous response variables using ordinal regression. Statistics in medicine, 36(27), 4316-4335.

      Manuguerra, M., Heller, G. Z., & Ma, J. (2020). Continuous ordinal regression for analysis of visual analogue scales: The R package ordinalCont. Journal of Statistical Software, 96, 1-25.

      (R1.5) The authors state that for the success rate index, a value close to -1 indicates a large negative difference for GVS, 0 indicates no difference, and 1 indicates a large positive difference. These are theoretical bounds; the actual distribution of each index should be examined to validate such claims. However, the paper lacks descriptive statistics for this composite index.

      We removed the composite index (See R1.6) and included the actual distribution of each index for the two studies in Extended Data Fig. 3.

      (R1.6) Notably, the "reduction" of the GVS effect in altered gravity was only demonstrated in one of the five available indices (success rate, p = 0.046). In fact, the success rate in Study 2 was 66.7(sham) vs 67.3 (GVS) in Table 2. It is highly debatable whether this marginal result justifies the conclusion that GVS effects "were reduced when the games included reasoning about altered gravity.

      We thank the reviewer for this important point. We agree that the original wording placed too much weight on a single marginal comparison and could be read as implying a direct overall benefit of GVS in Study 2. We have therefore revised both the analysis and the interpretation. The conclusion no longer rests on the absolute GVS–Sham difference in Study 2 alone, which was small when averaged across all games. Instead, we now ask a more targeted question: whether the relative effect of GVS differs between terrestrial and altered-gravity contexts as a function of the games’ gravity impact. To address this, we replaced the previous gravity-weighted index with separate Gravity Indexes for each measure and each gravity-impact level, and compared these indexes across the two studies.

      This revised analysis provides a more precise pattern. For success rate, the high-gravity-impact games showed evidence in the predicted direction, with a higher GVS/Sham index in Study 2 than in Study 1, suggesting that the negative effect of vestibular disruption observed under terrestrial gravity was reduced when participants reasoned about altered gravity (lines 285-287, Fig. 5, Table 5). For strategy, the distance index also showed gravity-impact-dependent differences between studies, indicating that GVS affected spatial strategy organisation differently depending on the gravitational context (lines 307-315; Fig. 5; Table 5). We have also tempered the relevant claims in the Discussion—rather than arguing for a broad facilitation effect, we now conclude that GVS has a context-dependent influence on physical reasoning, with detrimental effects under terrestrial gravity and reduced or relatively more favourable effects when reasoning must be adapted to altered gravity. Finally, we explicitly note that the time index should be interpreted cautiously because participants were not instructed to prioritise speed, making speed–accuracy trade-offs difficult to interpret (lines 335-336, 420-436).

      (R1.7) Questionable Assumptions Regarding Strategy. The authors assume that "big changes in tool positioning and frequent tool switching indicate poor evaluation of the failed outcome". This assumption is questionable. In solving this cognitive task, participants must explore and exploit solutions based on feedback. Large shifts in positioning or frequent tool switching might reflect active, adaptive exploration based on failed outcomes rather than a failure to evaluate them.

      We thank the reviewer for this comment. We agree that large changes in tool placement or tool switching are not inherently maladaptive, because exploration is an essential part of trial-and-error learning in the Virtual Tools task. Our interpretation is more specific: when these measures are averaged across attempts within a game, persistent large shifts in placement and frequent switching provide a proxy for reduced convergence on an effective strategy, rather than for any single exploratory move being “poor”. We have revised the manuscript to make this interpretation more nuanced (lines 194-197).

      We also clarified that this interpretation is grounded in our and others’ previous work using the same Virtual Tools task, in which these strategy measures systematically tracked improved reasoning across development and reduced reasoning efficiency in ageing (Grandchamp des Raux et al., 2024; Grandchamp des Raux et al., 2025; Dexter et al., 2025; Allen et al. 2023). Thus, although exploration can be adaptive, the pattern captured by these averaged measures has empirical validity as an index of how efficiently participants refine their strategy after feedback. We have therefore revised the wording to avoid implying that all switching or repositioning reflects poor evaluation, while retaining the use of these measures as established indicators of strategy organisation in this task (lines 194-197).

      (R1.8) Confounding Factors in GVS Interpretation… GVS does not selectively target the vestibular nerve; it also activates distributed fronto-parietal attention networks and hippocampal circuits essential for any reasoning task. Additionally, the vestibular system is linked to the limbic system and the cerebellum, which regulate emotional reactivity and arousal. Because attention and emotion are likely affected by GVS, the authors should be much more cautious in attributing their behavioral findings solely to changes in the "physical experience of the body.

      We thank the reviewer for raising this important point. We agree that GVS should not be interpreted as targeting the vestibular nerve in isolation, because vestibular signals are embedded within a distributed cortical and subcortical network that also contributes to attention, spatial cognition, arousal, emotion, and executive control. We have therefore revised the manuscript to acknowledge this broader vestibular-cognitive network explicitly, citing Ferrè and Haggard (2020), and to avoid attributing the behavioural effects solely to a narrow vestibular mechanism (lines 406-407).

      At the same time, the pattern of results is not consistent with a general attentional, arousal-related, or discomfort-driven impairment. If GVS had mainly disrupted participants’ general cognitive state, we would expect a broad reduction in performance across games and across gravitational contexts. Instead, we did not observe a general GVS effect across all games, and the effects were tied to the gravity relevance of the task and to the gravitational context: in Study 1, GVS affected measures most clearly in games with medium or high gravity impact, whereas the same pattern was not observed in Study 2 under altered-gravity reasoning. This selectivity strengthens the interpretation that the effects are related to gravity-dependent physical reasoning rather than to a non-specific physiological consequence of stimulation. We have revised the Discussion to make this point more explicit while still acknowledging that GVS acts on a broader vestibular-cognitive system rather than on a single isolated pathway (lines 398-410, 416-419).

      Ferrè, E. R., & Haggard, P. (2020). Vestibular cognition: State-of-the-art and future directions. Cognitive neuropsychology, 37(7-8), 413–420. https://doi.org/10.1080/02643294.2020.1736018

      Reviewer #2 (Public review):

      (R2.1) Absence of multiple-comparisons correction. A large number of game-level pairwise t-tests are conducted in both studies (upward of twenty per study) without correction for familywise error rate. The game-level effects that anchor the main narrative - in Study 1 alone: Remove, GoalMove, Spiky, Falling_A, Shafts_B, Gap, and Chaining - arise from an uncorrected pool of comparisons. The probability that some of these constitute false positives is non-trivial. The authors should apply a correction (e.g., Benjamini-Hochberg) or at a minimum discuss this limitation explicitly.

      We thank the reviewer for their comment. As we answered to R1.1, We have revised the manuscript to clarify that each game was treated as a distinct physical-reasoning problem, and these were used to localize the games in which the stimulation effect was expressed, not to compare games with one another or to draw broad conclusions from isolated contrasts (and therefore, in this case, no multiple-comparison corrections are required; lines 637-640). That said, to address the reviewer’s concern directly and to strengthen our conclusions in the paper, we also added mixed-effect models using gravity impact level and stimulation type as fixed factors and participant and game as random effects for each study (lines 168-177, 202-207, 257-259, 301-303, 641-651, Tables 2 and 4).

      (R2.2) The facilitation claim rests on a post-hoc and arbitrarily parameterized index…These coefficients are entirely arbitrary and bear no principled relationship to the actual gravitational magnitudes used in the study. Why not use the gravity dependency ratings themselves, or the empirically estimated gravity impact scores from the computational modelling mentioned in the Methods? The choice of weights should be either principled or tested across a range of values to demonstrate robustness.

      The reviewer raises an excellent point. As described in our response to R1.4, we agree that the original gravity-weighted index was not the best way to test the cross-study effect, because assigning numerical weights of 1, 2, and 3 to low-, medium-, and high-gravity-impact games imposed an interval structure that was not independently validated. We therefore removed this weighted index entirely.

      We also considered the reviewer’s suggestion of using the gravity-dependency ratings or computational gravity-impact estimates directly. However, these values were designed to classify and balance games according to the extent to which their solution depends on gravity; they were not calibrated as an interval-scale measure of the expected GVS effect, nor are they commensurable across the different outcome measures. Using them as continuous weights would therefore reintroduce the same problem: it would treat a stimulus-classification variable as a quantitative weighting parameter. Similarly, weighting by the physical gravity magnitudes used in Study 2 would not be appropriate, because gravity magnitude (0.5g vs 2g) and gravity dependency of a game are conceptually distinct: the former defines the simulated environment, whereas the latter defines how much solving a given game relies on gravity-based reasoning.

      To address the issue more directly, we now compute a Gravity Index separately for each measure and each gravity-impact level. We then compare these indices between Study 1 and Study 2 using models that include study and gravity-impact level as factors, rather than collapsing across games with author-defined weights. This approach preserves the theoretical distinction between low-, medium-, and high-gravity-impact problems while avoiding arbitrary parameterisation. We have revised the Methods, Results, and Discussion accordingly (lines 140-147, 276-292, 307-317, 588-594, 658-666, 692-717; Table 5; Fig. 5; Extended Data Fig. 3).

      (R2.3) Furthermore, the notation in equation (1) as currently typeset reads as "Gravity minus Weighted Index" rather than "Gravity-Weighted Index"; this should be corrected.

      We followed the reviewer’s comment and adjusted the notation in equation 1 (lines 702-706).

      (R2.4) The "facilitation" interpretation exceeds what the data in Study 2 directly support. Across all games in Study 2, GVS versus Sham differences in absolute performance are non-significant in all directions. The facilitation claim derives entirely from the GWI being higher in Study 2 than in Study 1 - a between-subjects comparison involving different participant groups and a non-pre-registered metric. The language of "facilitation" should be tempered accordingly, or the authors should provide additional analyses to support this framing.

      The reviewer is correct that more support is needed. We now strengthened the facilitation argument by adding a new mixed-effect models that includes gravity impact as a factor, by showing that: (1) while in study 1, GVS has a detrimental effect in some of the performance and strategy measures, in study 2 none of the GVS vs Sham differences is significant (lines 172-177, 205-207, 257-259, 301-303); and (2) the comparison of the GI between the 2 studies pinpoint to a facilitation role limited to games where gravity matters (284-287, 308-315). At the same time, we have tempered the language in the Discussion by avoiding a broad claim of facilitation and instead stating that the evidence points to a context-dependent effect of GVS, with detrimental effects under terrestrial gravity and reduced or relatively more favourable effects under altered-gravity reasoning, with moderate evidence for the success-rate index (lines 333-336). Thus, the revised manuscript directly addresses the reviewer’s concern in two ways: the interpretation no longer depends on a single aggregate Study 2 comparison, and the facilitation language has been replaced by a more precise conclusion supported by the new gravity-impact-level analyses.

      (R2.5) Gravitational manipulation is visual only, and the vestibular system is only one component of the gravity-sensing network. Gravity perception results, as the authors very well know, from a distributed multisensory integration process that involves, in addition to the vestibular system, visual, proprioceptive, and visceral inputs. The present paradigm manipulates gravitational context solely through visual cues and targets the vestibular system through GVS - a point the authors acknowledge but do not discuss in sufficient depth. It is important to distinguish clearly between real gravitational alterations (as achieved in parabolic flight or centrifuge environments, where the entire body is physically subjected to a different gravitational vector) and virtually altered gravity, where only one sensory modality is targeted while others remain anchored to 1 g. The scope of the conclusions should reflect this distinction.

      We thank the reviewing for raising this point and clarified the distinction in the introduction and discussion (lines 104-108, 353-356).

      (R2.6) The choice of 0.5 g and 2 g may lack sensitivity. Combining the two altered-gravity conditions in Study 2, because no significant effect of hypo versus hypergravity was found, is statistically pragmatic but conceptually unsatisfying. There is evidence in the space physiology literature that gravitational processing is not linearly symmetric around 1 g: threshold effects exist below and above terrestrial gravity that may not be captured by modest deviations (half and double g) - see refs below. It is worth discussing whether the absence of a hypo/hyper distinction in Study 2 reflects a genuine equivalence or a lack of sensitivity, and whether more extreme conditions (e.g., near-zero g or 4-5 g) might reveal different processing regimes. Whether 0.5 g and 2 g were sufficient to saturate the system or merely insufficient to perturb it remains an open question with direct implications for the interpretation of the null GWI effects on strategy measures.

      We thank the reviewer for this helpful point. We agree that gravitational processing may be non-linear around 1g, and we have revised the manuscript to acknowledge that more extreme gravitational manipulations may reveal effects that are not captured by 0.5g and 2g. In the present study, however, our aim was not to characterise the psychophysical function across different levels of altered gravity, but to test whether reasoning in a non-terrestrial gravitational context changes the effect of vestibular perturbation. We therefore tested whether hypogravity and hypergravity should be analysed separately by adding gravity level (0.5g vs 2g) to the mixed-effects models. Gravity level was not a significant predictor for any performance or strategy measure, and this was consistent with previous Virtual Tools work showing no reliable difference between hypo- and hypergravity effects. On this basis, we aggregated the two conditions as “altered gravity” for the main analyses (lines 248-253). We have now also clarified that this aggregation should not be interpreted as evidence that 0.5g and 2g are cognitively equivalent in all contexts, but rather that no reliable hypo/hyper distinction was detected in the present task and parameter range (lines 248-253, 462-463, 651-656).

      (R2.7) High-level reasoning is not defined with sufficient precision. The term "high-level reasoning" appears from the title onward and in the heading of the Study 1 results section (line 138), but it is never formally defined. The reader needs a clearer account of what distinguishes high-level physical reasoning from low-level sensorimotor prediction, and where the games used here fall along that continuum.

      We thank the reviewer for pointing this out and added a clear definition of high-level reasoning at the beginning of the Introduction section (lines 41-44).

      (R2.8) What specific physical competencies - ballistic trajectories, free-fall predictions, collision dynamics, frictional forces, inertial effects - are required across the game set? When describing the subset of games that drive key effects, this information is critical for evaluating whether effects are specific to gravity reasoning or to some other physical concept.

      The reviewer is correct that the Virtual Tools games require multiple physical competencies, including gravity-based prediction, collision dynamics, object support, containment, and the anticipation of object-to-object interactions. Importantly, most games do not isolate a single physical principle; rather, successful solutions typically require combining several physical predictions. For this reason, our aim was not to attribute each effect to one isolated physical primitive, such as ballistic motion or friction, but to test whether GVS effects were stronger in games whose solutions depended more heavily on gravity-based reasoning.

      To make this clearer, we revised the manuscript to state that the game set varied systematically in the extent to which gravity-related predictions were required for solution, and that this classification was based on piloting and previous computational modelling work in the lab (lines 112-116, 426-431, 588-594; Extended Data Table 1). This design is central to the logic of the study: if GVS produced a general disruption, effects should appear broadly across the task; if it affected gravity-dependent reasoning, effects should be most evident in games with higher gravity impact. We now clarify this point and avoid implying that the task isolates gravity from all other physical competencies.

      (R2.9) Performance measures are disconnected from underlying kinematics. The performance measures (success rate, number of attempts, time per attempt) are coarse, high-level summaries.

      We agree that success rate, number of attempts, and time per attempt are high-level measures. This is, however, aligned with the logic of the Virtual Tools task. Participants do not physically manipulate objects or perform complex reaching movements; they simply select a tool with one click and place it on the screen with another. The critical demand is therefore not manual dexterity or movement execution, but the ability to predict the physical cascade that will follow from a chosen tool and placement. For this reason, kinematic measures would not provide a direct index of the reasoning process targeted here. We have clarified this in the manuscript by emphasising that the task minimises motor demands and that performance depends primarily on tool selection and spatial placement, allowing us to focus on high-level physical reasoning rather than movement kinematics (lines 116-121).

      (R2.10) Time per attempt is used as a proxy for performance efficiency, yet participants received no instructions regarding speed, and different individuals may have adopted systematically different speed-accuracy trade-offs.

      We thank the reviewer for this helpful comment. We agree that time per attempt should not be interpreted as a straightforward performance-efficiency measure. Participants were told that each game had an overall time limit, but they were not instructed explicitly to respond as quickly as possible. Attempt duration could therefore reflect several processes, including deliberation, hesitation, task engagement, or individual speed–accuracy trade-offs, rather than better or worse reasoning. We have revised the manuscript accordingly: time per attempt is now treated cautiously as a secondary descriptive measure of attempt duration, rather than as a direct index of performance efficiency. We also clarified in the Methods that participants were given a time limit but no speed instruction, and in the Discussion that the time results should be interpreted with caution for precisely this reason (lines 121-125, 431-436, 558-560).

      (R2.11) It would be valuable to know whether time per attempt correlates with attempt number within a given game (which would indicate within-game learning) and whether mouse movement data - trajectory, velocity, hesitation - were recorded and could be analysed to provide more mechanistic insight into strategy formation.

      We thank the reviewer for this suggestion and agree with the reviewer that the insight into strategy formation (and hesitation in particular) could be examined more precisely, potentially using eye tracking to capture where participants look. We add a comment in our discussion (lines 434-436). We also included the correlation in our analyses (lines 183-186, 265-267, Extended Data Fig.1 and Fig.2).

      Reviewer #2 (Recommendations for the authors):

      (R2.12) Introduction, end of paragraph 2 (applied fields): The authors mention artificial intelligence and robotics as fields that could benefit from this work. Pedagogy and educational neuroscience are equally relevant: understanding how the brain conceptualizes gravity through embodied interaction could inform how physics is taught, and could motivate more sensorimotor-grounded instructional approaches.

      This is a great point! We have now added pedagogy and educational neuroscience as relevant fields, along with corresponding references (line 52).

      (R2.13) The gravitational acceleration is typeset as "ms<sup>2</sup>," which appears to conflate milliseconds-squared with the correct unit, m·s<sup>-2</up> (or m/s<sup>2</sup>). Please verify the superscript convention used throughout.

      We corrected the manuscript accordingly (line 78).

      (R2.14) When introducing GVS as the tool for gravitational manipulation, the authors should more explicitly clarify that GVS produces noise in the vestibular organ rather than a physical change in the gravitational environment. Readers familiar with space physiology will notice the asymmetry between this approach and paradigms involving true gravitational alteration (parabolic flight, centrifuges). The introduction should acknowledge this asymmetry upfront rather than leaving it to the Discussion.

      We agree that this distinction should be made explicit from the outset. We have therefore revised the Introduction to clarify that GVS does not physically alter the gravitational environment, as in parabolic flight or centrifuge paradigms, but instead introduces noise into vestibular signalling while participants remain in terrestrial gravity. This asymmetry is now acknowledged before the study rationale is presented, so that the scope of the manipulation is clear to readers from the beginning (lines 102-108).

      (R2.15) “covered by the same ethical approval than study 1" - should read "as study 1.”

      We corrected the manuscript accordingly (line 512).

      (R2.16) Line 422: Was the red text label the only cue indicating the gravity condition in the altered-gravity games? If so, this is an important detail with potential implications for how participants updated their expectations. Please clarify.

      We thank the reviewer for this comment. Yes, the red text label was the explicit cue indicating the gravity condition for each altered-gravity game. Participants were told before the task that the gravity condition would vary across games and that they should attend to the red sentence at the top of the screen to identify whether the current game was in hypo- or hypergravity. We have clarified this in the Methods, including that the visual label was presented for each game and served as the instruction cue for the gravitational context (lines 560-562).

      (R2.17) Lines 547-555 - GWI notation and coefficients: (a) Replace the subscript indices 1, 2, 3 in the equations with "low," "med," and "high" to improve readability and link the notation directly to the experimental conditions.

      We changed the manuscript accordingly (lines 697-706).

      (R2.18) Lines 547-555 - GWI notation and coefficients: (b) Justify the choice of weighting coefficients 1, 2, and 3. These are arbitrary integers that do not correspond to actual gravity levels or to the empirically estimated gravity impact scores used elsewhere in the paper. Either provide a principled rationale or demonstrate that the GWI result is robust across alternative plausible weightings.

      We agree with the reviewer that the original weighting coefficients of 1, 2, and 3 were not independently validated and therefore made the gravity-weighted index difficult to interpret. Rather than trying to justify these coefficients post hoc, we addressed the concern directly by removing the gravity-weighted index from the manuscript entirely. In the revised analysis, no numerical weights are assigned to the gravity-impact categories.

      Instead, we now calculate a Gravity Index separately for each measure and each gravity-impact level, and compare these indexes between Study 1 and Study 2 using Bayesian cumulative logit models. This approach preserves gravity impact as a categorical factor, avoids imposing an arbitrary linear weighting structure, and allows the cross-study comparison to be tested directly within each gravity-impact level. We have revised the Methods accordingly and describe this new analysis in detail (lines 140-147, 276-280, 658-666, 692-717). Thus, the revised manuscript no longer depends on the arbitrary GWI coefficients.

      (R2.19) Lines 547-555 - GWI notation and coefficients: (c) The composite expression in equation (1) - as currently typeset - reads as "Gravity minus Weighted Index"; please correct the formatting so it unambiguously reads as a gravity-weighted index.

      We corrected the manuscript accordingly (lines 702-706).

      (R2.20) P-values throughout the manuscript are reported without a leading zero (e.g., "p = .39") while Cohen's d values and other statistics include one. Please adopt a consistent convention; in line with APA 7 and most journal styles, all values between −1 and 1 should include a leading zero.

      Our statistics generally follow the APA 7th guidelines (https://apastyle.apa.org/instructional-aids/numbers-statistics-guide.pdf), which state: Put a zero before the decimal point when a number is less than 1 but the statistic can exceed 1. Do not use a zero before a decimal when the statistic cannot be greater than 1 (proportion, correlation, level of statistical significance). There was a formatting error in one of the tables (Table 3), which has now been corrected.

      (R2.21) The authors should either apply a correction for multiple comparisons to game-level t-tests or acknowledge this limitation explicitly and interpret game-level results as exploratory rather than confirmatory.

      See R1.1 and R2.1. We have revised the manuscript to clarify that each game was treated as a distinct physical-reasoning problem, and these were used to localize the games in which the stimulation effect was expressed, not to compare games with one another or to draw broad conclusions from isolated contrasts (and therefore, in this case, no multiple-comparison corrections are required; lines 637-640). That said, to address the reviewer’s concern directly and to strengthen our conclusions in the paper, we also added mixed-effect models using gravity impact level and stimulation type as fixed factors and participant and game as random effects for each study (lines 168-177, 202-207, 257-259, 301-303, 641-651, Tables 2 and 4).

      (R2.22) Discussion, circa line 274 (state of the body): The authors assert that their manipulation alters the body's gravitational state. This claim deserves qualification. Gravity perception results from distributed multisensory integration; the vestibular system is one contributor, but proprioception, vision, and visceral signals are equally involved. Moreover, altering gravity visually and disrupting vestibular signals does not approximate the full-body gravitational reweighting that occurs in real altered-gravity environments. This is not a fatal limitation, but the authors should acknowledge it more directly and discuss how their results might differ from findings in truly altered gravity contexts (e.g., parabolic flight or centrifuge experiments).

      We agree that our manipulation should not be described as equivalent to the full-body gravitational reweighting that occurs in real altered-gravity environments. GVS perturbs vestibular signalling while other sensory inputs remain anchored to 1g, whereas parabolic flight or centrifuge paradigms alter the gravitational context of the body more globally. We have revised the Discussion to make this distinction explicit and to qualify the scope of our claims accordingly (lines 353-359).

      At the same time, the distinction between full-body and partial gravitational manipulation does not undermine the logic of the present study. Parabolic flight or centrifuge paradigms would not be appropriate for the physical-reasoning task used here. Moreover, the parabolic-flight study by Kunavar et al. (2021), which the reviewer helpfully highlighted, also involved a mismatch between proprioceptive and vestibular signals. Taken together, these findings suggest that manipulating one important component of the gravity-processing system can still alter behaviour, while also leaving open the possibility that stronger or different effects may emerge when sensory conflict is reduced. We have incorporated this point in the revised Discussion (lines 356-370).

      (R2.23) Discussion, around line 290 (perturbing the body helps cognition): The authors make the interesting observation that vestibular perturbation can be beneficial in altered-gravity contexts. This resonates with a finding by Kunavar et al. (2021), who showed that restoring terrestrial gravity at the hand-environment interface while the body was immersed in real altered gravity during parabolic flight paradoxically improved performance - even though the gravitational context was incoherently distributed across body segments. That study suggests a broader principle: mismatch or perturbation within the sensorimotor system does not necessarily degrade cognition and may, in some circumstances, facilitate adaptation. The present results fit within this framework, and the authors should engage with this literature. The distinction between real and virtual gravitational manipulation is not merely semantic: even genuine immersion in microgravity during parabolic flight has been shown to be insufficient to update internal gravity representations unless paired with active sensorimotor engagement (Rannaud Monany et al., J Neurophysiol, 2022), which raises the question of whether a passive vestibular perturbation such as GVS can be expected to drive the kind of cognitive recalibration the authors propose.

      We thank the reviewer for drawing our attention to the work by Kunavar et al. (2021). We agree that this study is highly relevant, and we have now incorporated it into the Discussion (lines 360-364). We also agree that the work by Rannaud Monany et al. (2022) is important for interpreting our findings, and we now discuss it explicitly in the revised manuscript (lines 365-370).

      We have clarified our interpretation of the reviewer’s point about whether passive vestibular perturbation can drive cognitive recalibration. Our study did not involve passive exposure to GVS alone. Rather, participants reasoned about physical events while vestibular signalling was being perturbed. This is conceptually aligned with the conclusion of Rannaud Monany et al. (2022), where mere exposure to microgravity was not sufficient to update internal models, but exposure coupled with task-relevant motor imagery was. Similarly, in the present study, GVS was coupled with active physical reasoning, which we argue is critical for interpreting the observed effects.

      (R2.24) Discussion, circa line 295 (internal model of gravity): A natural reference point for the predictive coding discussion is McIntyre, Zago, Berthoz, and Lacquaniti (2001, Nature Neuroscience, "Does the brain model Newton's laws?"), which provides direct neurophysiological evidence for an internalized Newtonian physics engine in the brain. This paper should be cited here.

      We agree with the reviewer that this reference is relevant and added it to the manuscript (line 373).

      (R2.25) Discussion, circa line 352 (sensory modalities and adaptation): The proposal that vestibular perturbation accelerates the revision of gravity priors is intriguing. The authors should consider whether an analogous argument applies to visual and proprioceptive channels. They should also acknowledge that sustained adaptation to a novel environment requires not only a perturbation mechanism but also veridical, graded feedback so that the system can converge on an accurate updated model - a condition that is only partially met in the present paradigm.

      See R2.22. We revised the manuscript accordingly (lines 356-370).

      (R2.26) Discussion, closing paragraph (variability and adaptability): The authors raise the positive role of noise in living systems. This connects to a well-developed body of work on optimal movement variability (Stergiou and colleagues), which formalizes how neither too little nor too much variability is optimal for adaptive performance. This framework may help situate the authors' findings within a broader theoretical account of why controlled noise injection is beneficial in both biological and artificial systems. On the computational side, the same principle underlies several foundational algorithms: stochastic gradient descent (and its mini-batch variants) outperforms deterministic gradient descent in non-convex optimization landscapes; simulated annealing uses controlled random perturbation to escape local minima; Langevin dynamics leverages noise for efficient Bayesian sampling; and dropout regularization in deep neural networks injects noise during training to improve generalization. These are canonical examples where noise is not merely tolerated but functionally necessary - a point that strengthens the authors' broader theoretical message.

      We thank the reviewers for their suggestion and revised our manuscript accordingly (lines 385-390)

      Welling, M., & Teh, Y. W. (2011). Bayesian learning via stochastic gradient Langevin dynamics. In Proceedings of the 28th international conference on machine learning (ICML-11) (pp. 681-688).

      Stergiou, N., & Decker, L. M. (2011). Human movement variability, nonlinear dynamics, and pathology: is there a connection?. Human movement science, 30(5), 869–888. https://doi.org/10.1016/j.humov.2011.06.002

      Moss, F., Ward, L. M., & Sannita, W. G. (2004). Stochastic resonance and sensory information processing: a tutorial and review of application. Clinical neurophysiology : official journal of the International Federation of Clinical Neurophysiology, 115(2), 267–281. https://doi.org/10.1016/j.clinph.2003.09.014

      Sherman, S. O., Greenstein, M., Basner, M., Clark, T. K., & Anderson, A. P. (2023). Effects of additive sensory noise on cognition. Frontiers in human neuroscience, 17, 1092154. https://doi.org/10.3389/fnhum.2023.1092154

      Reviewer #3 (Public review):

      (R3.1) The main weakness of the manuscript is that its central conclusion is not strongly supported by the data. The key finding depends on a marginally significant cross-study comparison, whereas direct GVS-versus-Sham differences in Study 2 are minimal across aggregate measures. In addition, many game-level analyses involve a large number of uncorrected multiple comparisons, raising the possibility that some of the reported effects may reflect chance findings. The manuscript's most important metric, the Gravity-Weighted Index, was not preregistered and is exploratory in nature, yet it is treated as a primary basis for confirmatory conclusions.

      See R1.4 and R2.2. We moved away from the GWI method to apply a more robust comparison between the two studies. We agree that the original gravity-weighted index was not sufficiently justified because it combined the three gravity-impact levels, using numerical weights of 1,2, and 3. Although these weights followed the ordinal classification of the games, they were not independently validated and could therefore make the cross-study comparison difficult to interpret. To address this concern directly, we removed the gravity-weighted index entirely. In the revised manuscript, we instead use a Gravity Index that is calculated separately for each measure and each gravity-impact level, as the ratio between performance or strategy outcomes under GVS and Sham. This removes the arbitrary weighting scheme and provides a direct estimate of the stimulation effect within each gravity-impact category.

      We then compared these Gravity Indexes between Study 1 and Study 2 using mixed-effect models that include study and gravity-impact level as fixed factors, rather than collapsing across gravity-impact levels with our defined weights. We used the participant as a random factor. Because the indexes are bounded and showed clustering at structural values, we analysed them using Bayesian cumulative logit models, which are appropriate for bounded, non-normally distributed outcomes and allow the cross-study contrasts to be estimated without imposing a linear weighting structure. We also clarified how the gravity-impact categories were defined, based on piloting and previous computational modelling work in the lab, and report the classification of each game in Extended Data Table 1. These revisions directly address the reviewer’s concern by replacing the arbitrary weighted composite with a transparent, category-specific analysis of the GVS effect across terrestrial and altered-gravity contexts, in line with frameworks outlined by James et al. (2021), Li et al. (2023), Liu et al. (2017) (lines 140-147, 276-292, 307-317, 588-594, 658-666, 692-717, Table 5, Fig 5, Extended data Fig 3).

      James, N. T., Harrell Jr, F. E., & Shepherd, B. E. (2021). Bayesian cumulative probability models for continuous and mixed outcomes. arXiv preprint arXiv:2102.00330.

      Li, C., Tian, Y., Zeng, D., & Shepherd, B. E. (2023). Asymptotic properties for cumulative probability models for continuous outcomes. Mathematics, 11(24), 4896.

      Liu, Q., Shepherd, B. E., Li, C., & Harrell Jr, F. E. (2017). Modeling continuous response variables using ordinal regression. Statistics in medicine, 36(27), 4316-4335.

      Manuguerra, M., Heller, G. Z., & Ma, J. (2020). Continuous ordinal regression for analysis of visual analogue scales: The R package ordinalCont. Journal of Statistical Software, 96, 1-25.

      (R3.2) The cross-study comparison is also difficult to interpret because the two studies differ in participant samples, number of games, and partially in the stimulus set.

      We thank the reviewer for this comment. We have now clarified that the cross-study comparison was based on games that were common to Study 1 and Study 2 (lines 713-714). In addition, the indices were calculated in the same way in both studies, allowing us to compare the relative effect of GVS across the two experiments rather than relying on differences in raw performance between the two participant samples. We have emphasised this point in the revised manuscript (lines 712-715).

      (R3.3) Finally, the mechanistic claims in the Discussion-particularly those invoking predictive coding, stochastic resonance, or updating of internal gravity models-go well beyond what can be directly inferred from the present behavioral data.

      We took the reviewer’s advice, along with previous comments by the other reviewers and now added further findings in the literature, strengthening our claims in the Discussion (lines 356-370, 385-390).

      Reviewer #3 (Recommendations for the authors):

      (R3.4) Moderate the scope of the main conclusions. As currently presented, the results seem to support at most the possibility that vestibular gravity signals influence a limited subset of physical reasoning tasks under specific conditions, rather than physical reasoning more broadly. The manuscript would benefit from either a more cautious interpretation or additional supporting evidence from follow-up experiments.

      We revised the manuscript accordingly (lines 398-410, 423-436).

      (R3.5) Apply an appropriate correction for multiple comparisons to all game-level analyses (for example, FDR correction) and report clearly which effects remain significant after correction…A mixed-effects modeling approach, with the game treated as a random effect within participants, would also provide a more principled and statistically powerful analysis.

      See R1.1. We have revised the manuscript to clarify that each game was treated as a distinct physical-reasoning problem, and these were used to localize the games in which the stimulation effect was expressed, not to compare games with one another or to draw broad conclusions from isolated contrasts (and therefore, in this case, no multiple-comparison corrections are required; lines 637-640). That said, to address the reviewer’s concern directly and to strengthen our conclusions in the paper, we also added mixed-effect models using gravity impact level and stimulation type as fixed factors and participant and game as random effects for each study (lines 168-177, 202-207, 257-259, 301-303, 641-651, Tables 2 and 4).

      (R3.6) Provide a clearer justification for the classification of gravity dependence (low/medium/high) and for the weighting scheme used in the Gravity-Weighted Index. It would be helpful to report the quantitative criteria or validation procedure used to assign these categories, and to include sensitivity analyses showing whether the main findings are robust to alternative weighting schemes (for example, equal or binary weights). Treating gravity dependence as a continuous predictor could also strengthen the analysis.

      See R3.1. We abandoned the weighting system and use a Baysian cumulative logit model which does not imply any arbitrary weighting instead (lines 140-147, 276-292, 307-317, 588-594, 658-666, 692-717 , Table 5, Fig 5, Extended data Fig 3).

      (R3.7) Discuss the limitations of the cross-study comparison more explicitly. The two studies differ in participant samples, numbers of games, and partially in the task set, which makes the comparison difficult to interpret. At a minimum, the manuscript would benefit from a fuller comparison of participant demographics and other relevant characteristics.

      See R3.1. We used an indexing process which normalizes the data and isolates a relative effect. While raw scores could not be used to directly compare across the two studies, the use of a standardized scale allows valid comparisons between the experiments. We revised the manuscript accordingly (line 142-144).

      (R3.8) Ideally, future work should test Earth-gravity and altered-gravity conditions within the same participants.

      We agree that testing terrestrial- and altered-gravity conditions within the same participants would be a valuable design. However, we could not implement this approach for safety reasons, as it would have substantially increased each participant’s total exposure to GVS. The current design kept GVS exposure within acceptable safety limits, and we have now clarified this point in the revised manuscript and cited the work by Utz et al. related to safety limits (lines 619-620).

      Utz, K. S., Korluss, K., Schmidt, L., Rosenthal, A., Oppenländer, K., Keller, I., & Kerkhoff, G. (2011). Minor adverse effects of galvanic vestibular stimulation in persons with stroke and healthy individuals. Brain Injury, 25(11), 1058-1069.

      (R3.9) Address the lack of a direct manipulation check for GVS more explicitly. If any subjective reports related to dizziness, discomfort, or vestibular disturbance were collected, these could be reported as an indirect validation of the manipulation. If no such data are available, this limitation should be acknowledged clearly, and future work should consider including an independent validation measure such as postural stability.

      We thank the reviewer for raising this point. In our experiment, the maximum intensity was set at 1mA, which is well tolerated. There are no side effects with these GVS parameters. The stimulation protocol used a stochastic waveform, consisting of an alternating sum-of-sines voltage with dominant frequencies at 0.16, 0.32, 0.43, and 0.61 Hz, which has been used in previous studies, both in our and other labs. We have now added this information to the manuscript by citing the work of Zanchi et al. that used the same GVS protocol (lines 613-614).

      Zanchi, S., Cuturi, L. F., Sandini, G., Gori, M., & Ferrè, E. R. (2023). Vestibular contribution to spatial encoding. European Journal of Neuroscience, 58(9), 4034-4042.

      (R3.10) Reconsider the decision to collapse the 0.5g and 2g conditions into a single altered-gravity category. Even if the two conditions do not differ significantly in the current dataset, they are cognitively distinct manipulations, and combining them may obscure potentially meaningful interactions. Separate analyses, or at least explicit interaction tests, would strengthen the interpretation.

      We agree that 0.5g and 2g are cognitively distinct manipulations and that collapsing them should be justified statistically. We therefore conducted additional mixed-effects models including gravity level (0.5g vs 2g) as a factor (see responses R1.1 and R3.5). These analyses did not reveal significant differences between the two gravity levels for the relevant performance or strategy measures (lines 248-253). On this basis, we retained the aggregation of the 0.5g and 2g conditions as a single altered-gravity category in the main analyses.

      (R3.11) Clarify the interpretation of the tool-switching results. At present, the manuscript appears to invoke different post hoc explanations for different patterns of switching behavior, including increased exploration noise and reduced cognitive flexibility. The authors should either provide a more constrained interpretation or acknowledge more clearly that the current data do not distinguish between these possibilities.

      Increased switching can reflect a less stable or less efficient strategy, but in the context of a small number of attempts, indeed it may also reflect adaptive exploration or cognitive flexibility. The present data do not allow us to distinguish conclusively between these possibilities. We have therefore revised the Discussion to provide a more constrained interpretation and to acknowledge explicitly that the meaning of the switching-rate effects remains uncertain (lines 448-452).

      (R3.12) Expand the discussion of alternative explanations. In particular, the manuscript should address whether the observed effects could reflect non-vestibular influences of GVS, such as distraction, discomfort, changes in arousal, or anxiety-related effects, rather than a specific influence on physical reasoning.

      We thank the reviewer for this excellent suggestion. We agree that non-vestibular effects of GVS, including distraction, discomfort, arousal, or anxiety-related influences, should be considered. We have therefore revised the Discussion to acknowledge this possibility more explicitly. At the same time, the pattern of results argues against a primarily non-specific explanation: if GVS had mainly affected general attention, arousal, or discomfort, we would expect a broader impairment across games. Instead, the effects were limited to specific games and were related to the gravity relevance of the task. We have clarified that this selective pattern supports an interpretation in terms of gravity-dependent physical reasoning rather than a general consequence of stimulation, while still acknowledging the broader possible influences of GVS (lines 398-411).

      (R3.13) Acknowledge more explicitly that the Virtual Tools task depends on multiple cognitive processes in addition to physical reasoning, including visuospatial ability, executive function, and trial-and-error learning. A non-physical visuospatial control task would be helpful in future work for assessing the specificity of the reported effects.

      We agree with the reviewer and revised the manuscript accordingly (lines 437-438).

    1. Author response:

      The following is the authors’ response to the original reviews.

      Note added by the authors, October 2026:

      In preparing the data deposit for the Version of Record we carried out a figure-level traceability audit of all 101 panels of the paper, recomputing every published statistic from the value table that produced the plot. This identified a small number of corrections, which are being made in the Version of Record.

      The substantive one is in Figure 6d. The CS × opsin interaction was reported as F(1,12) = 10.91, P = 0.0063; the correct value is F(1,12) = 19.87, P = 0.0008. The analysis as stored declared the repeated-measures factor on the opsin rather than on the CS, which is not the design: opsin is a between-subjects factor. The data, the group means and the effect size are unchanged, the corrected effect is stronger rather than weaker, and the conclusion — that photoactivation of the SST+ vlPAG–RVM pathway abolishes fear-induced analgesia — is unaffected.

      In Figure 1—figure supplement 3, panels e and g have been redrawn so that each bar equals the ratio of the cell counts printed on it; the eight percentages concerned have been corrected in the figure and in the legend. The cell counts themselves are unchanged, and no statistical test is applied to these panels.

      The remaining corrections are to reported details: the names of the statistical tests in the legends of Figures 1f and 4e, the number of cells in Figure 4d (n = 12) and in Figure 5f right (n = 8, and the JAX stock number of the Sst-IRES-Cre line (013044).

      The source data behind every quantitative panel of the paper are openly deposited in the Dryad Digital Repository: https://datadryad.org/dataset/doi:10.5061/dryad.63xsj3vj3

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      In the manuscript by Winke et al, the authors present evidence that fear-induced analgesia is mediated by somatostatin projection cells from the vlPAG to the RVM. This study uses a mouse model of fear-induced analgesia, and incorporates optogenetic circuit manipulation with behaviour and electrophysiology to gain a meaningful insight into a novel circuit involved in fear-induced analgesia.

      Strengths:

      (1) This is a well-constructed study with appropriate controls and analyses.

      (2) Alternative interpretations of the data are systematically considered and eliminated via rational experiments. The authors are commended for a nice piece of experimental work.

      (3) The vlPAG is a known region of pain modulation, and this study adds valuable insight to the circuit involved in fear-associated analgesia.

      We are very thankful to the referee for these positive comments.

      Weaknesses:

      (1) Only male mice are included in this study.

      We thank the reviewer for this point. We used only males in this first study for practical reasons to work with a population as homogeneous as possible. However, taking sex differences in biological mechanisms into account, we included this restriction in the summary and discussion

      (2) Animals are excluded from analyses based on clearly defined criteria, but it is not clear how many mice were excluded from each group.

      We thank the reviewers for raising this point. As stated in the Methods, we applied strict inclusion criteria for mice undergoing the hot-plate test, specifically a discrimination index ≥ 0.4 and a conditioning index ≥ 0.3. Using these criteria, 23% of wild-type mice were excluded for failing to meet the discrimination criterion. In the transgenic groups, an average of 20% of mice failed to meet the learning criteria, and an additional 12% were excluded due to incorrect opsin injection or misplaced optic fiber placement.

      (3) The authors implement a pain sensitivity assay that involves a hot plate with progressively increasing temperature. The time to nociceptive responses is reported. Without reporting the actual temperature at which the mice respond, it makes it difficult to compare nociceptive responses to previously published work (which typically use a defined and static hotplate temperature).

      We thank the reviewer for this comment. We provided this information related to the actual temperature of the nociceptive response in the original manuscript in supplementary figures 1, 2 and 5.

      (4) The authors present evidence that inhibition of SST vlPAG cells enhances spinal nociceptive electrophysiological responses, but the corresponding pain sensitivity is not altered (Figure 2, CS- condition). The reason for the discrepancy between electrophysiological and behavioural responses is not clear.

      We believe this comment arises from a misunderstanding of our results. In our study, inhibiting SST+ vlPAG cells did not increase nociceptive electrophysiological responses. Instead, it decreased spinal nociceptive transmission, as evidenced by reduced nociceptive field potentials and WDR responses in Figure 4c,e. Consistent with this electrophysiological effect, photoinhibition of SST+ vlPAG cells also produced behavioral analgesia, as evidenced by increased nociceptive response latency in the hotplate test under both CS− and CS+ conditions (Figure 2f). Therefore, our electrophysiological and behavioral findings are not contradictory but instead support the conclusion that inhibiting SST+ vlPAG cells reduces pain sensitivity regardless of defensive state. We will revise the text to clarify this point.

      Reviewer #2 (Public review):

      Summary:

      Wenke et al. investigated the role of vlPAG somatostatin-expressing neurons in the mediation of analgesia during defensive states. A newly developed paradigm of cued fear-conditioned analgesia, which consists of a combination of an auditory fear retrieval session and a pain test, was used to evaluate this cell population's contribution to fear-mediated analgesia. Optogenetic manipulation of vlPAG SST+ neurons modulated the responses to a nociceptive cue (Hot Plate) presented concomitantly with an aversively conditioned tone. At the same time, alterations in the freezing levels could be observed during optogenetic activation of vlPAG SST+ neurons. In order to disentangle the impact of these cells on analgesia from their impact on the expression of defensive behaviors, the authors performed electrophysiological recordings from the dorsal horn in the spinal cord of anesthetized mice. A vlPAG-RVM-DH pathway was identified to trigger nociceptive C-fibers upon optic activation of the RVM. Finally, pathway-specific activation of SST+ vlPAG-RVM neurons could abolish CS-induced analgesia.

      Strengths:

      The study addresses a relevant topic, that is, brainstem circuits for pain-modulatory mechanisms as part of defensive states evoked by threat. This is important because the circuit mechanisms underlying pain are still not fully understood, and defining molecular markers of cellular circuit substrates may support the identification of potential pharmaceutical targets in treating pain. The authors confirm a previous study in that a somatostatin-positive cellular population presents a crucial vlPAG circuit element mediating anti-nociceptive effects. Key novelty aspects of the present study are the demonstration that these neurons seem to play a role specifically in threat-induced analgesia. This was possible by the elegant design and application of a novel fear analgesia paradigm, combined with cell- and pathway specific optogenetics.

      We thank the referee for such positive feedback.

      Weaknesses:

      Despite the convincing and rigorous experimental approach, the study leaves some interpretational room when it comes to the proposed circuit mechanism. This could either be addressed by additional experiments or by more discussion of alternative circuit layouts.

      Major Comments:

      (1) The paper by Zhang et al. (https://pubmed.ncbi.nlm.nih.gov/36641028/), which identified a role for vlPAG SOM+ neurons in mediating anti-nociception in neuropathic pain, needs to be referenced and its results discussed, if not reconciled. While functionally, both studies find an analgetic role of vlPAG SOM+ neurons projecting to the RVM, Zhang et al., using slice physiology, characterize those neurons as glutamatergic. In Figure 4E of Zhang et al. they find general (fear-independent) analgetic effects with PAG-RVM specificity by performing chemogenetic experiments.

      We thank the reviewer for highlighting this important point. We agree that the study by Zhang et al. is highly relevant and should be discussed in the revised manuscript. Their work shows that inhibiting vlPAG SST/SOM neurons with chemogenetic methods produces analgesia in a neuropathic pain model, and in our study, we similarly found that inhibiting SST+ vlPAG neurons increases hotplate response latency (Figure 2f), which aligns with an analgesic effect. Additionally, we observed that activating SST+ vlPAG neurons suppresses fear-conditioned analgesia.

      At the same time, there are important differences between the two studies that may explain the differences in interpretation. First, the behavioral paradigms are not identical. Zhang et al. used a hotplate protocol where animals were directly exposed to a nociceptive temperature, whereas in our study, we used a progressive temperature ramp and explicitly compared responses during a conditioned stimulus (CS+) and a non-conditioned control stimulus (CS−). These controls were important for us to distinguish fear-specific effects from more general effects related to stress, arousal, sensitization, or other non-associative processes.

      Second, the two studies differ in experimental context. Zhang et al. examined this circuit in a neuropathic pain model, whereas our study focused on acute nociceptive processing and fear-conditioned modulation of pain. We therefore believe that the apparent discrepancy might reflect differences in pain state and behavioral context, rather than a direct contradiction.

      Finally, Zhang et al. showed in slice recordings that SST+ vlPAG neurons provide excitatory input to RVM neurons. This is an important finding that we now address in the revised manuscript. At the same time, because the RVM contains heterogeneous neuronal populations with different projection targets and functions, these recordings alone do not prove that all recorded RVM neurons are part of the descending pathway controlling spinal nociception. Therefore, we have revised the Discussion to explicitly acknowledge Zhang et al. and to emphasize both the similarities and differences between the two studies.

      It can be argued that in addition to the two functionally distinct inhibitory SOM subtypes hypothesized by Winke et al., there is another, excitatory subpopulation. Also, the different experimental conditions (chronic vs. acute pain, non-threat vs. fearful cues/contexts may recruit different vlPAG SOM+ populations. All of this is conceivable, yet I wonder whether the contrasting findings could more parsimoniously be reconciled. The author's own results presented here in Supplementary Figure 3 suggests that SOM+ vlPAG cells are colocalizing with glutamate and thus could also be excitatory. In addition to this rather complementary piece of evidence, a more extensive characterization of vlPAG neurons using IHC and slice physiology would be needed to justify the unambiguous identification of their inhibitory nature.

      We thank the reviewer for this thoughtful comment. We agree that our current data do not support a definitive conclusion that all SST+ vlPAG neurons are inhibitory. As the reviewer notes, our Supplementary Figure 3 shows that SST+ vlPAG cells can also co-localize with glutamatergic markers, which is consistent with the possibility of cellular heterogeneity within this population. We also agree that different experimental conditions, such as chronic versus acute pain and non-threatening versus fear-related contexts, may activate different SST+ vlPAG subpopulations.

      Our intention was not to claim that SST+ vlPAG neurons constitute a uniform inhibitory population, but rather that SST+ cells are strongly represented among inhibitory neurons in the vlPAG. We agree, however, that more detailed characterization, including additional immunohistochemical analyses and slice physiology, is necessary to more definitively determine the neurotransmitter phenotype and functional connectivity of these neurons. We have therefore revised the text to temper our interpretation and to explicitly acknowledge the likely heterogeneity of SST+ vlPAG neurons, including the possibility of an excitatory subpopulation. We therefore modified the discussion accordingly:

      “Our results align with the parallel inhibition- excitation model, where inhibitory and excitatory cells form two distinct, parallel descending pathways for pain modulation.

      Indeed, previous research demonstrated the presence of an inhibitory pathway projecting throughout the PAG–RVM-spinal cord dorsal horn neuraxis. Our results complement this study by suggesting that one of these previously proposed parallel pathways is mediated by SST+ vlPAG cells and has a functional role in mediating analgesia. At the same time, our data indicate that vlPAG SST neurons are heterogeneous, with approximately one-third of these cells co-localizing with excitatory markers. Together with the recent observation that excitatory SST+ vlPAG neurons project to the RVM (Zhang et al., 2023), this raises the possibility that a subset of long-range SST+ vlPAG neurons contributes to an excitatory descending pathway within the PAG–RVM–spinal dorsal horn neuraxis. By contrast, local GABAergic SST+ vlPAG neurons may participate in local circuit mechanisms related to defensive-state expression, including freezing. Further anatomical and functional studies will be required to resolve these possibilities.”

      In the absence of a direct identification of these cells exclusively releasing GABA, an alternative explanation should be considered. What about looking at vlPAG SOM+ neurons as a putatively mixed bag of local, inhibitory interneurons and long-range, RVM-projecting excitatory cells? This model would then open up interesting questions as to the actual function of somatostatin as a modulator of vlPAG circuit activity and associated function, and from my perspective, would nicely fit into the view of PAG circuits as integrators of complex survival responses.

      We thank the reviewer for this insightful suggestion and agree that, in the absence of direct evidence that vlPAG SOM+/SST+ neurons are exclusively GABAergic, an alternative interpretation should be considered. In particular, we agree that this population may be heterogeneous and could include both local inhibitory interneurons and long-range excitatory neurons projecting to the RVM. We believe this is an important and constructive framework for interpreting our data, and we have revised the Discussion accordingly. In the revised text, we now explicitly acknowledge the likely heterogeneity of vlPAG SST+ neurons and discuss the possibility that distinct local and long-range SST+ subpopulations may contribute differently to defensive-state regulation and descending pain modulation. We agree with the reviewer on this point and have modified the discussion accordingly (see point above).

      (2) "Our data indicate that the optogenetic inhibition of SST+ vlPAG cells promotes analgesia irrespective of the animal's defensive state. In contrast, the optogenetic activation of long-range SST+ vlPAG cells that project to the rostral ventromedial medulla (RVM) abolishes the analgesia mediated by fear behavior." (lines 32-35). Consider toning down these conclusions, as contrasting activation with inhibition of two different (though overlapping) populations cannot be fully conclusive. Alternatively, a pathway-specific (vlPAG-RVM) inhibitory experiment could help to fully understand the circuit mechanism and verify the necessity of these neurons.

      We thank the reviewer for raising this point. We agree that inhibition of the entire SST+ vlPAG population and activation of the long-range SST+ vlPAG neurons projecting to the RVM population are not directly equivalent manipulations. Our conclusion was intended at the level of observed functional effects: inhibition of SST+ vlPAG neurons promotes analgesia regardless of the defensive state, while activating long-range SST+ vlPAG neurons projecting to the RVM suppresses fear-conditioned analgesia. This occurs regardless of whether the SST vlPAG neurons are excitatory or inhibitory. To address the excitatory or inhibitory nature of SST vlPAG neurons, we have revised the discussion to include a reference to the Zhang et al study.

      (3) Despite an overall very thorough reporting style, some information is missing from the manuscript:

      (a) In Figures 2d and f, what are the freezing levels during optogenetic manipulation? From Figure 3d, one can expect that freezing is inhibited during the hot plate test, which could bias the NC response towards shorter latencies.

      We thank the reviewer for this important comment. As shown in Figure 1e, we previously quantified freezing both at CS onset and at the time of the nociceptive response in the hot plate test. These analyses indicate that freezing levels at the time of the nociceptive response do not differ between the CS+ and CS− conditions. Therefore, the variation in hot plate response latency is unlikely to be due to differences in freezing at the time of response.

      We acknowledge, however, that freezing was not directly measured during optogenetic manipulation in this experiment. Based on the temporal profile of freezing shown in Figure 1e, we still consider it unlikely that the effect of optogenetic manipulation on nociceptive latency is mainly caused by a change in freezing behavior.

      (b) In Figure 5, the histological experiment showing the vlPAG-to-RVM pathway is presented by a qualitative image only. Here, some quantification would strengthen the finding.

      We thank the reviewer for this comment. The aim of the histological experiment in Figure 5 was to provide qualitative anatomical evidence that vlPAG projections reach the RVM and are positioned in close apposition to spinally projecting RVM neurons. We did not intend this experiment to serve as a quantitative characterization of connectivity. We agree that a more systematic quantification would be informative, but this would require additional dedicated experiments beyond the scope of the present manuscript.

      (c) In Figures 6 c and d "Consistently, activation of the SST+ vlPAG-RVM pathway during CFCA had no impact on CS-presentation, whereas the same manipulation performed during CS+ blocked the increase in NC response latency compared to GFP controls." (line 194-196). Is it possible that the NC response cannot be any lower than the one during CS-, thus constituting a floor effect?

      We are thankful to the reviewer for this important point. We agree with the reviewer that this is indeed a possibility. We have added a sentence in the discussion to acknowledge this limitation.“Another possibility is that our nociceptive test with a slow ramp of temperature induces a floor effect on nociceptive response latency, which may limit the detection of further decreases in latency under certain conditions.”

      (c) Connected to major point 1- this experiment is important for defining the circuit mode and therefore should be as convincing as possible. However, for the colocalization experiment in Supplementary Figure 3, the methodological description is missing and thus makes it hard to comprehend how this data set was generated (how many data points, etc.). The visual depiction of the results is non-standard and not easily graspable. Consider e.g., a Venn diagram.

      We apologize for this omission in the original manuscript. We have now provided this methodological information in the method section. We have now expanded the description of these data in the figure legend to ease the comprehension of the figure.

      Reviewer #3 (Public review):

      Summary:

      Conditioned analgesia refers to the ability of a learned fear cue to suppress pain-related behavior and neural activity. Understudied, the authors developed a novel conditioned analgesia procedure in which a cue that had been paired or unpaired with shock was played while a hot plate increased temperature. Compared to several control conditions, the authors found increased latency to a nociceptive response (paw licking). The authors identified somatostatin neurons in the periaqueductal gray as a likely mediator of the behavior. They then showed that: (1) stimulating vlPAG-SST neurons blocked nociceptive response latency increases to the CS+, (2) stimulating vlPAG-SST neurons suppressed fear retrieval freezing, (3) stimulating vs. inhibiting vlPAG-SST neurons drove opposing modulation of c-fibers and Aδfibers, (4) direct-projecting vlPAG SST neurons modulate freezing while RVM-projecting vlPAG SST neurons modulate conditioned analgesia.

      Strengths:

      These experiments have many strengths. The behavioral assay is chief among them. The assay is robust and controls for confounding factors to reveal a repeatable effect of a shock-paired cue to delay nociceptive responding. The optogenetic experiments provide the correct level of temporal precision, given the authors' time-specific interest in cued responding. Combining neuronal manipulations with spinal recordings is particularly innovative, especially in the context of more behavioral neuroscience-based assays. All-in-all, I found this to be an exceptionally strong set of experiments.

      Weaknesses:

      No obvious weaknesses were identified by this Reviewer.

      Recommendations for the authors:

      Comments from Reviewing Editor:

      Summary

      Three reviewers have assessed your manuscript on vlPAG somatostatin pathways contributing to conditioned analgesia. Conditioned analgesia refers to the ability of a learned fear cue to suppress pain-related behavior and neural activity. Understudied, the authors developed a novel conditioned analgesia procedure in which a cue that had been paired or unpaired with shock was played while a hot plate increased temperature. Compared to several control conditions, the authors found increased latency to a nociceptive response (paw licking). The authors identified somatostatin neurons in the periaqueductal gray as a likely mediator of the behavior. They then showed that: (1) stimulating vlPAG-SST neurons blocked nociceptive response latency increases to the CS+, (2) stimulating vlPAG-SST neurons suppressed fear retrieval freezing, (3) stimulating vs. inhibiting vlPAG-SST neurons drove opposing modulation of c-fibers and Aδ-fibers, (4) direct-projecting vlPAG SST neurons modulate freezing while RVM-projecting vlPAG SST neurons modulate conditioned analgesia.

      Strengths

      All three reviewers converged on multiple strengths. The assay developed was seen to be novel, rigorous, and included a variety of controls that convincingly demonstrated conditioned analgesia. Focusing on the ventrolateral periaqueductal gray, and more specifically on somatostatin-expressing cells, made prior sense, and the results more than justified this selection. Approaching the vlPAG and circuits with many converging methods provided further, compelling evidence for a role in conditioned analgesia.

      Weaknesses

      Specific weaknesses are described in the individual reviews. Generally, the following weaknesses were identified. The study only used male mice, a choice that should be better justified. Animals were reasonably excluded from analysis, but the final group ns for analyses were not always clear. Some statistical results lacked clarity. The relevance of these findings to prior work (particularly Zhang et al. 2023, Journal of Pain) was not always described. Relatedly, the results would be better contextualized by appreciating and describing the likely diversity of somatostatin functional types and projection types.

      Recommendations

      (1) Provide rationale for only using male mice, discuss the limitation of the exclusion of females, and note that male mice were the subjects in the abstract.

      Thank you for this recommendation, we have mentioned this information in the abstract and in the discussion. We have also mentioned the limitations of not including female mice in the abstract and the discussion of the revised manuscript.

      (2) Complete final report ns for each statistical analysis. If you have not already done so, please include full statistical reporting including exact p-values wherever possible alongside the summary statistics (test statistic and df) and, where appropriate, 95% confidence intervals. These should be reported for all key questions and not only when the p-value is less than 0.05 in the main manuscript.

      An extended table with all statistical tests and analysis for all figures has been provided in sup Table 1.

      (3) Include example videos of CFCA sessions, demonstrating optogenetic effects.

      We understand the editor’s request to include video material illustrating the behavioral responses. However, we would prefer not to include such videos in the manuscript, in accordance with our institution's guidelines and recommendations on the dissemination of animal experimentation footage. Importantly, all behavioral sessions were systematically video-recorded from both sides of the apparatus, allowing detailed offline analysis of the animals’ responses. These recordings were carefully examined by an experienced experimenter to assess nociceptive behaviors, including jumping responses and licking of the stimulated hindpaw. This procedure ensured a reliable and accurate evaluation of pain-related behavioral reactivity. While the videos themselves cannot be included in the manuscript for the reasons mentioned above, we believe that the behavioral scoring procedures described in the Methods section provide a clear and rigorous description of how these responses were assessed. In addition, Figure 1 includes an example image illustrating hindpaw licking behaviour, which is typically more subtle and more difficult to identify than jumping responses. We therefore believe that this visual example, together with the detailed description of the scoring procedure and the quantitative data provided, adequately supports the interpretation of the behavioural results.

      (4) Provide summary expression and ferrule placement figures.

      We thank the editor for this comment. We have now included schematic summaries of fiber placements for both SST and VIP mice used in this study, based on histological verification (Supplementary Figures 10 and 11). Representative images of viral expression are also provided (Figure 2a, Supplementary Figure 7b and f).

      (5) Detail how behavior judgments were made.

      We thank the editor for emphasizing this important methodological point. During all behavioral sessions, mice were video-recorded simultaneously from both sides of the apparatus, allowing a comprehensive and unobstructed view of the animals’ posture and movements throughout the experiment. These recordings were subsequently analyzed offline by an experienced experimenter trained to evaluate nociceptive behaviors. Pain-related behavioral responses were assessed based on well-established indicators of nociceptive reactivity. In particular, we quantified overt escape-like reactions such as jumping, which reflects a strong aversive response to the stimulus. In addition, we evaluated more localized nociceptive behaviors directed toward the stimulated limb, including licking of the hindpaw. These measures are commonly used in rodent pain assays and provide reliable behavioral readouts of nociceptive sensitivity. The combination of bilateral video recordings and expert behavioral scoring ensured that both subtle and robust nociceptive responses could be accurately detected and categorized during the analysis.

      (6) Provide the temperature at which nociceptive responses were initiated. Check grammar and references.

      The temperature at which nociceptive responses were initiated were originally reported in Supplementary Figure 1, 2 and 5.

      Reviewer #1 (Recommendations for the authors):

      (1) The authors use optogenetic manipulation of SST activity in the vlPAG to show that this cell type is involved in fear-induced analgesia. They include a valuable control to show that manipulation of another inhibitory cell type (VIP) also does not impact analgesia. It would be helpful to know the expression level of VIP cells in the vlPAG. Is this a predominant inhibitory projection cell in the vlPAG (besides SST)?

      We thank the reviewer for pointing this. While we did not quantify the expression level of VIP+ cells in the vlPAG in the present study, available data suggest that this population is relatively sparse compared to other inhibitory cell types. In particular, reference to the Allen brain atlas indicates that VIP gene expression in the vlPAG is limited and primarily localized around the fourth ventricle, within the lateral and ventrolateral PAG, rather than broadly distributed across the region. Consistent with this, we provide an example of viral expression in VIP-Cre mice in Supplementary Figure 7f, illustrating the restricted distribution of VIP+ neurons in the vlPAG. We have also provided a summary of ferrules placement for SST and VIP mice used in our study in Supplementary Figures 11 and 10, respectively.

      (2) The numbers of animals dropped from each experiment should be indicated - perhaps on the statistics table?

      We thank the reviewer for pointing this.

      As stated in the Methods, we applied strict inclusion criteria for mice undergoing the hot-plate test, specifically a discrimination index ≥ 0.4 and a conditioning index ≥ 0.3. Using these criteria, 23% of wild-type mice were excluded for failing to meet the discrimination criterion. In the transgenic groups, an average of 20% of mice failed to meet the learning criteria, and an additional 12% were excluded due to incorrect opsin injection or misplaced optic fiber placement.

      (3) Line 105: "...,which activity..." change to "..., whose activity..."

      Done

      Reviewer #2 (Recommendations for the authors):

      (1) Please also provide absolute temperature values of the nociceptive response threshold.

      The temperature at which nociceptive responses were initiated was originally reported in Supplementary Figure 1, 2 and 5.

      (2) It would be nice to see an example video of a CFCA session (with and without optogenetic manipulation).

      We understand the editor’s and reviewer’s request to include video material illustrating the behavioral responses. However, we would prefer not to include such videos in the manuscript, in accordance with our institution's guidelines and recommendations on the dissemination of animal experimentation footage. Importantly, all behavioral sessions were systematically video-recorded from both sides of the apparatus, allowing detailed offline analysis of the animals’ responses. These recordings were carefully examined by an experienced experimenter to assess nociceptive behaviors, including jumping responses and licking of the stimulated hindpaw. This procedure ensured a reliable and accurate evaluation of pain-related behavioral reactivity. While the videos themselves cannot be included in the manuscript for the reasons mentioned above, we believe that the behavioral scoring procedures described in the Methods section provide a clear and rigorous description of how these responses were assessed. In addition, Figure 1 includes an example image illustrating hindpaw licking behaviour, which is typically more subtle and more difficult to identify than jumping responses. We therefore believe that this visual example, together with the detailed description of the scoring procedure and the quantitative data provided, adequately supports the interpretation of the behavioural results.

      (3) Please provide a schematic summary of fiber placements and opsin expressions confirmed by histological examinations.

      We thank the reviewer for this comment. We have now included schematic summaries of fiber placements for both SST and VIP mice used in this study, based on histological verification (Supplementary Figures 10 and 11). Representative images of viral expression are also provided (Figure 2a, Supplementary Figure 7b and f).

      (4) "Valid nociception readout responses included jumping or licking the hindpaw." (Line 453). How was this evaluated- manually or automated, blinded etc.?

      We thank the reviewer for emphasizing this important methodological point. During all behavioral sessions, mice were video-recorded simultaneously from both sides of the apparatus, allowing a comprehensive and unobstructed view of the animals’ posture and movements throughout the experiment. These recordings were subsequently analyzed offline by an experienced experimenter trained to evaluate nociceptive behaviors. Pain-related behavioral responses were assessed based on well-established indicators of nociceptive reactivity. In particular, we quantified overt escape-like reactions such as jumping, which reflects a strong aversive response to the stimulus. In addition, we evaluated more localized nocifensive behaviors directed toward the stimulated limb, including licking of the hindpaw. These measures are commonly used in rodent pain assays and provide reliable behavioral readouts of nociceptive sensitivity.The combination of bilateral video recordings and expert behavioral scoring ensured that both subtle and robust nociceptive responses could be accurately detected and categorized during the analysis.

      (5) Line 226 REF33 doesn't seem to fit.

      The reference list has been updated. Related to this section in which we discuss the disinhibition mechanisms inducing nociception in chronic stress mice. We have cited the work of Samineni et al., 2015 (reference 15) and Tovote el al., (reference 23) both related to these disinhibition mechanisms.

      Full sentence for reference 33 (now 35): “Two independent previous studies found that long-range inhibitory inputs from the central medial amygdala contact inhibitory cells within the vlPAG, implicated in different roles: the modulation of fear behavior (23) and nociceptive transmission (35)”.

      Ref 35 - Yin, W. et al. A Central Amygdala–Ventrolateral Periaqueductal Gray Matter Pathway for Pain in a Mouse Model of Depression-like Behavior. Anesthesiology 132,1175–119 (2020)

      (6) Some minor language, semantic, and grammatical flaws.

      The manuscript has been evaluated for language, semantic and grammatical flaws

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      Zhang et al. report on an ambitious study that investigates multiple aspects of the neural and behavioral underpinnings of auditory-motor surprisal in the context of an auditory-motor learning paradigm (piano keyboard). Using an intricate design comprising several sub-parts and control procedures, they report that early ERPs (50-100 ms latency) reflect violations of established key-pitch mappings.

      Strengths:

      This is a carefully devised and executed study. The paradigm is quite intricate and, at the same time, addresses multiple aspects of auditory-motor learning, and does so in a rigorous way.

      Weaknesses:

      Perhaps because of the exhaustive approach, it is sometimes difficult to follow which parts of the experimental design the results come from; there are some questions regarding appropriate statistical methods, the inclusion/treatment of musical background in participants, and the nature (latency & extent) of the identified neural components that detect auditory-motor violations.

      Reviewer #2 (Public review):

      Summary:

      Zhang et al. report an EEG study (n=18) of participants playing a keyboard where the correspondence between keys and pitches is varied to introduce sensory-motor mismatches (discrepancies between sensory inputs and expected sensory consequences of motor commands). They find that the auditory N100 amplitude is enhanced for the initial keystroke following a mapping switch but rapidly attenuates for subsequent keystrokes (showing rapid updating of the forward model), whereas the motor-related P50 amplitude only differentiates trained versus untrained mappings after 30 minutes of goal-directed practice (potentially showing timescales of inverse model updating). Using parallel univariate and mTRF decoding analyses, they conclude that forward models (mapping action to predicted sound) update almost instantly to track short-term context, while inverse models (mapping sound to motor commands) update slowly and require extended, targeted practice.

      Strengths

      (1) Methodological innovation:

      The study utilizes an interesting, continuous auditory-motor paradigm that moves beyond standard trial-by-trial oddball designs, offering a more ecologically valid measure of trial-to-trial adaptation.

      (2) Analytical elegance and rigor:

      The combination of traditional univariate ERP analyses with multivariate temporal response function (mTRF) decoding is elegant, allowing the authors to successfully dissociate overlapping auditory and motor variance streams.

      (3) The dissociation between the rapid adaptation of the N100 forward model and the slower adaptation of the P50 inverse model is interesting.

      Weaknesses

      (1) Confounded passive listening baseline:

      The passive listening control condition lacks an orthogonal behavioural task (e.g., an occasional oddball detection task). Active playing inherently necessitates focused attention on auditory feedback to monitor performance, whereas passive playback does not. The globally weaker stimulus-evoked pattern at electrode Fz during passive listening strongly suggests that the absence of an N100 effect in this condition may simply reflect a lower state of attention, rather than isolating the absence of a motor-driven forward prediction, in particular because the pure sensory suprisal was also enhanced for "firsts" notes, so this could also lead to stronger N1, but this effect may be masked.

      Here, our goal is to probe surprisal resulting from natural deviations of the expected sensorimotor map, and to test whether the observed response can be accounted for by the auditory components alone. In previous work, passive listening (without an explicit behavioral task) has been widely deemed sufficient to measure auditory surprisal (cf. Di Liberto 2020). Because the listener is not privy to the order of firsts and others within a session, any general attentional effects would be expected to influence all notes and therefore cannot explain the selective enhancement observed for “first” notes which follow a map change.

      (2) Overclaimed theoretical novelty:

      The conceptual framing leans excessively on the authors' specific "MirrorNet" framework, presenting foundational, decades-old tenets of the motor control literature (i.e., unsupervised exploration for forward models vs. supervised skill acquisition for inverse models; Wolpert, Jordan, both in the nineties) as their own novel "conjectures." This theory-heavy introduction obscures the paper's actual empirical contribution to the design and the interesting question regarding the distinct temporal adaptation scales of forward versus inverse models. I think some rewriting can improve the paper.

      Thank you for pointing this out. It was not our intention to present the work of Wolpert etc. as a novel conjecture. We substantially revised the Introduction to emphasize that our contribution builds upon that theoretical framework and is also a study of how this framework evolves over time. We have cited Wolpert in the Introduction, and have now integrated the forward and inverse pathways more clearly into our hypotheses about the different effects of long- versus short-term sensorimotor experience on the MirrorNet framework.

      (3) Misplaced surprisal terminology:

      In a similar vein, I find the use of the term "auditory-motor surprisal" more theoretical grandstanding than actually useful. The significance statement claims to "extend this principle from sensory processing" but in fact, the concept of sensory motor unexpectedness is again a staple of the forward motor literature. Moreover, nowhere in the paper do they actually estimate sensorimotor surprisal. While the authors compute surprisal for their auditory baseline using IDyOM, their central sensorimotor analysis relies entirely on a simple categorical mismatch (first vs. subsequent keystrokes). The phenomenon can equally be referred to by its established nomenclature-"sensorimotor mismatch" or "sensory motor unexpectedness".

      In the revised Introduction, we added a discussion of the relationship between surprisal and contextual predictions to clarify our terminology. In practice, the terms auditory-motor surprisal and sensorimotor mismatch refer to closely related phenomena. However, we chose the term surprisal because it emphasizes that prediction violations depend not only on the overall frequency of an event, but also on the context in which it occurs. In the surprisal literature, an event can be unexpected because it violates predictions generated from recent context, or long-term statistical regularities, or prior experience, even if the event itself is not objectively rare.

      This distinction is important for our paradigm. A given note may occur frequently throughout the experiment and therefore is not rare in an absolute sense. Nevertheless, the same note may be highly surprising if it occurs immediately after a key-pitch map change, thus violating the participant's sensorimotor predictions. We therefore use the term surprisal to emphasize the role of contextual expectations rather than simple deviance or rarity.

      We finally agree that, in the absence of an auditory-motor equivalent of models such as IDyOM, our study does not provide a continuous estimate of surprisal. Instead, we use the distinction between first and keystrokes as a categorical approximation of high- and low-surprisal events. Developing computational models that estimate continuous auditory-motor surprisal from the preceding sensorimotor context would be an interesting direction for future work, and we have added a note concerning this in the Conclusion.

      (4) Incremental conceptual advance regarding the N100:

      The paper frames the N100 finding as a major discovery, but as far as I know, the attenuation of the auditory N1 to self-generated sounds via accurate motor prediction-and its enhancement during sensorimotor mismatch - is one of the most heavily documented phenomena in the auditory-motor literature (e.g. Timm et al., 2013; Bendixen et al, 2012; 2013). As far as I'm concerned, the authors should clarify that the novelty lies in the novel, elegant design that provides a new way to correct for non-sensory-specific motor-induced attenuation, and characterizing the distinct adaptation timescales of forward versus inverse models -- not in demonstrating N100 modulation by sensorimotor mismatch, which is well-documented, AFAIC.

      We agree now that the main finding of the paper is not discovering N100 as a signature of sensorimotor mismatch and we have revised the Introduction as discussed above. We now instead emphasize how it evolves over time and connect it to behavioural studies of sensorimotor perturbation where a behavioural adaptation is observed after one trial. We also incorporated the suggested literature on the N100 in the Introduction and Discussion because it shows that this neural signal has been previously seen in sensorimotor mismatch studies.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      As very general feedback, I would encourage the authors to revise the manuscript so that it is much clearer which results come from which part of the experiment. For example, it took me a while to figure out that the ERP results in Figure 3 came solely from the 'Variable map playing' parts of the study (and perhaps only from the Pre-test phase?).

      To improve clarity, we have rearranged the order of the figures and the respective text to organize the article into three main parts: the Variable Playing Task (Experiment I), the Training (Experiment II), and the TRF analysis (Experiment III). The paradigm panels are now closer to the Figure explaining their results. The Figure outlining how these tasks are carried out (previously Figure 2D) during one experimental session has been relegated to the supplementary materials.

      Major:

      (1) Statistics

      (a) I couldn't shake the impression that the authors are treating the statistical analyses a bit too casually. Some analyses use parametric (ANOVA, t-test), others non-parametric tests (Wilcoxon) or bootstrapping, without explicitly reasoning for one or the other; there are also some examples where I believe no correction for multiple comparisons is applied, but should be applied (e.g., tests in Figure 4?).

      We have added information in the Methods section to clarify the statistical choices. Here is a summary of our reasoning:

      Bootstrapping (to find the difference between first and others): this was to account for the imbalance in class sizes and is more conservative than parametric alternatives. That being said, parametric tests do converge on the same result (Figure 6C, main effect of keystroke type in the 2-way within-subjects

      ANOVA).

      For Figure 4, we have replaced the pairwise tests with a more robust linear mixed-effects model to capture the relationship between the number of previous keystrokes and amplitude. This avoids multiple pairwise comparisons between conditions. However, the conclusions of the figure remain unchanged: the amplitude difference increases with the number of previous keystrokes.

      Wilcoxon tests (subject-wise differences): With N = 18 participants, we do not meet the conventional threshold for normality (n > 30). The Wilcoxon test was therefore the appropriate choice.

      Within-subjects ANOVA (training and first vs. others): A two-way within-subjects ANOVA was used when comparing two conditions. Within-subjects designs with N = 18 do not violate ANOVA assumptions in the same way between-subjects designs would, since the critical assumption is the sphericity of difference scores rather than marginal normality.

      (b) Relatedly, I am not sure it is ok to run uncorrected statistical tests to identify 'time regions of interest', and to then zoom in on these and run additional statistical tests on them; this seems conspicuously like double dipping?

      We did the uncorrected tests as an exploratory analysis, but we would have arrived at the same result if we chose timepoints of interest based on the literature (P50 and P100 were both well-documented; P250+ also potentially could have had an effect based on the literature (Lutz et al., 2013 for example), but in our experiment we did not find it).

      (c) Comparing firsts versus other keystrokes: I wonder whether the bootstrapping procedure is necessary? In the MMN literature, this imbalance (oddball vs. standard) has not been an issue, as far as I am aware (or it has not been addressed?); I can follow the authors' reasoning for addressing this imbalance, but would feel more comfortable with the bootstrapping procedure if the authors can show that there is only a quantitative, but not a qualitative difference between statistics with bootstrapping vs. without bootstrapping (i.e. having a large imbalance between firsts and others keystrokes).

      While bootstrapping is less commonly used in some ERP studies, we chose this approach because it provides a robust estimate under class imbalance between conditions, as is typical in oddball-like paradigms. The effect of firsts versus others keystrokes remains significant under standard parametric analyses, consistent with the main effect observed in the two-way ANOVA (Figure 6C).

      (d) In addition, is it really correct to derive a null distribution only from the other keystrokes, as opposed to from both firsts and other keystrokes?

      Our procedure defines a null distribution based on differences between randomly sampled other keystrokes. This allows us to quantify whether the observed amplitude difference between first and other keystrokes exceeds what would be expected from differences within the other condition alone. Under the null hypothesis, the first–other difference does not differ from the distribution of differences obtained by comparing randomly selected subsets of other keystrokes of equal size.

      (2) Latency and duration of ERP differences

      I was rather surprised by how early the effects appear to be. Coming back to the MMN paradigm: here, the latency of the peak MMN for oddballs is typically in the ~150-250 ms range, i.e. in P2 territory. Granted, the effect can be initiated in the N1 component range, but then it persists through P2; in the current paradigm, the effect is very selective to the N1 (or even the P50 latency for Pre- vs. Post-training comparisons, which puts this effect squarely in the primary auditory cortex). I would encourage the authors to explore this apparent discrepancy with respect to the MMN latency a bit more; is this related to passive vs. active paradigms? But why does the effect not persist and is seemingly restricted to a brief time window? Presumably, the auditory-motor mismatch, once it is detected, will have 'downstream' effects?

      The early N100 effect has been reported multiple times in previous literature so we don't find this result surprising. It's possible that there are downstream effects that we're not seeing here. For example, we show in Figure S13 that the playing ERP is likely a linear sum of auditory and motor signals. The motor ERP also peaks at around 150, so in theory it could obscure the classic MMN. This point was mentioned in the Discussion (line 290).

      (3) Musical background of participants

      The authors state that some participants had more than 10 years of formal musical training, but that "none of the musically trained participants played piano as their primary instrument". How many of those nevertheless played piano? And how did this affect their performance? It would have been much cleaner to restrict participants to non-musicians...

      I am not convinced that performance in the training task is an appropriate proxy for musicianship (as the authors suppose on page 10). In general, I think the consideration of musicianship in the study is by far the weakest and should probably be left out.

      That being said, it is unfortunate that not more information on participants' background is provided, and that the authors did not exclude musicians, as this likely also has an impact on the results, since they presumably have had a stronger 'natural' key-pitch mapping than non-musicians.

      Participants did fill out a questionnaire adapted from the Goldsmiths Musical Sophistication Index previously used in our laboratory’s other studies.We found no correlation with the GSI general score, nor the subscores. We have added the questionnaire results in the supplementary materials and the correlation plots for the overall musical sophistication score and the perceptual abilities score (the subscale most closely associated with the demands of our task). Nevertheless, for our use case, we do not believe that the questionnaire is more relevant for predicting sensorimotor learning abilities than the actual performance during training. For example, aspects of emotion and social engagement in music are also measured, which we don’t find to be relevant to musical learning abilities, and perceptual abilities are self-reported.

      (4) How were peak amplitudes determined? (They should not be determined by simply picking the maximum, as this is susceptible to outliers, but instead as an average over a pre-defined time window.) In general, the description of methods would benefit from being more detailed.

      We indeed computed the peak response as the maximum over a 40 ms window. However, given the large number of trials, and that the signal was already low-pass filtered to 30 Hz, corresponding to a ~33 ms cycle, it is unlikely that the estimate is significantly affected by transient noise or spurious peak fluctuations. The concern about outliers would be more relevant for single-trial data.

      (5) Figure 3A and 6A 'Pre-training ERP' seem to be identical; why is that? Shouldn't Figure 3A essentially show the average of Figure 6A 'Pre-test ERP' and 6A 'Post-test ERP'?

      Yes, it is indeed identical. Figure 3A is the variable map playing without the influence of any other tasks, therefore it’s the pre-training ERP.

      (6) I had trouble following the results in Figure 4B/D. Why does 4B only go as far as 3 previous keystrokes, but 4D goes as far as 7? Maybe I am misunderstanding something here?

      We showed only the contexts for which there were more than 300 trials, which we noted in the Methods section. There are fewer firsts in general, and fewer trials for higher numbers of keystrokes in the context. Therefore the 300 trial cutoff allows us to go up to 3 previous keystrokes for Figure 4B, but 7 previous keystrokes for Figure 4D.

      (7) In Figures 3E and 3F, eyeballing and comparing the null and listen vs. null distributions (3E) with the First vs. Other distributions (3F), I had trouble wrapping my head around how the ones in 3F can be highly significantly different (p<0.001), while the others in 3E are not. (See also my question above re the calculation of the null distribution.)

      Regarding Figure 3E, as detailed in the Methods section, the comparison between playing and listening was performed using a permutation test, whereas the p-values for comparisons between playing and null or listening and null were computed empirically as the proportion of values in the null distribution that exceeded the observed statistic. This is because playing and listening are both empirical (non-null) distributions, making a direct permutation test more appropriate for their comparison.

      (8) Please clarify whether or not the decoders were compared to all keystrokes (firsts and others)?

      The decoders were compared to all keystrokes in the main text (Figure 7), but a sized-match sample of firsts and others yielded the same conclusion (Figure S12).

      (9) Last paragraph of Disentangling auditory...

      If I understand it correctly, then neither ANOVA revealed an interaction; yet, the authors computed post-hoc pairwise comparisons nevertheless?

      There is an interaction for P50 according to the ANOVA (Figure 6C). We followed up with post-hoc comparisons to investigate whether this interaction is driven by a particular key-pitch map.

      (10) Figure S9: More information is needed re the TRF decoder; why such a short time window (as opposed to (showing) the ERP epoch -.2 to .5 s)? What does it mean for the decoder to have its peak at 0 s?

      Since we used an inverse TRF formulation, the target reconstruction corresponds to a sparse impulse vector with value 1 at keystroke onsets and 0 elsewhere. As a result, only the temporal location at t=0 is of interest, with the expectation that the reconstruction should be flat outside this point. As a sanity check, we verified that averaging across onset-aligned windows reveals a clear peak at t=0, confirming that the model captures the expected temporal alignment between keystrokes and reconstructed responses.

      Minor:

      (1) Please include line numbers in the revised document to facilitate the review of the manuscript.

      (2) Baseline period: either baseline correct to 100 ms, or show the entire 200 ms baseline period in the figures.

      No baseline correction was applied to the ERP signals. Instead, data were re-referenced to the mastoids and band-pass filtered (1–30 Hz) to reduce slow drifts and high-frequency noise. As shown in Figure S5, the pre-stimulus baseline period does not exhibit systematic drift across conditions, consistent with stable baseline activity following preprocessing.

      (3) I was surprised to read that the authors used Sennheiser 650 headphones - surely they introduce significant electrical interference?!

      We have previously used headphones in EEG experiments in our lab without issues (cf. Cantisani 2023, Di Liberto 2020). In preprocessing, a notch filter at 50 Hz is applied to remove line noise, and ERP analyses are further low-pass filtered at 30 Hz to isolate the relevant evoked response components.

      (4) ICA should be run on continuous data to avoid situations where an eyeblink cannot be accurately identified (and removed) because it's cut off by the epoch (and this way it would remain in the epoch and contribute noise).

      ICA was indeed run on the continuous data (10 minutes for each task). We clarified this in the Methods section.

      (5) The supplementary video was not available.

      We have let the eLife team know about this.

      (6) Figure 2F: I believe the x-axis tick marks should read Block1 and Block2, instead of Pre and Post? Please clarify (also in the corresponding text) whether this is averaged across Pre-training and Post-training sessions, or only for one of them?

      Thank you for pointing out the error, it should indeed read block 1 and block 2, and has been updated. Both take place during the 30-minute training session, which consists of 2 blocks.

      (7) Figure 3: It wasn't clear to me how only significant channels are shown.

      We applied a mask so that only the significant channels are coloured according to amplitude difference. Non-significant channels are shown in white. The explanation for this is now found in Results > Experiment II > Effects of targeted skill acquisition training.

      (8) For the decoder analyses, how did the authors determine that investigating/using the same electrodes for auditory vs. motor ERPs is appropriate? I am aware that ERPs evoked by the auditory cortex are maximal at fronto-central electrodes; is the same the case for motor ERPs?

      We did not perform any pre-selection of channels for the decoder analyses. All channels were included in model training and prediction, allowing the decoder to learn data-driven spatial weights for reconstruction without imposing priors about channel relevance for auditory or motor processing.

      (9) Figure 4A/C: The stems represent keystrokes during the Variable map Pre/Post test? This indicates that this particular participant often only played 3 notes?

      Participants occasionally paused after producing short sequences of 3–5 notes. This behavior varied across individuals, with some producing near-continuous sequences with brief (< 1 s) pauses, and others inserting longer pauses (2–3 s) between melodic segments. Participants were instructed to generate short, varied melodic motifs and to avoid repeating identical sequences.

      (10) Figure 5E: Were these based on size-matched comparisons, i.e. similar to the method the authors applied to the other analyses comparing first vs. other keystrokes?

      The figure shows the means without size matching, but using size-matched comparisons doesn’t change the conclusions of the figures; we added this analysis in a supplementary figure.

      (11) Figure 6C and 6G: there seem to only be 16 and 17 datapoints, respectively?

      Figure 6C: We double-checked in the code and SVG file and there are indeed 18 subjects and 18 points.

      Some points are not clearly visible in the figure due to very close overlapping.

      Figure 6G: We unintentionally excluded one subject from the plot by setting the x-axis limit to between 2 and 4 on the training score. We have now adjusted the plot so that all subjects are visible.

      (12) Figure 6C: Why an ROI here, but not elsewhere?

      The ROI selection was based on prior ERP studies reporting robust auditory responses over central electrodes and motor-related error responses over frontal midline electrodes (Gehring 1993, Lutz 2013).

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      This manuscript presents compelling evidence from a wild chickadee population linking heritable spatial cognition to extra-pair paternity success, supporting sexual selection via good genes in a food-caching species. The integration of RFID cognition tests with ddRAD paternity assignment is methodologically strong and timely for behavioral ecology, though causal mechanisms and confounds warrant clarification.

      Overall, a major revision of the manuscript is recommended, addressing the points below.

      (1) Confirmation of manipulation and treatment effects.

      The central claim hinges on spatial cognition driving EP siring, but direct evidence that cognition predicts observed copulations (vs. post-copulatory mechanisms) is absent. While territories do not cluster by performance (Figure S4), quantify male aggression/movement data during fertile periods to rule out intrusion-based EPP. The authors should provide metrics like nearestneighbor distances for EP sires or playback responses linking cognition to dominance, as in prior chickadee work. Without this, causal female preference remains correlational.

      We do provide the mean distance to all known EP sires in Figure S2, in addition to the known neighbors coded by cognition and EPP (Figures S3 and S4). Unfortunately, we do not have data with playbacks for this set of individuals, though we have shown that males respond to threats from high or low elevation birds equally, which provides a potential proxy for cognitive performance and dominance (e.g., high elevation birds perform better on the task than low elevation birds, and low elevation birds are dominant/,more aggressive than high elevation birds; Kozlovsky et al. 2014, Beh Ecol and Sociobiol; Branch et al. 2015, Behaviour; Branch & Pravosudov 2016, Ethology).

      As mentioned in discussion of the manuscript, we do not see a significant relationship between dominance and task performance in our system (Heinen et al 2021) – this is also true for the closely-related black-capped chickadees (Robayo Noguera et al 2025). This is not to say that social dominance status does not affect female preference or choice, but that data is outside the scope of this work. We would like to highlight that we’ve shown high repeatability in individual task performance and shown a strong gene c basis for spa al learning and memory performance (Sonnenberg et al. 2019; Branch et al 2022; Semenov 2024, Current Biology). While social dominance status is a rela ve trait and known to change with me and age (eg adults are dominant to juveniles).

      From discussion:

      “Furthermore, while higher social dominance status is associated with access to better territories in chickadees (86), we see no association with dominance status and spatial cognitive abilities in our system (46) or closely related black-capped chickadees (81). While it is possible that our results reflect some unmeasured trait(s) linked to spatial cognitive ability, such as boldness, aggression, or increased exploratory behavior (e.g., 32), previous data from our system do not support these additional alternative hypotheses. Chickadees with enhanced spatial cognitive abilities are not more aggressive (78) nor do they show higher rates of exploratory behavior (e.g., higher space use) (79).”

      We agree that the results we present are correlational. A causal relationship is outside the scope of this research, as we cannot manipulate cognition in the wild and chickadees will not breed in captivity. The strength of our approach lies in multi-year data collection and the ability to compare among the social and extra-pair males, as well as using what we know about the system and species to rule out additional explanations, including age.

      (2) Female cognition-EPY link inconsistency.

      Poor female cognition predicts more EPY (first-20-trials: offspring-level χ<sup>2</sup>=6.21, P=0.013; nests: χ<sup>2</sup>=6.79, P=0.009), but not for full-task (P>0.5). The authors should discuss why (e.g., learning speed vs. memory stability) and add exploratory correlations (female errors vs. EPY proportion). They should soften claims in the Discussion section of "female-driven" without consistent support and should frame this as a hypothesis.

      Absolutely, we agree that this is an interesting nuance to the results regarding female cognition. While number of errors on the first 20 trials and across the entire task are highly correlated, this is not a 1-to-1 relationship (Figure S7a). We suggest that performance in the first 20 trials reflects memory acquisition, while performance across the full task reflects memory retention and recall (Sonnenberg et al. 2019) – both critical components of spatial learning and memory for food-caching birds.

      Previous work has shown that performance in the first 20 trials and across the entire task is linked to survival (Sonnenberg et al. 2010) and longer lifespan (Welklin et al. 2024) – meaning both metrics reflect fitness. In the discussion, we suggest females may be compensating for their poorer abilities by seeking EPY, but this is speculative, as we do not have data beyond the correlative relationship we report and cannot provide more insight to the difference between the first-20 and entire task. This said, it is not only poor performing females that have EPY in the nest and we included the female/mother identity as a random factor in our models (see Statistical analysis section of Methods). Certainly, further investigation into female task performance and mate choice is warranted.

      Edit to MS:

      In the discussion we have edited the sentence to be more specific to our findings:

      “Indeed, females with poorer spatial memory acquisition (made more errors on the first 20 trials) had more extra-pair young in their nests, while social male cognitive performance did not predict EPY in the nest.”

      (3) Cognitive task sensitivity and validity.

      Mean errors aggregate learning curves effectively, but single feeder-assignment (nonpreferred) confounds neophobia/motivation with spatial ability. The authors should report trial-by-trial improvements (Figure S7 subset) or criterion-to-learn metrics. Justify excluding high-error birds (<3 mean); sensitivity analysis needed to check bias toward high performers.

      We respectfully disagree that our task lacks sensitivity or validity. The criterion-to-learn or trials-to-criterion metric has been criticized for decades and should not be used in studies comparing individual variation, in our opinion (e.g., Pravosudov 2022, Current Opinion in Behavioral Science; Harrington & Lambert 2025, Biology Letters).

      We use metrics based on the nature of our task to assess performance and ensure birds have learned before we include them in our analyses, for instance, all birds made < 3 errors on average and completed at least 20 trials. Random chance performance on our task is 3.5 errors (7 possible errors), therefore, birds that make more than 3 errors have not learned the task and therefore would not be included in analyses. It should be noted that this is very rare and typically if birds are excluded its because they do not complete 20 trials.

      See Testing spatial cognition section of the manuscript:

      “In addition, birds were included in analyses if they performed at least 20 trials and made fewer than mean 3 errors across the 4-day testing period.”

      We can certainly understand concerns about individual differences in motivation and neophobia, however, we have also considered this and made efforts to address these issues. That said, we do rely on birds to participate willingly in the spatial task and there may be some bias associated with those that participate vs. those that do not that we cannot account for. Chickadees, as a caching species, are particularly well-suited for our work as they appear to have infinite motivation to obtain and store food items in the wild (and individuals indeed differ in this, hence the differences in the number of trials completed, which we control for in our analyses). We know this not only from our study but work from many researchers, where birds have ad libitum food and continue to cache. Regarding neophobia, birds are introduced to the feeder array in stages, as we explain in the methods, and no humans are present during testing.

      “Each array consisted of eight equidistant RFID-based feeders on a square (122 x 122 cm) aluminum frame suspended ca. 4 m above the ground (Figure 1). Each feeder is equipped with a small, motorized door. Prior to testing, we kept the feeder doors of the arrays open for approximately one month. Next, the feeder doors were closed and programmed to open for any bird with a PIT tag, this allowed birds to habituate to the motorized feeder doors for one week. Finally, we measured the spatial learning and memory abilities of mountain chickadees using a 4-day task. The spatial learning and memory task involved pseudo-randomly assigning each bird to a single feeder in the 8-feeder array that was not its most-visited feeder during the previous two habituation stages.”

      Finally, using the first-20 and 4-day task performance metrics we’ve shown relationships between survival, longevity, genetic variation, and reproductive output, while seeing none of these relationships with the cognitive flexibility task (all with different groups of birds over the years), which we find to be the most compelling evidence that our metric is valid and sensitive.

      (4) Paternity assignment robustness.

      ddRAD-CERVUS with bimodal LODs (Figure S8) is solid, but unassigned EPY (social-genotyped but no sire) implies missing sires (~?% of EPY?). Include all alive males as candidates yearly? Test power simulations for LOD thresholds. 2019 exclusion justified, but multi-year SNP alignment could boost resolution.

      One of the limitations or challenges of our system is that the birds inhabit a highly contiguous forest and our field site is not demarked by boundaries or barriers, meaning we do have undetected males just outside our field site that likely sire offspring and we have no data for. That said, we were able to assign paternity to 630 out of 732 offspring, giving us a success rate of 86%. We have now added this to the first paragraph of the results. For all 732 chicks we knew the social males genotype and could ID presence of EPY, but in that 14% we could not ID the EP male specifically. We did include all alive males as potential sires. This includes males that may not have been nesting in our boxes that particular year, but were detected alive in the previous winter testing season that we were able to genotype.

      We tried a multi-year SNP alignment first, but obtained stronger paternity assignments and differentiation between first and second-tier candidate sires when we ran each year separately. Running the SNP analysis for each year separately resulted in more SNPs to use in each year which increased our ability to confidently assign paternity.

      (5) Mechanistic speculation vs. data.

      Discussion invokes hippocampus genes (GWAS priors) and good genes, but no offspring cognition/survival data. Label as hypotheses; suggest tracking EPY recruitment. No brood size costs for EP sires is key, but monitor long-term nest investment (e.g., feeding rates).

      Indeed, these are informed speculations/hypotheses based on our previous work showing the genetic bases of cognition and high levels of heritability (Branch et al 2022; Semenov 2024, Current Biology). We also know that juvenile survival is predicted by performance on our spatial cognitive task (Sonnenberg et al 2019, Current Biology). However, we do not have offspring survival for these particular EPY (past fledging the nest). We recruit about 5% of the young back into our study site (Whitenack et al. 2025), which makes it difficult to make meaningful inferences at this point. Though, as we continue to collect data in this system we hope to obtain a sample size to address these questions.

      We have collected data on feeding rates at the nest via RFID in some years, however, these measures come with additional caveats as they do not control for the amount/quality of food. Though, preliminary analyses suggest no difference in feeding rates based on cognitive abilities.

      We use the mass of the nestlings at Day 16, which is a common proxy for survival likelihood in Passerines, and we know individuals of higher mass are more likely to survive and be recruited back into the system (Whitenack et al. 2025).

      Reviewer #2 (Public review):

      Summary:

      In this study, the authors ask whether spatial cognition is under sexual selection in mountain chickadees. To do so, the authors examined a large dataset that includes a) spatial cognition data for both males and females (obtained via use of a clever RFID-based feeder system) and b) social and extra-pair paternity nesting data. As predicted, males with higher spatial cognition sired more extra-pair offspring, and extra-pair sires had, on average, higher spatial cognition scores than the males they cuckolded. Interestingly, females with lower spatial cognition scores were more likely to seek extra-pair copulations, potentially to compensate for their own low spatial cognition. Surprisingly, there was no difference in spatial cognition scores between males that sired their own offspring and those that lost paternity at the nest. Also surprising was the fact that there were no differences in patterns of extra-pair paternity and spatial cognition between high- and low-elevation sites. The latter is particularly surprising in that spatial cognition should be under stronger selection at the high elevation site. Overall, this is a fascinating study that demonstrates that spatial cognition - a trait under natural selection as it directly impacts winter foraging and survival behaviour -is also under sexual selection.

      Strengths:

      The authors have a robust dataset (n = 732 offspring sampled over 3 years), high-quality spatial cognition data collected with a procedure that has been well-honed over the years, and couple the data with solid statistical procedures that address many potential covariates and potentially confounding factors. In addition, the authors are careful in the discussion to elaborate on the many potential alternative explanations from the results and questions that are likely to arise in the minds of readers (e.g., how are females assessing male spatial ability?)

      Weaknesses:

      Overall, no major weaknesses were identified in this study. As always, there are editorial issues that I would encourage the authors to consider, including presentation of data/results and clarification on some statistical issues. Overall, however, this is an excellent study that will make an important contribution to our understanding of the evolution of cognition and targets of sexual selection.

      Reviewer #3 (Public review):

      Summary:

      The authors presented evidence that spatial cognition in this population is under sexual selection, with extra-pair males, primarily chosen by the females, having better spatial cognition than males they cuckolded and males with better spatial cognition having more extrapair young.

      Strengths:

      This cognitive ecology study was conducted on a well-known long-term study population of free-ranging mountain chickadees. This strong base, alongside a thorough study design and extensive statistical analyses, enabled the authors to address research questions that few other labs can address, making this a potentially powerful study of broad general interest.

      Weaknesses:

      Throughout the manuscript, there is a focus on the "mean number of location errors per trial over the first 20 trials". Performance changes across trials, so why weren't learning vs peak performance analyzed separately? Similarly, authors also describe results in the context of the entire task, but sometimes in the context of the first 20 trials - why is one prioritised over the other, and why is the emphasis not always consistent? Are the results across the two generally the same? A more thorough explanation addressing all these points is necessary.

      Results are often similar in both metrics, however, the relationship between first 20 and total trials is not 1 to 1 (reported at top of results section and Figure S7a). We suggest that performance in the first 20 trials reflects memory acquisition, while performance across the full task reflects memory retention and recall (Sonnenberg et al. 2019) – both critical components of spatial learning and memory for food-caching birds. Previous work has shown that performance in the first 20 trials and across the entire task is linked to survival (Sonnenberg et al. 2010) and longer lifespan (Welklin et al. 2024) – meaning both metrics reflect fitness.

      We did locate several instances where the metric used is not clear and we have corrected this, thank you.

      To summarize, we reported results for both metrics for analyses related to the main hypotheses, and then reported first-20 trials in the main text for additional tests and provided the entire test data in the Supplemental Materials.

      Lines 429-432: Why was a categorical (i.e., chi-square test) and not a numerical comparison implemented? A numerical statistical test would capture more of the variation (i.e., the number of years separating the social and EPY males).

      We agree and have added a paired t-test to assess whether within each offspring, the social father differed in age from the EP father. This test returned a similar result (χ<sup>2</sup><sub>1</sub>=0.27, P=0.662) and has been added to the results.

      Recommendations for the authors:

      Reviewer #2 (Recommendations for the authors):

      (1) Statistical analysis:

      The authors include elevation as a fixed effect in their models; however, I am curious as to why there were no elevation interaction terms included in the model, as I would predict that selection for higher spatial cognition would be stronger in high-elevation sites.

      We did test for an interaction between elevation and cognition in many of our models and did not find any support for interactions. For example, there was no interaction between elevation and cognition in the number of EPY sired model.

      (2) General comments:

      (a) I would prefer to see extra-pair paternity written out rather than EP, EPY, EPP, etc., as the inclusion of the words takes little extra space in the text and makes for easier reading (personal preference).

      We agree and have spelled out EP, EPY, EPC, and EPP throughout the MS.

      (b) The discussion does an excellent job addressing these questions, but it could be worth noting in the introduction why it is unlikely that this pattern would result simply from selection for dominance (or other factors), given that readers familiar with chickadees would likely immediately think about the role of dominance in extra-pair paternity.

      We have added this point to the introduction, thank you:

      “Previous research in chickadees shows that females often produce extra-pair young with socially dominant males (e.g., 44, 45), however, in our study system we do not see a significant relationship between social dominance and spatial cognitive abilities (46). One potential explanation for this, is that social dominance changes over an individual’s lifetime and with age, while spatial cognition is repeatable and consistent over individual mountain chickadee’s lifetime (25, 27-32).”

      (3) Specific comments:

      (a) Line 27-31: This feels like a weak justification. The study is really about selection on cognition rather than the study of sexual selection per se. I would encourage the authors to revise this justification statement to focus on how sexual selection can help shape cognition.

      We have edited the abstract.

      (b) Line 49: Suggest a stronger start rather than justifying the paper by stating that mate choice has been a focus of evolutionary biology.

      We have edited this statement.

      (c) Line 50: I believe this should be "mate choice" rather than "sexual selection"

      Edited.

      (d) Line 59-62: Confusing wording throughout, especially as "high quality" does not refer to sperm competition, but rather sperm that may have an advantage during sperm competition.

      Suggest reworking the sentence for clarity.

      We changed this to quality instead of competition.

      (e) Line 69: Predictable variation in what?

      We have removed predictable variation.

      (f) Line 87: time;

      Corrected.

      (g) Line 104: Cut "specifically (i.e., caches are not used for provisioning young),".

      Removed.

      (h) Line 106: Presumably referring to assortative mating?

      Added.

      (i) End of the introduction focuses on a couple of primary questions; however, once the reader gets to the methods and results, we find many more tests (e.g., age, brood size, female cognition, etc.). If the authors are going to include these additional tests (which I think they should), then I encourage them to provide the predictions or justifications for those analyses here. In addition, please double-check to ensure the presentation of all tests is consistent throughout the intro/methods/results/discussion.

      We have now added this information to the end of the introduction as alternative explanations, rather than specific predictions. These additional analyses were implemented post-hoc to exclude alternative explanations for the patterns observed, but we have linked them to the statistical analyses as requested by Reviewer 3 and for clarity.

      (j) Suggest including sample size (nests, nestlings, etc. per year) in methods.

      We have provided all sample sizes in the Supplemental Tables and in the text where appropriate.

      (k) Line 255: How many egg dumps? Would be interesting to have a number here for future meta-analyses, reviews, BOTW accounts, etc.

      Unfortunately, we do not have this data available, and the numbers were very low which is why we did not report them in the manuscript. As we continue to work in the system we will be able to provide this information.

      (l) Line 273: See comment above re: elevation as an interaction term in models.

      Addressed above.

      We did test for an interaction between elevation and cognition in many of our models and did not find any support for interactions. For example, there was no interaction between elevation and cognition in the number of EPY sired model.

      (m) Line 282: extra period.

      Removed.

      (n) Line 328: Change "Here" to "Next".

      Edited.

      (o) Line 465: I would suggest bringing this in earlier and considering the flow of how ideas are presented. Seems more logical to first look at whether males lost paternity, then, if so, to whom those males lost paternity.

      We have reorganized the results section to be consistent with the stats methods order.

      (p) Line 553: suggest "likely means" as there may be other attributes of individual quality outside of spatial cognition that are important.

      Yes, we have added this qualifier.

      Reviewer #3 (Recommendations for the authors):

      (1) Section starting at line 268: This section has a long list of statistical analyses. To better help the reader follow the aims of the study and the relationship between them, I recommend numbering the research questions in the introduction and pairing them with the description of each statistical test here in the Statistical Analyses section.

      We agree, thank you for this suggestion.

      We have now added this information to the end of the introduction as alternative explanations, rather than specific predictions. These additional analyses were implemented post-hoc to exclude alternative explanations for the patterns observed, but we have linked them to the statistical analyses and results as requested.

      (2) Lines 295-297: What was the percentage of tested individuals that had brood size data available?

      We only have brood size information for birds that breed in our nestboxes and make it to day 16 post-hatching – this is a much-reduced sample from those that participate in cognitive testing (we test around 150 birds a year between both elevation sites). In addition, throughout breeding stages we lose nests to predation, prior to day 16, when we collect blood samples from the chicks. Birds also participate in cognitive testing and breeding in multiple years, so our sample size for EPP is a result of repeated measures in some instances.

      (3) Lines 473-479: The study is done, so use the past tense throughout the manuscript.

      Thank you, we have edited this for consistency.

    1. Author response:

      We thank both reviewers for their constructive and thoughtful evaluations, and the editors for the positive assessment. We are grateful that the reviewers found the question important, the design clear, and the exploratory-replication structure a strength. Below we briefly outline the directions of our planned revision; a full point-by-point response to the public reviews and the recommendations will accompany our resubmission.

      The reviewers raise several points we find valuable and intend to address. First, we will clarify the scope of our central claim. We will distinguish our confirmatory result, that the Multiplicative model best accounts for the data among the preregistered candidates, from stronger statements about the underlying computation, making explicit that the evidence most directly supports cross-domain integration, with multiplication the best-supported rule among those tested. Second, we agree on the importance of situating our findings within Bayesian accounts of cue integration, and will add a discussion of how the multiplicative combination of statistically independent cues relates to probabilistic inference about self-causation and to prior cue-integration work on the sense of agency. Third, we will sharpen definitions of key terms such as ‘integration’ and ‘domain-general’ and the framing of our contribution, clarifying that it concerns how multi-feature prediction errors are combined. Finally, we will address and discuss the distinction between the integration we demonstrate and its interpretation as a domain-general representation of agency.

      We believe these revisions will strengthen the manuscript, and we thank the reviewers again for their helpful guidance.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public Review):

      Drp1 supports mitochondrial fission (doi: 10.1038/s41586-019-1296-y). Viral sensing triggers mitochondrial fusion, leading to MAVS aggregation and improved type-1 IFN response. It was suggested that impairment of Drp1 upon phosphorylation by Tbk1 enhances mitochondrial fusion in virus-infected cells (doi.org/10.1016/j.molcel.2020.10.018). In this manuscript, Fang et al. describe an unexpected role of caspases activated upon Rift Valley fever virus (RVFV) infection in inactivating Drp1. They show that Drp1 is targeted by multiple caspases, including caspase-3, -6, -7 and -8. Indeed, cleavage of Drp1 leads to mitochondrial elongation, boosting the type-1 IFN response of infected cells. Finally, the authors establish the general disability of the proposed mechanism in the context of cellular infections with H1N1, SeV, and HSV-1. Caspase-dependent and independent cell death processes provide important host defence mechanisms against obligatorily intracellular viral pathogens. This work suggests that caspases reinforce antiviral response involving also the mitochondria-type 1 IFN axis. As such, the manuscript is well written, and the proposal pertaining to caspase-mediated targeting of Drp1 may have implications beyond host-virus interaction studies. However, several loose ends remain, and these concerns need to be addressed to substantiate the mechanistic model.

      Reviewer #2 (Public Review):

      In the present study, authors report the role of virus-induced apoptosis in positively regulating the innate immune response. Upon infection, host cell apoptosis is triggered as a defence mechanism against virus replication. Culmination of infected-cell death impairs replicative potential for viruses, hence attenuating virus propagation. Reports exist denoting the inhibitory effect of apoptosis upon innate immune signalling. Contrary to that, the findings of this manuscript underscore the possible role of apoptosis in enhancing innate immune signalling and effector response. Infection-induced activation of caspases (3, 6, 7, and 8) has been demonstrated to cleave DRP1 protein. DRP1, a positive regulator for mitochondrial fission, degradation leads to altered mitochondrial morphology (elongation).

      Mitochondria, being a hub for innate immune signalling (via operation of RLR-MAVS-downstream effector molecule-axis), upon elongation as a result of DRP1 depletion, results in greater innate immune signal flux and interferon induction. Increased interferon induction thus acts to inhibit virus propagation, as demonstrated by the authors using cell-culture models.

      Strengths:

      (1) The findings presented by the authors have been validated by employing elaborate biochemical experimental approaches. The study entails extensive biochemical characterization of DRP1 residues targeted by activated caspases, in vitro assays validating caspase-mediated DRP1 cleavage & caspase-DRP1 interaction.

      (2) This study possesses broad implications since the authors demonstrate the role of caspase-mediated DRP1 cleavage in promoting innate immunity in the context of infection by diverse viruses (both RNA and DNA viruses).

      Weaknesses:

      Although the authors undertook a thorough experimental approach attempting to validate their findings, all the experiments were performed using either cell-culture models for infection or in vitro biochemical assays (cleavage and protein-protein interaction). Additional experimentation using animal models (in vivo) will further help strengthen the biological significance of their findings under more physiological settings.

      Reviewer #3 (Public Review):

      Summary:

      The authors demonstrated that the NSs protein of RVFV triggers the activation of apoptotic caspases, which cleave the mitochondrial fission factor DRP1 resulting in mitochondrial elongation.

      Strengths:

      The manuscript provides an insightful investigation into a novel mechanism through which apoptotic caspases promote anti-viral immunity by regulating mitochondrial morphodynamics.

      We are very grateful for this constructive review. Our specific responses are enclosed below.

      Recommendations for the authors:

      Reviewing Editor Comments:

      It is advised that the deficiencies and weaknesses pointed out by all three reviewers are meticulously addressed. This will be important to mechanistically substantiate the proposed model. While the absence of animal data represents a deficiency, the authors may graphically/textually articulate future courses of in vivo experiments that may shed further light on the physiological significance of the proposed mechanism.

      Reviewer #1 (Recommendations for the Authors):

      (1) Figure 1: While Figure 1 is convincing, could it be possible to add some quantification for mitochondrial morphodynamics? For example, the average number, size, perimeter, interconnectivity, and elongation of mitochondria from uninfected and infected cells may be compared in a violin plot. This approach should then be followed throughout the manuscript.

      We appreciate the reviewer’s suggestion. We agree that quantitative analysis of mitochondrial morphology would be valuable to the study. However, it seems that a widely accepted quantification standard for the mitochondrial elongation phenotype is currently not available. We also tried to use the MiNA (Mitochondrial Network Analysis) plugin (ImageJ; 2017 Acta Histochem, doi:10.1016/j.acthis.2017.03.001) to analyze mitochondrial morphology. Unfortunately, this plugin could not be properly executed due to unknown reasons. For this reason, we propose not to include the quantitative data in the main manuscript, also because the immunofluorescence analysis showed a rather distinctive phenotype. If the reviewer can suggest a method for this kind of quantification, we could try with the suggested method.

      (2) Figure 2: NSs of RVFV interact with the general transcription factor TF-IIH and primarily reside in the nucleus. Then, what could be the mode of caspase activation by NSs? Is the interaction between NSs and TF-IIH important for caspase activation? In general, the link between NSs and caspases may be discussed more elaborately.

      Regarding the mode of caspase activation, our recent publication (together with other’s previous work) showed that the NSs-mediated TFIIH degradation leads to transcriptional inhibition resulting in rapid downregulation of the short-lived pro-survival protein MCL-1, contributing to BAK activation (2024 Cell, doi: 10.1016/j.cell.2024.09.008; 2024 PLoS Pathog, DOI: 10.1371/journal.ppat.1012387). Activation of BAK may trigger mitochondrial apoptosis (2022 Nat Commun. doi: 10.1038/s41467-021-27851-y).

      (3) Figure 3: Some data quantification will be important for immunoblot analyses. This is relevant for other figure panels as well.

      We have now included semi-quantitative analyses for the key immunoblot data in Figure 3.

      (4) Figure 3: Previous studies implicated MITOL-mediated pathway in Drp1 degradation (doi: 10.1242/jcs.257808). Importantly, the ubiquitin-proteasome system was shown to degrade PKR in RVFV-infected cells (doi.org/10.1371/journal.ppat.1005437). It could be important to determine the PKR level in immunoblot analyses performed in Figure 3A to ensure that MG-132-mediated inhibition was not inadequate in those experiments.

      We have now included detection of PKR in the revised Figure 3A and updated the corresponding text in the manuscript. The results showed that MG132 treatment effectively rescued the RVFV-induced degradation of PKR. In contrast, MG132 treatment did not inhibit RVFV-induced DRP1 downregulation.

      These results indicate that while proteasomal degradation of DRP1 may occur in other contexts, it is not the primary mechanism for DRP1 downregulation in the context of RVFV infection.

      (5) Figure S2F and Figure S2G assure the necessity and sufficiency of NSs in caspase activation and should be placed in the main text. These figures MUST also include an additional panel comparing the level of full-length and cleaved Drp1.

      We have reorganized the figures in the revised manuscript accordingly. The changes are as following:

      (1) The original Figure 3G (showing caspase activation during RVFV infection) has been moved to the Supplementary Information as new Figure S2F to streamline the main figures.

      (2) The data showing that NSs expression alone is sufficient to trigger caspase activation and PARP-1 cleavage remains as Figure S2G, with DRP1 downregulation shown separately in Figure 2E from the same samples. This arrangement was maintained for narrative flow in the main text, but we have updated the text to explicitly guide the reader between these figures.

      (3) We have put the original Figure S2F to the main text as new Figure 3G. This figure now includes the DRP1 cleavage data from the same experiment. And we compared the level of full-length and cleaved Drp1.

      (6) Figure 4: Figure 4A needs a positive control to show that caspase 1, -4, and -9 were active in the in vitro assay condition.

      As suggested, the corresponding positive controls of caspase-1, -4, and -9 have now been included in the revised Supplementary Figure S3.

      The enzymatic activities were confirmed as follows:

      Caspase-1 and Caspase-4: We tested cGAS as a reported substrate (2017 Immunity, doi:10.1016/j.immuni.2017.02.011). While the cleavage fragments for cGAS were not observed potentially due to the epitope affinity of the antibody, a clear reduction in full-length cGAS level was observed upon incubation with both caspase-1 and caspase-4 (Figure S3A), indicating substrate degradation by these caspases.

      Caspase-9: Its activity was demonstrated by its ability to process a catalytically inactive mutant of procaspase-3 (Figure S3C).

      (7) There are some anomalies related to the size of the cleaved Drp1, and this needs serious attention. Figure 3E suggests the size of the cleaved Drp1 produced in RVFV-infected cells to be ~ 55 kDa. However, Figure 4A and Figure 4D indicate that the size of the cleavage products is around 15 kDa [Drp1(1)] and 35 kDa [Drp1(2)]. This must be clarified. Did the Drp1(D556E) mutant still produce the 55 kDa band upon virus infection?

      Below, we provide a point-by-point response.

      (1) Clarification on the apparent size discrepancy of cleaved DRP1 fragments:

      The apparent size difference arises from the use of different antibodies targeting distinct regions of the DRP1 protein.

      In Figure 3E, we detected endogenous DRP1 using an anti-DRP1 monoclonal antibody (CST, #5391) by Western blot. Under these conditions, this monoclonal antibody recognize a single linear epitope. The detection of the ~55 kDa fragment provides evidence that the epitope for this monoclonal antibody is located N-terminal to the D500/D503 cleavage site. Therefore, the ~55 kDa band represents the large N-terminal fragment generated after caspase cleavage.

      In contrast, Figures 4A and 4D analyze exogenously expressed, C-terminally strep-tagged DRP1 (DRP1-strep) using an anti-strep antibody. This setup visualizes the C-terminal cleavage fragments (~15 kDa or ~35 kDa) that contain the strep tag.

      These experiments are designed to detect different portions of the cleaved DRP1 protein. We have also revised the respective figure legends to state the protein source and detection method to prevent confusion.

      Specific Cleavage Pattern of the DRP1(D556E) Mutant:

      The full-length DRP1-strep protein is 83.2 kDa. Cleavage at D556 produces an estimated ~61.9 kDa N-terminal fragment and an estimated ~21.3 kDa C-terminal fragment (containing the strep-tag). Cleavage at D503 produces an estimated ~56.3 kDa N-terminal fragment and an estimated ~26.9 kDa C-terminal fragment (containing the strep-tag). Therefore, the DRP1(D556E) mutant would not produce the N-terminal ~61.9 kDa fragment (cleaved DRP1 (1), Author response image 1) and the C-terminal ~21.3 kDa fragment. However, since the D503 site remains intact, this mutant can still be cleaved at D503, yielding the ~56.3 kDa N-terminal fragment (cleaved DRP1 (2), shown in Author response image 1) and the ~26.9 kDa C-terminal fragment. When detected with an anti-DRP1 antibody, the ~56.3 kDa N-terminal fragment from D503 cleavage is observed. This fragment migrates at approximately 55 kDa on immunoblots. The result (see Author response image 1) are consistent with this interpretation and reflect the situation during virus infection.

      Author response image 1.

      (8) Figure 5: It will be meaningful to add a panel on mitochondrial morphodynamics upon Drp1 knockdown in this Figure. This may provide a correlative argument linking mitochondria to type 1 IFN response through Drp1.

      According to this suggestion, we performed this experiment and included a new panel showing mitochondrial morphology in DRP1 knockout cells. The new Figure 5D demonstrates that DRP1 knockout induces significant mitochondrial elongation compared to control cells.

      (9) Figure 6 and Figure 7: One may consider combining these in one consolidated panel.

      We have now combined the original Figure 6 and Figure 7 into a single consolidated panel (new Figure 6 in the revised manuscript).

      (10) Figure 7: Figure 7B needs particular attention. It seems that RVFV infection causes a similar downmodulation of both Drp1-wt and Drp1-3DE. However, Drp1-3DE did not produce the 15 kDa cleavage product and did not support enhanced type 1 IFN response as much as its WT counterpart did. Could the proteasomal pathway have a role in degrading caspase-resistant Drp1? Could the cleavage product have a role in enhancing anti-viral pathways? This must be meticulously addressed involving additional experimental designs, keeping in mind the results obtained using Drp1 knockdown cells (Figure 5).

      We thank the reviewer for this comment. (1) Regarding the similar downmodulation of DRP1-WT and DRP1-3DE, the RVFV NSs has a potent function to inhibit host transcription. The exogenous DRP1-WT and DRP1-3DE are expressed from a CMV promoter via lentiviral transduction. This high-level exogenous expression system is sensitive to the transcriptional inhibition caused by RVFV-NSs, potentially explaining the observed similar reduction in protein levels. (2) Regarding the role of proteasomal pathway in degrading caspase-resistant Drp1, our data indicate that the proteasomal pathway is not the primary mechanism for the downregulation of the caspase-resistant DRP1-3DE. This is supported by the observation that the downregulation of endogenous DRP1 was largely insensitive to MG132 treatment (Figure 3A). (3) Whether the cleavage product plays a role in enhancing anti-viral pathways is an interesting question, which we propose to address in future study considering the scope of the current study.

      (11) Figure 7: A panel may be added to compare the effect of overexpression of WT and mutant Drp1 on mitochondrial morphodynamics.

      According to this suggestion, we have performed the experiment, and the data are included as a new panel in the revised Figure 6H. The results indicate that upon RVFV infection, control cells (PCDH) exhibited significant mitochondrial elongation. In contrast, cells overexpressing either DRP1-WT or DRP1-3DE did not show significant mitochondrial elongation morphology.

      (12) Figure 8: Considering the known role of Drp1 in MAVS aggregation (doi.org/10.1016/j.molcel.2020.10.018), this figure in its present form could appear less informative. One may argue that a comparison of WT and mutant Drp1 for controlling virus-induced MAVS aggregation could be more meaningful.

      We thank the reviewer for this comment. The major finding of our work is revealing a novel, caspase-dependent mechanism of DRP1 down-regulation. Figure 8 (revised Figure 7) showed that depletion of Drp1 promoted MAVS aggregation resulting in a strong antiviral effect. Regarding the suggestion to compare DRP1-WT and DRP1-3DE for MAVS aggregation during virus infection, we have focused our analysis on the DRP1 knockout system. This approach mimics the natural outcome of infection, where virus-induced caspase activation leads to the depletion of endogenous DRP1. Overexpression of WT and mutant Drp1 could hamper virus-induced depletion of Drp1 due to it’s high abundance, and may therefore affect the MAVS aggregation analysis.

      (13) Figure 9: This figure establishes that Drp1 is cleaved by caspases in response to cellular infection by multiple viruses. However, the significance of caspase-mediated Drp1 cleavage per se in the progeny virus titre remains unclear.

      We agree with this comment. The purpose of the original Figure 9 (revised Figure 8) is to show that the caspase-dependent Drp1 cleavage may occur in response to different virus infection. Whether and how this may affect progeny virus production, would be an interesting topic for future investigation. According to this comment, we reworded our description in the corresponding Results section.

      (14) Would caspase inhibition impact mitochondrial morphodynamics and progeny virus titres? This question needs to be experimentally addressed.

      Our data in Figures 3C, 3D, and 3F showed that the pan-caspase inhibitor Z-VAD-FMK effectively blocks virus-induced DRP1 cleavage in a dose-dependent manner. However, this upstream inhibition did not result in a significantly variation of nucleoprotein (NP) expression under RVFV infection. It is possible that the broad-spectrum inhibition of caspases by Z-VAD-FMK may simultaneously affect multiple aspects of the host cell and affect virus-host interactions.

      For this reason, we employed the caspase-resistant DRP1-3DE mutant (revised Figure 6), which allowed us to specifically analyze the functional impact of Drp1 cleavage without introducing the effects of global caspase inhibition and caspase-dependent processes. The result that DRP1-3DE enhances viral replication provides evidence for the role of DRP1 cleavage in restricting virus production.

      (15) One weakness is a lack of in vivo data despite the availability of Drp1-floxed mice. What are the results that one may anticipate based on the current study? This should be indicated in the Discussion section.

      We thank the reviewer for this suggestion. According to this suggestion, we have now added discussion of the anticipated outcomes of in vivo studies.

      Reviewer #2 (Recommendations for the Authors):

      (1) Based on the DRP1-residues that caspase-3 targets for cleavage (500/503 and 556), 3 fragments having molecular weights of 55, 5.5 and 22 kDa, approximately, should be generated. In Figure 3E, the authors show the presence of DRP1 cleavage product having the size of approx. 50 Kda. Since the antibody (anti-DRP1) used by the authors recognizes the C-terminal region of DRP1, immunoblot for DRP1 under RVFV infection context should also demonstrate the presence of ~20 Kda DRP1 fragment. The authors should provide immunoblots showing the same.

      We agree with the reviewer that, based on the identified cleavage sites at D500/D503 and D556, a C-terminal fragment of approximately 20 kDa should be detectable.

      In our experiments using whole-cell lysates, we consistently observed the ~55 kDa cleaved DRP1 fragment but were unable to detect the smaller ~20 kDa fragment with the anti-DRP1 monoclonal antibody (CST, #5391). According to the manufacturer’s information, this antibody was raised against the carboxy-terminal region of human DRP1; however, the exact epitope has not been disclosed (we tried to contact the company, but did not get an answer). Since this is a monoclonal antibody, we infer that this single epitope likely resides upstream of the caspase-3 cleavage sites (D500/D503 and D556). Consequently, the C-terminal cleavage fragment may lack this epitope and is not recognized by the antibody.

      To verify the generation of this C-terminal fragment, we performed in vitro cleavage assays using C-terminally strep-tagged DRP1 (DRP1-strep), where an anti-strep antibody clearly detects the ~20 kDa band (as shown in Figures 4A and 4D–4F). We have included this information in the manuscript for clarity.

      (2) In Figure 4A, although the band for active caspase3 (from in vitro cleavage assay) is missing, DRP1 shows cleavage. Similarly, in Figure 4E, the band for active caspase3 is also missing. The authors should provide explanations for these data.

      The reason is that under our standardized in vitro cleavage assay conditions, the anti-His antibody did not efficiently detect these particular commercial recombinant proteins, likely due to variations in epitope accessibility, protein conformation, or the detection sensitivity of the Western blot. The enzymatic activity of caspases used in our assays was verified using established positive control substrates. For caspase-3, activity was confirmed by cleavage of the well-characterized substrate PARP1 See Figure S3B.

      (3) In Figure 4F, WT-DRP1 full length-band exhibits reduction in intensity upon treatment with caspase3, which is expected given the ability of caspase3 to cleave DRP1. However, although mutating 'D500/556E & D500/503/556E' abolishes DRP1 cleavage by caspase3, total DRP1 band intensity exhibits marked reduction in both cases. The authors should provide an explanation for this anomaly.

      The recombinant protein used in this assay is C-terminally strep-tagged DRP1 (DRP1-strep), detected with an anti-strep antibody. The mutation of sites D500/503/556E prevented cleavage at these positions. However, the observed decrease in full-length protein indicates that caspase-3 cleavage may occur at other, alternative sites within DRP1, such as D221 (Figure 4C). The detection of cleavage fragment is dependent on the anti-strep antibody recognizing the C-terminal tag. Cleavage at alternative sites located between the mutated sites and the C-terminus is likely to produce shorter C-terminal fragments that may be difficult to be detected. Therefore, it is possible that although caspase-3 cleavage proceeds at these alternative sites in the mutant proteins, the fragments remain undetectable with our detection method.

      (4) In Figures 7B and 7D, infection by RVFV of cells overexpressing DRP1-3DE (caspase-mediated cleavage-resistant) also leads to a reduction in full-length DRP1, although no cleavage product was seen. Does this indicate a possible role for other DRP1 residues being targeted by caspases upon virus infection? Treatment of DRP1-3DE-overexpressing RVFV-infected cells with a pan-caspase inhibitor will further provide insight into whether other DRP1 sites can also be targeted by caspase activity. Moreover, the authors should treat RVFV-infected cells with pan-caspase inhibitor and verify whether WT-DRP1 cleavage is restored concomitant with the abrogation of interferon induction and signaling.

      We thank the reviewer for this comment. (1) For the reduction of full-length DRP1-3DE in RVFV-infected cells, similar with the response to the above comment, it is possible that the transcription inhibition effect of RVFV lead to reduction of Drp1-3DE expression level, an effect which may be more pronounced in the exogenous overexpression system. Additionally, the existence of other potential caspase cleavage sites, such as D221 (Figure 4C), may also in part account for the observed reduction. (2) Regarding the suggestion to use pan-caspase inhibition to analyze interferon signaling, we feel that blocking multiple caspase activities with the pan-caspase inhibitor Z-VAD-FMK will likely affect the global caspase activity in the cell affecting the scope beyond the interferon signaling pathways and is likely to complicate the interpretation of the results. Therefore, we employed the DRP1-3DE mutant for the analysis (revised Figure 6). This way we would not introduce the unspecific effects of global inhibition of multiple caspase-dependent processes. The result that DRP1-3DE enhances viral replication (revised Figures 6E-6G) provides evidence for the role of DRP1 cleavage in antiviral immunity.

      (5) MAVS aggregation shown by SDD-AGE in Figures 8B, 8C & 8D does not display a typical appearance characterizing MAVS aggregation. The pattern shown in the above-mentioned immunoblots is very atypical for aggregates and indicates an increased MAVS abundance in RVFV-infected (8B)/DPR1-KO (8C, 8D) lanes. The aggregation of MAVS when demonstrated in SDD-PAGE gels exhibits a completely different pattern. The authors should include positions for molecular weight markers indicating their corresponding molecular sizes in the immunoblot. That will help in differentiating MAVS monomer from the aggregates and will help assess the extent of MAVS aggregation upon infection/DPR1-KO.

      We thank the reviewer for this comment.

      In the meantime, we checked literatures detecting the pattern of MAVS aggregation using the same technique (e.g., 2011 Cell, DOI: 10.1016/j.cell.2011.06.041; 2017 Nature Communications, DOI: 10.1038/ncomms15138), where, if we understood correctly, MAVS aggregation showed a similar high-molecular-weight smear. It is common in SDD-AGE not to use protein markers, as this method separates by molecular size under semi-denaturing conditions and is designed to resolve high-molecular-weight aggregates rather than provide precise molecular weights.

      (6) In Figure 9D, the authors should also immunostain cells with virus-specific antibodies. This will help delineate that only virus-infected, but not uninfected cells exhibit elongation of mitochondria (as indicated by the appearance of TOM20 staining). In addition to that, the authors should provide an immunoblot for SeV antigen in Figure 9F. Instead of upregulating the H1N1 antigen, caspase inhibition by zVAD-FMK displayed a reduction in viral protein concomitant with DRP1 cleavage inhibition. Whereas, HSV-1 antigen abundance was seen to be enhanced upon the inhibition of apoptosis, which is consistent with the activity of axis entailing apoptosis-DRP1 cleavage-mitochondrial elongation-enhanced innate immunity- reduced virus propagation. The authors should explain this discrepancy.

      Regarding Figure 9D (revised Figure 8D) and virus-specific staining, we now provided the viral antigen (NP) staining for RVFV and H1N1 (See Author response image 2). However, highly specific antibodies for SeV and HSV-1 immunofluorescence (IFA) are not available for us at the moment. We therefore propose to keep the original layout of the figure.

      Author response image 2.

      Regarding the immunoblot for SeV antigen in Figure 9F, we now provided the immunoblot for SeV antigen. See Figures 8F.

      Regarding the H1N1-NP level upon Z-VAD-FMK treatment in Figure 9E, the reduction in NP signal with Z-VAD-FMK can be explained by the fact that the H1N1-NP protein itself is a substrate for caspase cleavage, as previously reported (DOI: 10.1007/s00705-007-0003-8). A zoom-in view of the blot in Figure 9E reveals a smaller migrating band corresponding to the cleaved NP. Z-VAD-FMK treatment inhibited the generation of this cleavage band, concurrently with the inhibition of DRP1 cleavage. When the ratio of internal control tubulin was considered, the NP level in the Z-VAD-FMK treatment group would not indicate a reduction of signal.

      Figures 8E in the revised manuscript and Author response image 3.

      Author response image 3.

      (7) Previous report (Wu et al, 2022, Nat cell death & disease, DOI: 10.1038/s41419-022-05156-2) demonstrates the inhibitory role of apoptosis in interferon-induction upon HSV/SeV in macrophage cells. However, in this study, the authors suggest apoptosis positively regulates interferon response (upon SeV/HSV-1 infection of macrophage cells). The authors should provide an explanation for possible reasons accounting for this difference in the discussions section.

      We propose that the functional consequence of caspases activation, which process different substrates, will likely pose two-sided effects on immune signaling as a two-sided “sword”. While the established caspase-dependent cleavage of molecules such as cGAS, MAVS, or NF-κB may pose inhibitory effect, the caspase-dependent cleavage of other substrates (such as Drp1 and yet-to-be identified other substrates) may pose the opposite effect. The overall effect would need to be determined in a context-dependent manner. We have included this notion in the revised Discussion section.

      Reviewer #3 (Recommendations for the Authors):

      (1) Please add the full name in the Abstract.

      We have now added the full names for all relevant abbreviations upon their first appearance in both the Abstract and the Introduction sections.

      (2) There is no scale bar in Figure 1A, 2A, 2B, 9D upper panel, Figure 8A.

      We have now added scale bars to the revised figures: upper panels of Figure 1A, 2A, 2B, and 8D (original 9D), and Figure 7A (original 8A), as suggested.

      (3) Can the author explain more in the text why DRP1, but not other mitochondria proteins?

      Our initial investigation simultaneously examined the key regulators of both mitochondrial fusion (MFN1, MFN2, OPA1) and fission (DRP1) using the same set of cell samples. This comparison showed that DRP1 was specifically down-regulated upon RVFV infection (Figure 2C).

      (4) Can the author explain more in the text why further study H1N1, SeV, HSV-1, but not other viruses?

      H1N1, SeV and HSV-1 are model RNA or DNA viruses that are commonly used and were selected as model viruses in our system. We propose that other viruses could also be investigated in further studies.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Summary of the Key Clarification Underlying This Revision

      Both reviewers independently identified what appeared to be a direct contradiction between our LC-MS/MS measurements of intracellular ATP (Figure 2) and our single-cell QUEEN reporter measurements of intracellular ATP (Figure 5): NTT1 expression appeared to lower rather than raise intracellular ATP, and exogenous ATP treatment appeared to further lower the QUEEN signal even though LC-MS/MS showed the opposite. We have carefully reviewed the reviewers’ comments alongside our original figures and legends, and we agree that the source of this apparent contradiction was insufficiently explained in the original submission.

      To make the reported quantity intuitively track ATP abundance, we have now:

      - Plotted the reciprocal of the 488 nm signal (1/488 nm) in the updated Figure 5, eliminating the inverse correlation between AU values and ATP abundance;

      - Revised the Figure 5 legend, axis labels, Methods, and Results to explicitly state that the plotted value is directly proportional to intracellular ATP abundance, removing any ambiguity about directionality;

      - Subtracted autofluorescence from the raw QUEEN reporter fluorescence signal;

      - Expanded the Methods and Results to explain, side by side, why the QUEEN-based and LC-MS/MS based measurements are complementary but not numerically identical (different dynamic ranges; live single-cell sampling over time versus bulk lysates at fixed timepoints); and

      - Re-examined Figures 2, 5, and 7 together to confirm that, once the QUEEN directionality is correctly read, the two datasets are internally consistent: NTT1 expression lowers baseline intracellular ATP relative to Wt, and exogenous ATP supplementation raises intracellular ATP in NTT1 cells (and, more modestly and via a distinct mechanism, in Wt cells), by both methods.

      Because this misunderstanding affected interpretation of the foundational ATP data, it appears to have influenced evaluation of all downstream conclusions. For example, neither reviewer meaningfully engaged with:

      - The identification of distinct cell death trajectories of aged cells;

      - The mitochondrial dependency of NTT1-associated toxicity and the observed lifespan differences; and

      - The distinction between intracellular ATP manipulation and extracellular ATP sensing mechanisms.

      Example of a Data Discrepancy Resolved by This Clarification

      In some instances, we think the original figures did not present the data clearly enough to support the intended reading, which we address below.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      The authors aim to engineer a synthetic system for manipulating ATP homeostasis in budding yeast by expressing the microsporidian nucleotide transporter NTT1, thereby enabling ATP import from the extracellular environment. Using this system, they attempt to test whether intracellular ATP abundance causally regulates replicative lifespan and whether extracellular ATP sensing contributes independently to longevity pathways. The manuscript presents data from ATP biosensing, transcriptomics, mitochondrial perturbations, and microfluidic aging assays to build a dual-mechanism model linking ATP availability, MAPK signaling, mitochondrial function, and aging trajectories.

      Strengths:

      A major strength of the study is its creative application of xenotopic synthetic biology to directly manipulate ATP homeostasis-an ambitious approach that addresses an important and difficult question in aging biology. The use of complementary methods, including single-cell ATP reporters, microfluidic lifespan measurements, and RNA-seq, generates a rich experimental dataset with the potential to reveal multiple layers of ATP-dependent physiological regulation. The manuscript also raises interesting hypotheses regarding extracellular nucleotide sensing and HOG/MAPK pathway involvement, opening conceptual space for future exploration of ATP-based signaling in yeast.

      Weaknesses:

      Despite these strengths, the manuscript suffers from several critical weaknesses that undermine the central conclusions. Foremost, the intracellular ATP measurements contradict key interpretations: NTT1 expression lowers ATP levels, yet multiple sections assert or assume that NTT1 increases intracellular ATP via import. This unresolved contradiction propagates throughout the mechanistic model. The authors do not consider or experimentally address the more parsimonious explanation that NTT1 may be a bidirectional ATP transporter, which would unify many perplexing results. Several important analyses are missing (e.g., transcriptomic comparison of NTT1 cells with vs. without ATP), and key signaling claims lack proper validation (e.g., Hog1 quantification, AMPK controls). Additionally, inconsistencies in figures-such as incorrect scale bars, mismatched ATP measurements, and a conceptual model contradicted by the data-further detract from clarity. As a result, the manuscript does not yet convincingly achieve its stated aims, and the current evidence does not adequately support the proposed causal relationships between ATP homeostasis and lifespan.

      We thank the reviewer for a rigorous and constructive critique. The central objection that our intracellular ATP measurements contradict our interpretation arose from a presentational error in how the QUEEN reporter data were plotted. As described in our Methods (QUEEN reporter section), the QUEEN biosensor is a ratiometric reporter whose 410 nm/488 nm excitation ratio increases with ATP binding. Because repeated 410 nm excitation causes phototoxicity over the multi-day time course of a replicative aging experiment, our longitudinal single-cell measurements (Figure 5) used only the 488 nm channel, for which fluorescence intensity decreases as ATP binds the reporter. In the original Figure 5, arbitrary fluorescence units (AU) were therefore inversely correlated with intracellular ATP abundance, such that higher AU values corresponded to lower ATP levels. We described this inverse relationship in the Results section and labeled the relevant figure panels “Low versus High,” but on reflection we agree this was not stated clearly enough in the figure legend itself, where a reader would most naturally look for it. As a result, the two datasets read as contradictory even though they are fully consistent, and we take responsibility for that lack of clarity.

      The reviewer proposes that NTT1 may function as a bidirectional transporter, with net ATP export accounting for the reduced ATP we observe in untreated NTT1-expressing cells. We considered this possibility, and our expanded metabolite data argue against it. LC-MS/MS shows that ATP, ADP and AMP are all significantly reduced in untreated NTT1-expressing cells relative to wild type (new Figure S2B), with AMP most severely affected a contraction of the entire adenylate pool rather than a shift in its distribution.

      Our transcriptome data identify the source of this contraction. NTT1 expression produces a coordinated downregulation of de novo purine biosynthesis, spanning the pathway (new Figure S2A), consistent with the pronounced AMP deficit. Parallel pyrimidine biosynthesis genes are unaffected, indicating a purine-specific response rather than a general biosynthetic shutdown. We therefore conclude that reduced de novo purine synthesis, not reverse transport, is the parsimonious explanation for the lower baseline nucleotide levels in NTT1-expressing cells, and we have added this analysis and interpretation to the Results and Discussion.

      Under ATP-replete conditions, both LC-MS/MS and the corrected QUEEN readout show a clear increase in intracellular ATP in NTT1-expressing cells, consistent with import. We have additionally added the transcriptomic comparison of NTT1-expressing cells with and without exogenous ATP that the reviewer requested (new Figures S1–S3), quantified Hog1 phosphorylation, and audited every figure, legend and numerical value in the manuscript.

      Reviewer #2 (Public review):

      Summary:

      This work presents interesting findings where the addition of exogenous ATP extends the replicative lifespan of yeast cells in a way that seems uncorrelated with actual increased intracellular ATP levels or mitochondria. To be clear, the addition of ATP to yeast growth media increases the number of cell divisions per cell in yeast. Expression of the NTT1 ATP transporter gene increases intracellular ATP levels according to LCMS analysis, but the effect on replicative lifespan works without the NTT1 gene and without an intracellular increase in ATP (possibly with a decrease in intracellular ATP), so the effect appears to be independent of the effect on intracellular ATP levels or mitochondria, as mitochondria-less R0 yeast cells also have increased numbers of cell division when grown with extracellular ATP. The plots in Figure 5 make it seem like exogenous ATP addition lowers intracellular ATP for both the NTT1 cells and the wild-type cells, and that is not what the data in Figure 2d with LCMS shows.

      As an aside, this seems like a better model for increased tumor cell growth in the presence of increased extracellular ATP, which happens in some cancers.

      Restated, the data suggest they were successful in increasing intracellular ATP by LCMS, but not by queen reporter, and that the seemingly likely increased intracellular ATP was not causative, as cells that did not have an increase in intracellular ATP, but had the same exogenous ATP addition, also gained an increase in replicative lifespan. There could also be two distinct mechanisms extending replicative lifespan to the same degree in these two different strains. More measurements, controls, and analyses are needed to accurately determine what is happening with intracellular ATP levels with age. It is currently unknown if there is any correlation between ATP levels and replicative aging (with properly controlled longitudinal measurements).

      Strengths:

      Longitudinal imaging of single cells. Analyzed ATP levels with two approaches. Creative approach to use NTT1 transporter to increase intracellular ATP levels. Solid replicative lifespan data.

      Weaknesses:

      Mostly unclear about ATP levels with age and the relationship, or lack thereo,f between intracellular ATP levels and replicative lifespan. No idea what this effect depends on, but some ideas what it does not depend on (mitochondria or increased intracellular ATP). Experiments seem to lack biological controls (cells without gfp) for age related changes in autofluorescence (and pH that can affect gfp signal) for the fluorescent microscopy quantifying ATP with age using the QUEEN reporter (seems that way as written); conflicting evidence on ATP levels; lack of LC-MS measurements in old cells; no apparent correlation between ATP levels and replicative lifespan, but that could be wrong - just not apparent from the longitudinal data plots. The LCMS data seems better than the microscopy data on ATP because the microscopy approach seems to lack proper biological controls, and the selection of only the top 40% of pixels to quantify signal seems unjustified as written, and possibly prone to technical artifacts. Figure 2 B&C plots of ATP levels should show what the cells were normalized to. The figures also seem too diluted and should probably be combined or put in the supplements (hog1 western) if they do not relate to the lifespan effect. There seem to be some technical scientific editorial errors, like in Figure 7.

      We appreciate this careful and, in most respects, accurate reading. The reviewer concludes that the lifespan extension conferred by extracellular ATP does not depend on an increase in intracellular ATP, since it occurs in cells lacking NTT1 and in rho<sup>0</sup> cells, and suggests that two distinct mechanisms may extend lifespan in the two strains. This is precisely the model our data supports, and we are encouraged that the reviewer arrived at it independently: we propose an intracellular, import-dependent and mitochondria-dependent mechanism operating in NTT1-expressing cells, and a separate extracellular ATP-sensing mechanism that acts without import and without functional mitochondria. We have rewritten the Results and Discussion to make this dual-mechanism structure explicit rather than leaving it to be inferred, and Figure 8 has been revised so that the model matches the data.

      The apparent conflict between the QUEEN and LC-MS/MS measurements, which underlies much of the reviewer's uncertainty about ATP levels with age, is resolved by the correction described below. We have additionally subtracted autofluorescence from the reporter signal, stated the normalization for the ATP measurements in the Figure 2 legends, and added a justification in the Methods for restricting quantification to the brightest pixels. The QUEEN reporter is a soluble cytoplasmic protein excluded from the vacuole, which occupies an increasing fraction of cell volume in ageing mother cells, so whole-cell quantification systematically underestimates cytoplasmic signal in old cells for reasons unrelated to ATP. On the request for LC-MS/MS on sorted old cells, we agree this would be valuable in principle, but because individual cells follow divergent ATP trajectories with age, a bulk measurement of a sorted population would average across those trajectories and would not be directly comparable to our single-cell data.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      The intracellular ATP measurements contradict key interpretations: NTT1 expression lowers ATP levels, yet multiple sections assert or assume that NTT1 increases intracellular ATP via import. This unresolved contradiction propagates throughout the mechanistic model. The authors do not consider or experimentally address the more parsimonious explanation that NTT1 may be a bidirectional ATP transporter… Several important analyses are missing (e.g., transcriptomic comparison of NTT1 cells with vs. without ATP), and key signaling claims lack proper validation (e.g., Hog1 quantification, AMPK controls). Additionally, inconsistencies in figures, such as incorrect scale bars, mismatched ATP measurements, and a conceptual model contradicted by the data, further detract from clarity.

      We thank the reviewer for this central and constructive critique. As explained above, the apparent contradiction in intracellular ATP directionality stemmed from an underexplained sign convention in the QUEEN reporter readout in Figure 5, which we have now corrected and clarified throughout the text, legends, and axis labels. With this correction, NTT1 cells show reduced baseline ATP and a clear, dose-dependent increase in intracellular ATP upon exogenous ATP treatment, consistent between the QUEEN and LC-MS/MS assays. There is a discrepancy between the two methods (QUEEN versus LC-MS/MS) specifically in the Wt cell ATP measurements, which we discuss in the Results section.

      The authors seem to assume that NTT1 expression should result in ATP influx… the authors should consider an alternative interpretation: the ATP transporter is bidirectional… this interpretation seems to be consistent with many of the observations in the manuscript, and this bidirectional ATP flux can be experimentally tested.

      We thank the reviewer for this insightful alternative hypothesis. With the QUEEN directionality now corrected (see summary above), the core observation motivating this suggestion lower ATP in NTT1 cells alongside evidence of import is substantially resolved: NTT1 cells have lower baseline intracellular ATP than Wt, and both LC-MS/MS and the corrected QUEEN readout show that exogenous ATP raises intracellular ATP specifically in NTT1 cells, consistent with net import under ATP-replete conditions. In addition, our expanded LCMS/MS data (Figure S2) suggest that NTT1 overexpression results in decreased de novo purine biosynthesis, offering a possible explanation for the decreased ATP levels in these cells.

      The RNA-seq analysis compared the effects of adding exogenous ATP in WT and NTT1 cells. However, analysis can also be done to compare the effects of NTT1 under conditions with or without exogenous ATP.

      We have added the missing transcriptomic comparison of NTT1 cells with versus without exogenous ATP, and the corresponding data are now presented in three new supplementary figures (Figures S1–S3).

      “In NTT1-expressing cells, ATP is directly imported from the extracellular environment…” the authors are assuming NTT1 cell imports ATP from media with ATP supplementation. This should be reconciled with the lower intracellular ATP concentration and lifespan shortening.

      This statement refers specifically to the ATP-treated condition, in which both LC-MS/MS and the corrected QUEEN measurements show elevated intracellular ATP in NTT1 cells relative to untreated NTT1 cells and to Wt. We have revised the text to make this conditional context explicit.

      The western blots for Hog1p and Hog1 should be quantified… I suggest using p-Hog1 or phos-Hog1 to indicate the phosphorylated form.

      We have now quantified Hog1 phosphorylation by western blot analysis from two independent biological replicate experiments, each probed with a different commercial phospho-Hog1 antibody, to confirm that the result is not antibody-specific (Figure 4, Figure S8; Methods). We have also adopted the reviewer’s suggested nomenclature and now consistently denote the phosphorylated form as Hog1ᵖ throughout the text and figures to avoid ambiguity with the Hog1p gene product naming convention.

      The model in Figure 8 indicates a larger lifespan extension in the NTT1 cells. This is not consistent with the data presented in Figure 5-7.

      The statement regarding a larger lifespan extension is consistent with the data presented in Figures 5 and 7, but we agree this connection was not spelled out clearly enough in the original text. These two figures differ in their treatment conditions. In Figure 6D, 10 µM ATP treatment resulted in a significant median lifespan extension in both Wt and NTT1 cells, though the magnitude of the extension differed: As stated in the Results, Wt cells showed a median RLS increase of 41% (p = 1.28E-12) upon 10 µM ATP supplementation, while NTT1 cells, which also showed an increase in ATP levels (Fig. 6B, C), showed an even more pronounced extension (median RLS increase = 60%, p = 4.03E-18) in lifespan (Fig. 6D). In Figure 7, we analyzed the higher dose of ATP treatment (10 mM) to examine its toxic effect on lifespan. Figure 7A shows that the lifespan-extension effect observed at the low ATP dose (Fig. 6) diminished under the 10 mM treatment condition for NTT1 cells but not for Wt cells. Figure 7B shows that elimination of functional mitochondria rescues this mitochondrial toxicity in NTT1 cells, such that these cells extend their lifespan to a magnitude comparable to Wt under 10 mM ATP treatment conditions.

      Reviewer #2 (Recommendations for the authors):

      The fluorescence imaging shows that cells with exogenous ATP have lower ATP levels, and that is not what was shown in Figure 2 by LCMS. So, as it is, this is confusing and not conclusive and may have to do with technical artifacts.

      We would like to clarify that our data do not in fact conflict. Figure 2B (fluorescence imaging) shows that NTT1 cells have lower intracellular ATP than Wt under baseline (no exogenous ATP) conditions, and that exogenous ATP treatment increases intracellular ATP abundance in both cell types. Figure 2C shows that under 2-deoxyglucose (2DG) treatment, Wt cells display decreased ATP levels regardless of exogenous ATP treatment, whereas NTT1 cells show increased intracellular ATP upon ATP treatment, further supporting the import function of NTT1. Our LC-MS/MS data (Fig. 2D, left panel) independently corroborate the fluorescence results in Figure 2B: NTT1 cells show lower ATP abundance than Wt cells at baseline, and exogenous ATP treatment raises intracellular ATP in NTT1 cells but not in Wt cells. We discuss the modest discrepancy between the LC-MS/MS and QUEEN measurements specifically for Wt cells in the Results section.

      The plots in Figure 5 make it seem like exogenous ATP addition lowers intracellular ATP for both the NTT1 cells and the wild-type cells, and that is not what the data in Figure 2d with LCMS shows… Restated, the data suggest they were successful in increasing intracellular ATP by LCMS, but not by queen reporter, and that the seemingly likely increased intracellular ATP was not causative…

      We appreciate the reviewer’s detailed reading of Figures 2 and 5. As described above, this apparent conflict arose because Figure 5 originally plotted a raw fluorescence value that is inversely related to ATP abundance without stating this clearly enough in the legend. We have corrected the legend, axis labels, and Results text so that the plotted quantity in Figure 5 (1/488 nm QUEEN signal) increases with ATP abundance, matching the LC-MS/MS data in Figure 2. With this correction, both assays agree that exogenous ATP treatment raises intracellular ATP in NTT1 cells; we discuss in the Results the more modest and assay-dependent behavior we observe in Wt cells, where LC-MS/MS and QUEEN differ somewhat in sensitivity and time-resolution.

      It needs a bit more experimental clarification and some thinking about what it means to disrupt ATP homeostasis with high extracellular levels of ATP, a generally biologically unnatural/pathological situation.

      The central premise of our study is that altered intracellular ATP is associated with lifespan. Mitochondrial functional decline is a hallmark of ageing, but whether this correlates with decreased ATP, and whether age-associated ATP changes are linked to cellular aging, remains an overlooked question. Here, for the first time, we show that not every cell exhibits a decreasing ATP trajectory with age, and that maintaining ATP homeostasis can extend lifespan. Interestingly, extracellular ATP sensing is directly relevant to cell-to-cell communication (purinergic signaling); however, this has never been characterized in yeast. Our data indicate that a similar, conserved mechanism may also be present in yeast, although the exact components of this sensing cascade require further study. This information is included in the Introduction and Discussion sections of the manuscript.

      The data for ATP levels with age needs to be cleaned up/refined… Sort some high bud scar cells and test them with LCMS… run wild-type cells to subtract out the autofluorescence… or redo it on a scope with linear unmixing.

      Our data indicates that each cell follows a different ATP-abundance trajectory during aging: while some cells show decreasing ATP with age, others show no change, and still others show increasing ATP. Population-level testing of sorted old cells would therefore not yield results that are directly comparable to our microfluidic experiments, in which we track individual cell trajectories over time. In the updated figure, we have subtracted autofluorescence.

      Figures 1 and 2 could be combined, and so could 3 and 5, 6 and 7. Figure 4 should probably be a supplement or part of another figure since upregulating HOG1 has nothing to do with the lifespan extension effect.

      We appreciate this suggestion for streamlining the figures. Our data show only decreased Hog1 activity under ATP treatment conditions; we did not test whether this decline in Hog1 activity is associated with lifespan extension. However, we would like to include this figure in the main text, because it directly validates the effect of extracellular ATP sensing on modulation of Hog1 activity.

      Figure 7 seems like it is showing that the NTT1 strain’s shorter replicative lifespan is rescued by losing mitochondria, and not that toxicity from ATP in the NTT1 is alleviated by losing mitochondria.

      Both the NTT1 strain’s shorter replicative lifespan and its ATP toxicity (10 mM) are rescued by eliminating respiratory mitochondria. In Figure 7, we analyzed the higher dose of ATP treatment (10 mM) to examine its toxic effect on lifespan. Figure 7A shows that the lifespan-extension effect observed at the low ATP dose (Fig. 5) diminished under the 10 mM treatment condition for NTT1 cells but not for Wt cells. Figure 7B shows that elimination of functional mitochondria rescues this mitochondrial toxicity in NTT1 cells, such that these cells extend their lifespan to a magnitude comparable to Wt under 10 mM ATP treatment conditions.

      I think you should make sure your pinhole is opened up to catch all the signal in z from each cell… It seems like taking the mean intensity of the top 40% of pixels in a cell can create technical artifacts… Please justify why you use that approach.

      We have added justification for the top-40%-pixel approach to the Methods: because the QUEEN reporter is a soluble cytoplasmic protein excluded from the large vacuoles that occupy an increasing fraction of cell volume as mother cells age, whole-cell or full-z-stack quantification systematically underestimates cytoplasmic ATP signal in older cells for reasons unrelated to ATP abundance. Restricting analysis to the brightest pixels focuses quantification on reporter-containing cytoplasm and avoids this age-confounded dilution artifact.

    1. Author response:

      The following is the authors’ response to the previous reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Objectives of the study and impact of the work

      The authors of this article primarily aim to reconstruct the evolutionary history of the insect odorant receptor (OR) family, which is responsible for the detection of odorant signals by olfactory neurons. Due to the lack of phylogenetic signal present in the sequences of this multigene family, which evolves very rapidly, phylogenetic analyses have so far never made it possible to precisely retrace how ORs diversified prior to the appearance of present-day insect orders, and what the drivers of this diversification were. For example, one may suspect that the adaptation of ORs to odors emitted by plants constituted a critical step in insect evolution during the "angiosperm terrestrial revolution," which occurred at the end of the Cretaceous, but nothing currently allows this to be asserted.

      There are very nice examples, notably in drosophilids, derived from comparisons between closely related species and documenting mechanisms of OR adaptation to certain signals. However, what the authors attempt to do in this work is to produce a macroevolutionary analysis at the scale of insects as a whole, based almost exclusively on bioinformatic analyses. To do this, they annotated OR genes in about one hundred insect species and developed pipelines for analyzing sequence similarity, structural similarity and functional similarity, the latter being estimated through a molecular docking approach. An important element in the evolution of insect ORs is the appearance of a unique co-receptor, called Orco, which appears to be an OR that has lost the ability to bind odorants. In addition to the large-scale bioinformatic analysis, the authors also aim to explore more specifically the factors that favored the emergence of Orco and the selective advantage conferred by the existence of OR-Orco complexes.

      Given the importance of odorant receptors in insect biology and in their adaptation to different environments and lifestyles, retracing their evolutionary history is indeed a major question in evolutionary biology. In principle, this type of work therefore has the potential to become a reference in the field and to provide a basis for significant scientific advances.

      Major strengths and weaknesses

      The sampling chosen for collecting OR sequences is very impressive, with more than 100 insect families represented, covering most of the major orders. This sampling appears appropriate for the question being addressed. The analysis pipeline used to collect the sequences makes sense, relying on homology-based annotation tools coupled with a structure-based filter. Nevertheless, one can note aberrant numbers of ORs for certain species (much lower than reality). A lower number of OR genes is somewhat expected, as the authors chose to apply a fairly stringent filter on sequence quality (based on predicted 3D structure), which reduces the number from 14,000 to 9,000. This choice seems logical given the subsequent use of these data, but it inevitably leads to data loss. However, the low number of genes also results from the fact that the pipeline did not function correctly for all genomes.

      In the revised version of the manuscript, the authors included a benchmarking step, which is a good point. They compared their OR gene annotations with previous reports in the same species. Unfortunately, this comparison is irrelevant because the chosen reference OR repertoires are actually a mix of transcriptome and genome annotations. Furthermore, comparisons with entire OR gene repertoires essentially demonstrate that their annotation was of good quality for species in which OR sequences were already present in the query OR database, but poor for species in which they were not. Therefore, these supplementary analyses made by the authors are not particularly in favor of an overall good quality of OR gene repertoires in the >110 species studied. The fact that some OR genes may be missing and that the total number may not be exact for each species is not prohibitive for studying the evolution of the family on a broad scale. However, it does call into question the correlation between the number of ORs and lifestyles and diets.

      Thank you for this important comment. We agree that it is inappropriate to directly compare genome-based OR annotations with OR repertoires derived solely from transcriptomes, because transcriptome-only datasets generally do not capture the complete OR gene complement of a species. We therefore repeated the benchmarking analysis and collected, wherever available for the species included in this study, published OR repertoires based on genome annotation or genome annotation supported by transcriptomic evidence. Transcriptome-only OR datasets are no longer included in this comparison.

      The updated benchmarking analysis shows that, for most species with comparable genome-based reference repertoires, the number of ORs identified in this study exceeds 70% of the previously reported number, with good agreement in OR repertoire size for most species (Table S1). Diabrotica virgifera is an exception: a previous manual annotation reported 124 complete ORs, whereas we identified 78, approximately two-thirds of the previously reported number. This result indicates that our automated annotation and stringent structural filtering pipeline may indeed underestimate OR repertoire size in some species. The large, repeat-rich genome of this species may further complicate gene prediction and the reconstruction of OR loci. We have therefore explicitly stated in the revised manuscript that incorporating transcriptomic evidence and manual curation may help recover more complete OR repertoires from such complex genomes.

      Another notable outlier is Anagrus nilaparvatae. A previous study reported 88 ORs, whereas we identified 330. Examination of the methods used in that study revealed that its OR search relied primarily on homology searches using known OR sequences from two other hymenopteran species. Because insect ORs constitute a rapidly evolving gene family with pronounced lineage-specific expansions, a limited query set may fail to detect highly divergent or species-specific ORs. In comparison, our study used OR queries from a broader range of insects and a genome-level annotation pipeline specifically designed for insect ORs, which may have enabled the detection of more highly divergent candidate ORs. Because the protein sequences of the 88 ORs were not made available in the original study, we are currently unable to perform a one-to-one comparison to verify whether all of these ORs are included in our annotations.

      You also noted that our better performance in species such as Drosophila melanogaster, Anopheles gambiae, and Bombyx mori might partly reflect the inclusion of known OR sequences from these species in the query database. We consider this an important and directly testable question. We therefore divided the benchmark species into two groups according to whether conspecific OR sequences were represented in the query database, and used ln(OR count_this study / OR count_previous) to quantify differences in OR counts relative to previous genome-based annotations. No significant difference was detected between the two groups (P = 0.841, Fig. S1 B). Given the unusually large difference in OR counts between the two studies for A. nilaparvatae, we also performed a sensitivity analysis excluding this species, which yielded the same conclusion (P = 0.413, Fig.S1 C). Thus, among the species for which comparable genome-based reference repertoires are currently available, we found no evidence that the inclusion of conspecific ORs in the query database systematically affected the final OR repertoire size. We have added this analysis to the supplementary material of the revised manuscript.

      Finally, we agree that annotation biases in OR repertoire size may affect analyses of its correlations with ecological traits. We therefore repeated all relevant ecological sensitivity analyses using an updated OR count dataset, taking the larger of the OR counts from our study and the previous annotation for each species (Fig. S1 D- G). The main statistical results remained consistent with the original analyses: OR counts were still significantly associated with adult diet, larval diet, and habitat, whereas no significant association was detected with circadian rhythm. We therefore consider the statistical associations between OR counts and the main ecological variables to be reasonably robust within the range of annotation discrepancies detectable using the currently available genome-based benchmarks, although automated annotation and stringent structural filtering may underestimate OR counts in some species. The updated benchmarking analyses are described in Supplementary Text S1 and summarized in Table S1.

      The following revision has been added (lines 103-107): “Benchmarking against curated OR repertoires showed that the automated pipeline recovered most previously reported ORs and that stringent structural filtering produced a high-confidence set of structurally intact receptors (Supplementary Text S1, Tables S1–S3, and fig. S1B–C). For most species with comparable genome-based references, retained OR counts exceeded 70% of published values.”

      From the dataset collected, the authors attempted to categorize ORs in several ways, starting with the reconstruction of sequence similarity networks. The approach is interesting, but fails to reveal homology relationships between ORs from species belonging to different insect orders. So it is unclear what the advantage of this approach is compared with the "classical" phylogenetic approach.

      Thank you for raising this important question. Our intention was not to replace classical phylogenetic analysis with sequence similarity networks. Rather, we used network-based approaches as a class-wide framework to classify ORs independently according to sequence similarity, structural similarity, and docking profiles, and then compared how these different classifications correspond across insect taxa and major macroevolutionary transitions.

      For smaller gene families with limited sequence divergence, defining subfamilies based on gene trees is a well-established and highly effective approach, because phylogenetic trees can both identify subfamilies and reveal their evolutionary relationships. However, the insect OR superfamily exhibits pronounced birth-and-death evolution, with frequent gene duplications and losses across lineages, and comprises a vast number of highly divergent sequences. Consequently, when a single phylogenetic tree is constructed for the entire OR superfamily, deep nodes often lack sufficient support, and relationships among subfamilies may be difficult to resolve consistently. It is therefore challenging to obtain a stable and consistent classification of thousands of ORs into subfamilies across insects using a single gene tree alone. We therefore used sequence similarity networks as a complementary classification approach. Their main advantage is that they allow large datasets to be grouped according to sequence similarity among all ORs without requiring the resolution of every deep phylogenetic relationship. More importantly, similar network frameworks can be used to construct sequence similarity, structural similarity, and docking-profile similarity networks, allowing SeqC, StrC, and dPC to be compared directly within a common analytical framework. This is difficult to achieve using conventional gene trees alone and is the main reason for our choice of a network-based approach.

      Sequence similarity networks alone cannot directly resolve homology relationships among ORs from different insect orders. During the previous revision, we therefore sought to link sequence communities to phylogenetic relationships. We conducted additional phylogenetic analyses of shared sequence communities containing multiple insect orders to search for potentially conserved OR lineages spanning different orders. However, among these shared communities, we identified only one conserved OR lineage spanning four insect orders with relatively clear phylogenetic support. We have added this result to the Supplementary Data S6. This finding further indicates that clearly identifiable orthology relationships spanning multiple orders are very limited among extant insect ORs.

      The following revision has also been added (lines 150-154): “The SSN is not intended to replace phylogenetic reconstruction, but rather to provide a complementary framework for summarizing sequence relationships among thousands of highly divergent ORs at a class-wide scale. It allows major patterns of OR sequence similarity and diversification to be visualized more clearly across the entire dataset. Phylogenetic analyses can then be used to further resolve evolutionary relationships within specific sequence communities.”

      The clustering based on structure also leads to the identification of a majority of "orderspecific" clusters, which does not provide major insights into the evolution of ORs. However, the authors highlight a group of ORs in flies that appear to possess an unusual intracellular region, as well as a cluster of OR shared across many insect orders that exhibit a larger binding cavity. This is really interesting, although more relevant to OR structure than to their evolution.

      Thank you for this important comment. We agree that the previous version of the manuscript focused primarily on structural differences among structural communities and did not adequately explore their potential evolutionary implications. StrC23 is the most widely distributed structural community, spanning 12 insect orders and containing 46.3% of the ORs. We further found that its putative binding pockets were significantly larger than those of other ORs, which we previously interpreted as a potentially conserved structural pattern across taxa. Following your suggestion, we conducted additional analyses of the phylogenetic and orthology relationships within StrC23. The results showed that StrC23 does not correspond to a single, broadly conserved orthogroup spanning insect orders, but instead contains 156 distinct orthologous groups. Of these, 24 encompass more than 10 species. Only a few of these larger groups span multiple insect orders: one contains ORs from Hymenoptera, Diptera, and Trichoptera, and two contain ORs from both Lepidoptera and Trichoptera. The remaining groups show pronounced order specificity, including nine Hymenoptera-specific groups, eight Lepidoptera-specific groups, and four Diptera-specific groups.

      These results indicate that the large putative binding pocket shared by StrC23 members cannot simply be attributed to a single conserved orthologous lineage spanning multiple orders, but is distributed across several phylogenetically independent OR lineages. This pattern may reflect convergent evolution toward similar structural features in different OR lineages, or the retention of an older structural feature in multiple OR lineages that subsequently underwent substantial sequence divergence. The current data do not allow us to distinguish conclusively between these two possibilities. We have added the phylogenetic and orthologous-group analyses of StrC23 to the revised manuscript and supplementary material to further clarify the evolutionary implications of this structural community shared across insect orders.

      The following revision has been added (lines 208-218): “To further investigate the evolutionary basis of this broadly shared structural feature, we examined the phylogenetic and orthology relationships among StrC23 receptors. StrC23 was divided into 156 orthologous groups, 24 of which contained ORs from more than 10 species. However, only a few of these larger groups spanned multiple insect orders: one included ORs from Hymenoptera, Diptera, and Trichoptera, while two included ORs from both Lepidoptera and Trichoptera (Supplementary Data S6). Thus, StrC23 does not represent a single conserved cross-order orthologous lineage, but instead comprises multiple phylogenetically distinct OR lineages. Its shared large-pocket architecture therefore cannot be explained solely by conservation of a single orthologous lineage and may reflect either structural convergence or retention of an ancient structural feature followed by substantial sequence divergence.”

      The analysis of structural diversity then leads the authors to focus on the Orco co-receptors, which are characterized by modifications of the binding pocket and the appearance of an extracellular loop that could explain the loss of the ability to bind odorant molecules. This part, which relies on in vitro experiments, is interesting and constitutes the most striking result of this study, which could in itself have been the subject of a separate manuscript.

      We thank the reviewer for the positive assessment of this part of our work.

      The rest of the manuscript is based on the prediction of OR response spectra using molecular docking. The work that has been carried out is extremely substantial, and the objective of linking clusters based on sequence similarity or 3D structural similarity with functional categories is entirely relevant. The docking score threshold used was chosen thoughtfully, which is very good, and according to the calculation performed should ensure a true positive rate of more than 20%, which is excellent in such a docking analysis. But in the absence of functional validation, this 20% true positive rate is not sufficient to extrapolate OR function, and docking-derived binding breadth measures used in the remaining of the manuscript have to be taken with caution, as acknowledged by the authors themselves. Consequently, the chance that results of this part of the work will enlighten the evolution of OR on a broad scale is low. For example, the fact that insect lineages that emerged after the Permian-Triassic extinction have more broadly-tuned OR is an interesting observation, yet remains highly speculative.

      Thank you for this important comment. We agree that, even after optimizing the docking threshold, the current hit rate of approximately 20% remains insufficient to interpret molecular docking results as reliable predictions of actual OR ligand responses or functions. We also acknowledge that the biological implications of some docking results were still overstated in the previous revision, potentially leading readers to interpret these computational results as approximations of actual OR function. To avoid this misunderstanding, we have further revised the relevant terminology and interpretation of results throughout the latest manuscript. For results derived entirely from molecular docking, we no longer use terms such as ‘docking-derived function’, ‘functional community’, or other expressions that might imply experimental evidence of function. Instead, we consistently use ‘docking profile’ to make clear that these analyses reflect only similarities in computational docking patterns among receptors.

      In addition, following your comments and the related suggestions from Reviewer 2, we have removed all results and discussion that directly linked docking-based predictions of OR function or recognition breadth to species ecology. We have explicitly presented the few remaining macroevolutionary comparisons as hypothesis-generating observations rather than evidence of functional evolution. For example, differences in docking-profile composition among extant insect lineages that originated before or after the end-Permian mass extinction (EPME) are now described only as a broad statistical pattern, with any interpretation framed as an experimentally untested hypothesis. Whether this pattern reflects actual differences in receptor tuning, and whether it is evolutionarily linked to environmental changes associated with the EPME, still requires testing through broader taxonomic sampling, reliable ancestral-state reconstruction, and functional experiments. We hope that these revisions restrict the interpretation of molecular docking results to what the evidence can support and bring the corresponding conclusions into closer alignment with the current strength of evidence.

      The following revision has been added in Result section (lines 367-369): “These observations should be interpreted as a docking-derived comparative pattern among extant lineages rather than direct evidence of ancestral functional changes across the

      EPME.”

      And Discussion section (lines 410-414): “However, this interpretation remains hypothetical. Because rapid OR evolution and limited cross-order orthology preclude reliable reconstruction of deep ancestral repertoires, the EPME-related pattern should be viewed as a descriptive comparison among extant lineages. Further validation will require broader taxon sampling, ancestral reconstruction, and experimental testing of receptor tuning breadth.”

      In summary, despite the large number of analyses performed, the authors do not really succeed in achieving the stated objective of reconstructing the evolutionary history of insect ORs, and the results obtained do not strongly support all the conclusions regarding the links between OR repertoires and environment or lifestyle.

      Thank you for this important comment. We agree that ‘reconstructing the evolutionary history of insect ORs’ was too broad a formulation and exceeded what our methods could reliably address. A rigorous reconstruction of evolutionary history requires well-resolved phylogenetic relationships across taxa, ancestral-state inference, and systematic analysis of gene duplication and loss events. We have therefore redefined the scientific objectives of this study. The revised manuscript no longer claims to have reconstructed the evolutionary history of insect ORs. Instead, it aims to systematically characterize insect OR diversity and classification patterns at the levels of sequence, structure, and docking profile, compare the correspondence among these levels, and describe differences in their distribution across insect taxa and broad macroevolutionary contexts.

      We have also reassessed the strength of different types of evidence concerning the relationships between OR repertoires and environment or lifestyle. For relationships between OR repertoire size and ecological traits, we repeated the genome-based benchmarking. After rerunning the ecological correlation sensitivity analyses using the updated OR count dataset, the main statistical results remained consistent with the original analyses. We therefore consider the current data to continue to support statistical associations between OR counts and ecological traits, with a degree of robustness. By contrast, we have removed results and discussion directly linking predicted OR function or recognition breadth to species ecology, and no longer use terms such as ‘docking-derived function’ or ‘functional community’ that might imply experimental evidence of function. The remaining macroevolutionary comparisons of docking profiles, such as differences in docking-profile composition among groups considered in relation to the EPME, are treated only as hypothesis-generating comparative patterns, rather than direct evidence of receptor functional evolution. We explicitly state that these hypotheses require future testing through functional experiments and more reliable ancestral-state reconstruction.

      In summary, we have redefined the study objectives and no longer describe this work as a reconstruction of insect OR evolutionary history. We have retained the statistical associations between OR counts and ecological traits that remained supported after reassessment, while removing results and discussion linking receptor function to ecology on the basis of molecular docking. We believe these revisions better align the scientific objectives and scope of the conclusions with the evidence provided by the available data and methods.

      We have revised the final paragraph of the Introduction to clarify the scope and objectives of this study (lines 80-91): “In this study, we characterized large-scale patterns of OR diversification across 115 species spanning 16 insect orders. Using a framework that integrates network analysis, protein structure prediction, and molecular docking, we constructed sequence-similarity (SSN), structural-similarity (StSN), and docking-profile similarity networks (dPSN) to classify ORs from three distinct perspectives. We identified differences in OR sequence-community diversity between holometabolous and non-holometabolous insects, as well as differences in docking-profile community composition among extant lineages whose order-level origins fall on opposite sides of the end-Permian mass extinction (EPME). Across this class-wide sampling, OR repertoire size was associated with adult diet, larval diet, and habitat, but not with circadian rhythm. Moreover, the conserved β-sheet in the extracellular loop 2 (EL2) region of Orco, together with its specialized binding-pocket architecture, is associated with its reduced ligand-binding capacity and represents a prominent structural specialization of the co-receptor lineage.”

      Reviewer #2 (Public review):

      The remarkable evolvability of the olfactory system enables animals to rapidly adapt to dynamic and chemically complex environments. Over the past two decades, substantial effort has been devoted to uncovering the evolutionary principles that drive the diversification of odorant receptors (ORs), yielding key insights into the forces shaping their striking variability in both vertebrates and insects. In this manuscript, Zhang and colleagues analyze the OR repertoires of over 100 insect species, leveraging sequence and structural similarity to infer patterns of gene family evolution within this diverse and ecologically important clade. By integrating sequence-based and structure-based comparisons, their study builds on a compelling and recently emerging line of research made possible by the advent of AlphaFold, which has previously clarified the phylogenetic relationship between insect Ors and the gustatory receptor gene family and revealed the unexpectedly deep evolutionary origins of this ancient structural fold.

      Applying this approach to a large set of ORs derived from species throughout the insect phylogeny, the authors confirm many previously reported patterns of OR evolution. More importantly, with their large-scale approach the authors found new structural features of different Or clades, resulting in intriguing testable hypotheses about Or evolution that have the potential to support future directions in studying this important gene family. For example, the authors identify a structural feature mostly unique to the OR co-receptor ORco, a beta-sheet in EL2, which they functionally show reduces odorant binding affinity - a key aspect of ORco, which does not bind ligands in the ancestral ligand-biding site. This is a particularly strong part of the manuscript, since the authors support their in silico-derived hypothesis with functional data.

      We thank the reviewer for the positive assessment of this part of our work.

      In an attempt to assess the relationship between sequence identity and structure on one hand and function on the other, the authors perform an in-silico structure prediction and chemical docking analysis. While not suitable to assess the actual function of individual receptors without functional testing, this strategy revealed potential receptor clades with differences in the number and type of docked chemicals. As a response to the previous reviews, the authors now changed their writing to refer to these results as 'docking-derived function' instead of just 'function'. While I appreciate that the authors changed their wording, this semantic change still can be read as referring to dockingderived predictions as conclusions of actual biological function. However, this is not the case. Any functional claims based solely on the docking approach need to be interpreted with caution, as in silico-only approaches are currently not well enough predictors for actual receptor function. Accordingly, I strongly recommend to remove the parts that connect receptor function to structure or ecology.

      Thank you for highlighting this important issue again. We agree with your comments and acknowledge that the presentation of molecular docking results in the previous revision still overstated their biological implications. Following your suggestion, we have removed all results and discussion that directly linked receptor function to species ecology solely on the basis of molecular docking, to avoid interpreting computational predictions as actual biological functions. We then systematically reviewed and revised docking-related terminology throughout the manuscript. For results derived entirely from docking analyses, we no longer use ‘docking-derived function’, ‘functional community’, or other expressions that might imply experimental evidence of function. Instead, we consistently use ‘docking profile’ to clarify that these analyses reflect similarities in computational docking patterns among receptors, rather than experimentally validated functional categories.

      Through these revisions, we hope to distinguish more clearly between computational docking profiles and experimentally validated receptor function, and to avoid biological interpretations of docking results that exceed the available evidence. We believe these changes bring the manuscript's conclusions into closer alignment with the strength of the evidence.

      Assessing their docking analyses with respect to species ecology, the authors identify correlations suggesting that Or repertoires might follow predictable evolutionary trajectories broadly aligned with species ecology. These are interesting hypotheses. However, due to the inability to predict actual receptor function the author's claims about ecology-function relationships are not well supported. Accordingly, the authors should change the respective parts of the manuscript in way that it is clear these are currently untested hypotheses. This includes adjusting the title, since the work does not find any experimental support for ecological tuning.

      Thank you for this important suggestion. We agree that the current molecular docking analyses cannot support direct conclusions about relationships between actual receptor function and species ecology. Following your suggestion, we have removed the results and discussion directly linking docking-based predictions of OR function to species ecology. For the remaining macroevolutionary comparisons, such as differences in docking-profile composition among groups considered in relation to the EPME, we explicitly state that these results represent only computational patterns observed in extant taxa. The evolutionary interpretations proposed from these patterns remain experimentally untested hypotheses and cannot be considered direct evidence of changes in actual receptor function.

      In addition, following your suggestion, we have changed the manuscript title to ‘Classwide sequence, structural, and docking-profile diversity of insect odorant receptors and structural specialization of Orco’. The new title no longer emphasizes ‘ecological tuning’ or ‘olfactory perception’, but instead focuses on class-wide diversification of insect OR sequences, structures, and docking profiles, together with the experimentally supported structural specialization of Orco.

      The following revision has been added in Result section (lines 367-369): “These observations should be interpreted as a docking-derived comparative pattern among extant lineages rather than direct evidence of ancestral functional changes across the EPME.”

      And Discussion section (lines 410-414): “However, this interpretation remains hypothetical. Because rapid OR evolution and limited cross-order orthology preclude reliable reconstruction of deep ancestral repertoires, the EPME-related pattern should be viewed as a descriptive comparison among extant lineages. Further validation will require broader taxon sampling, ancestral reconstruction, and experimental testing of receptor tuning breadth.”

      I believe that future studies combining functional testing with an explicit evo-eco framework could benefit from this work and the explicit hypotheses it generates. But the authors should be careful to not overstate their in-silico derived results.

      Thank you for this suggestion. We have revised the manuscript accordingly.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      Below are my comments in response to the rebuttal letter. I thank the authors for their careful revision and detailed responses to the points raised in my review.

      (1) OR annotation pipeline and correlation analyses

      Previous comment: "One can note aberrant numbers of ORs for certain species (much lower than reality), which indicates that the pipeline probably did not function correctly for all genomes. In the absence of a validation step comparing the results with already known OR repertoires, it is difficult to estimate the overall quality of the data. [...] It calls into question certain results that rely on this total number, such as the correlation between the number of ORs and genome size, lifestyle, and diet."

      The response made by the authors on that point is not particularly convincing. They compared their OR gene annotations with previous reports in the same species, but this comparison is irrelevant because the chosen reference OR repertoires are actually a mix of transcriptome and genome annotations (the OR counts for Harmonia axyridis, Plutella xylostella, Pierus brassicae, Dendrolimus kikuchii, Carposina sasakii, Hermetia illucens, Chlorops oryzae and Propsilocerus akamusi are from transcriptomes). As not all OR genes are expressed in a given tissue, the number of ORs in transcriptomes is always lower than in genomes. Furthermore, comparisons with entire OR gene repertoires essentially demonstrate that their annotation was of good quality for species in which OR sequences were already present in the query OR database (Bombyx mori, Drosophila melanogaster, Anopheles gambiae) but was of bad quality for species in which OR sequences were NOT in the query (Diabrotica virgifera). However, re-annotation of Diabrotica led to an OR repertoire of 78 complete genes, vs. 124 in the manually curated genome annotation (1/3rd of the genes are missing). So these supplementary analyses made by the authors are not particularly in favor of an overall good quality of OR gene repertoires in the >110 species studied. They have also repeated the correlation analyses using 'full' OR gene sets where available. This showed that the correlation of OR count with genome size is no longer valid, but the correlation with diet or lifestyle is. However, if a mix of gene numbers from transcriptomes and genomes was used (see my comment above), I am afraid that these novel correlation analyses are not relevant. In conclusion, I would disagree with the claim that "These new benchmark and sensitivity analyses directly strengthen the evidence supporting our dataset and its ecological interpretations".

      Thank you for further highlighting this issue. As detailed in our response to the Public Review, we repeated the OR annotation benchmarking, excluded transcriptome-only repertoires, and restricted comparisons to genome-based reference datasets or genome-based datasets supported by transcriptomic evidence. The updated results show that, for most species with comparable reference data, the number of ORs identified in this study exceeds 70% of the previously reported number. We also explicitly acknowledge that repertoire size may still be underestimated in some species.

      We also directly tested whether query database composition systematically affected the number of annotated ORs. No significant difference was detected between species with and without conspecific OR queries (P = 0.841; P = 0.413 after excluding Anagrus nilaparvatae). Thus, we currently find no evidence that conspecific queries systematically increase the final OR count.

      In addition, we repeated the sensitivity analyses of ecological correlations using the updated OR count dataset. The main statistical results remained unchanged: OR counts were still significantly associated with adult diet, larval diet, and habitat, but not with circadian rhythm. We therefore consider these statistical associations between OR counts and ecological traits to be reasonably robust to the annotation differences currently detectable. Detailed results are provided in our response to the Public Review and in the revised supplementary text S1.

      (2) sequence similarity-based clusters

      Previous comment: "The authors attempted to categorize ORs in several ways, starting with the reconstruction of sequence similarity networks. The approach is interesting, but in the end, the results do not seem to be sufficiently exploited. [...] For example, clusters SeqC26 or SeqC28, which appear to be shared by many insects, are potentially very interesting. It might have been relevant to combine this similarity-based clustering approach with phylogenetic reconstructions within each shared cluster."

      The authors have followed this suggestion and identified an orthogroup conserved across several insect orders, which is an interesting observation. However the phylogeny of this orthogroup should be provided in supplementary data, which does not seem to be the case.

      We thank the reviewer for the positive assessment. The corresponding phylogenetic tree has been added to the supplementary data S6.

      (3) structure-based clusters

      Previous comment: "The clusters shared by several orders are not truly exploited, which does not provide new insight into the evolution of ORs"

      The authors show an interesting feature for a cluster of ORs from several insect orders, with a large putative binding pocket. However, it is not clear whether they verified or not if this cluster also correspond to an orthogroup or if this shared feature (a large binding pocket) is a convergence. They also improved the discussion of their results on a cluster of fly ORs with a long intracellular domain, which is a good thing.

      Thank you for this important question. To determine whether StrC23, a structural community shared across multiple insect orders, corresponds to a conserved orthogroup, we performed additional phylogenetic analyses of its OR sequences and identified orthology relationships within the community based on the gene tree. The results showed that StrC23 does not correspond to a single orthogroup spanning insect orders, but instead contains 156 distinct orthologous groups. Of these, 24 encompass more than 10 species. Among these 24 larger groups, one contains ORs from Hymenoptera, Diptera, and Trichoptera, and two contain ORs from both Lepidoptera and Trichoptera. The remaining groups show pronounced order specificity, including nine Hymenoptera-specific groups, eight Lepidoptera-specific groups, and four Diptera-specific groups.

      These results indicate that the large putative binding pocket characteristic of StrC23 is not explained by a single, broadly conserved orthogroup spanning multiple orders, but is distributed across several phylogenetically independent OR lineages. We therefore consider that this shared structural feature cannot simply be interpreted as direct retention within a conserved orthologous lineage. It may reflect convergent evolution toward similar structural features in different OR lineages, or the retention of an older structural feature in multiple OR lineages that subsequently underwent substantial sequence divergence. The current data do not allow us to distinguish conclusively between these two possibilities. We have added the phylogenetic analysis of StrC23 to the revised manuscript to clarify the evolutionary relationships within this structural community.

      The following revision has been added (lines 208-218): “To further investigate the evolutionary basis of this broadly shared structural feature, we examined the phylogenetic and orthology relationships among StrC23 receptors. StrC23 was divided into 156 orthologous groups, 24 of which contained ORs from more than 10 species. However, only a few of these larger groups spanned multiple insect orders: one included ORs from Hymenoptera, Diptera, and Trichoptera, while two included ORs from both Lepidoptera and Trichoptera (Supplementary Data S6). Thus, StrC23 does not represent a single conserved cross-order orthologous lineage, but instead comprises multiple phylogenetically distinct OR lineages. Its shared large-pocket architecture therefore cannot be explained solely by conservation of a single orthologous lineage and may reflect either structural convergence or retention of an ancient structural feature followed by substantial sequence divergence.”

      (4) molecular dynamics simulation

      Previous comment: "The molecular dynamics modelling does not add anything in the way it is conducted (5 ns is too short)."

      The authors argue that such a short simulation is sufficient for testing the interaction between a compound and the extracellular beta-sheet of the coreceptor Orco. I'm not a specialist enough to confirm whether this is actually true, but I trust the author's expertise in this area.

      We thank the reviewer for the positive assessment.

      (5 / 6) molecular docking and functional extrapolation

      Previous comment: "in the absence of functional validation, this 20% true positive rate is not sufficient to extrapolate OR function"

      The authors argue that molecular docking was not used to identify specific OR/ligand pairs, but rather to "estimate the potential binding tendencies of OR repertoires". I agree with this point; correlations were made using "binding breadth index values" that are calculated for entire OR repertoires. The text of the manuscript has been edited to refer to "docking-derived" functional clusters and binding breadth index, and to emphasise that the results should be interpreted with caution, which is a good point as it will prevent potential misinterpretation by the reader. However, this does not change the fact that interpreting the olfactory capacity of one species based on docking-derived binding breadth values of its OR repertoire is highly speculative (especially when OR repertoires are incomplete) and the chance that results of this part of the work will enlighten the evolution of OR on a broad scale is low.

      Thank you for raising this concern. We agree that repertoire-level analyses do not resolve the inherent limitations of molecular docking in predicting actual receptor function. Although such analyses summarize overall docking patterns rather than individual OR–ligand interactions, they still cannot reliably define a species’ true olfactory capabilities. It therefore remains insufficient to describe a species' actual olfactory capabilities solely on the basis of docking-derived binding breadth. As detailed in our response to the Public Review, we have addressed this issue by following your suggestions and those of Reviewer 2 and removing the results and discussion that used the binding breadth index to directly link predicted receptor function to ecological traits such as diet, habitat, and circadian rhythm. We have also further standardized the terminology, replacing ‘docking-derived function’, ‘functional community’, and other expressions that could imply experimentally established function with ‘docking profile’, to emphasize that these results describe computational docking patterns rather than experimentally determined receptor functions. Through these revisions, we hope to distinguish more clearly between computational docking patterns and experimentally established receptor functions, and to restrict the interpretation of the related macroevolutionary comparisons to what the current data can support.

      (7) EPME

      Previous comment: "ORs of non-holometabolous insects cannot be considered equivalent to those of species that existed before the Permian-Triassic extinction"

      The authors have now clarified the fact that they compared extant insect orders rather than ancestral and derived OR repertoires.

      We thank the reviewer for the positive assessment of the revised manuscript.

      (8 to 16)

      The authors have carefully considered all the points raised in the recommendations for the authors, improving the manuscript on several aspects.

      We thank the reviewer for the positive assessment of the revised manuscript.

      Minor comment

      Line 217: Orco did not emerge in the ancestor of Zygentoma, it emerged in the common ancestor of Zygentoma and Pterygota.

      Thank you for pointing this out. We have corrected the statement.

      Reviewer #2 (Recommendations for the authors):

      The authors have done a good job in their revision of the manuscript. They addressed many of the reviewers' concerns well.

      We thank the reviewer for the positive assessment of our previous revision.

      However, the functional claims are still too strong and need to be removed or tempered down as described in the public review.

      Thank you for this suggestion. We have removed or tempered the functional predictions in the manuscript in accordance with the Public Review. Please see our response to the Public Review for details.

      Further, the manuscript title is not a good fit for the content. I would argue that the paper does not 'reveal ecological tuning shaping olfactory perception', since Or structurefunction relationships are involved in olfactory sensation or detection. Perception, however, requires interpretation, which is done by neural circuits but not receptors expressed within. Further, I still think that referring to 'ecological tuning' is far-fetched based on the docking approach that cannot really resolve the tuning of receptor sets. I would think that the work reveals interesting correlations between docking-derived population tuning and ecology. But that does not necessarily have anything to do with actual function and thus may not make much sense to advertise in the title or abstract.

      Thank you for your suggestions concerning the manuscript title. Following this comment, we have changed the title from ‘Evolutionary dynamics of insect odorant receptors reveal ecological tuning shaping olfactory perception’ to ‘Class-wide sequence, structural, and docking-profile diversity of insect odorant receptors and structural specialization of Orco’ The new title no longer emphasizes ecological tuning or olfactory perception, but instead focuses on the two aspects of this study supported by the most direct evidence: class-wide patterns of sequence and structural diversification in insect ORs, and the experimentally supported structural specialization of Orco.

      Consistent with the revised title, we have further adjusted the relevant wording in the Abstract, Results, and Discussion, and removed content directly linking receptor function to species ecology on the basis of docking results. We believe that the revised title and abstract more accurately reflect the main content of the study and the scope of its evidence, while avoiding functional or ecological interpretations of computational predictions that exceed their evidential support.

      I suggest selecting a title that fits the sequence/structure/in silico docking nature of their large macroevolutionary approach and findings better. After all, apart from the orco work this manuscript is mostly a resource of in silico predictions.

      Thank you for this suggestion. We have revised the manuscript title.

      Author response table 1.

      Numbers of OR genes in previously annotated species.

      Reference

      Carey AF, Wang G, Su CY, Zwiebel LJ, Carlson JR. 2010. Odorant reception in the malaria mosquito Anopheles gambiae. Nature 464: 66-71.

      Engsontia P, Sangket U, Chotigeat W, Satasook C. 2014. Molecular evolution of the odorant and gustatory receptor genes in lepidopteran insects: implications for their adaptation and speciation. J Mol Evol 79: 21-39.

      Ma Y, Guo Z, Wang L, Wang B, Huang T, Tang B, Zhang G, Zhou Q. 2022. The genome of the rice planthopper egg parasitoid wasp Anagrus nilaparvatae casts light on the chemo- and mechanosensation in parasitism. BMC Genomics 23: 541.

      Mier P, Fontaine JF, Stoldt M, Libbrecht R, Martelli C, Foitzik S, Andrade-Navarro MA. 2022. Annotation and Analysis of 3902 Odorant Receptor Protein Sequences from 21 Insect Species Provide Insights into the Evolution of Odorant Receptor Gene Families in Solitary and Social Insects. Genes (Basel) 13.

      Paddock KJ, Corcoran JA. 2025. Life-stage dependent behavior mimics chemosensory repertoire diversity in a belowground, specialist herbivore. G3 (Bethesda) 15.

      Robertson HM, Warr CG, Carlson JR. 2003. Molecular evolution of the insect chemoreceptor gene superfamily in Drosophila melanogaster. Proc Natl Acad Sci U S A 100 Suppl 2: 14537-14542.

      Tanaka K, Uda Y, Ono Y, Nakagawa T, Suwa M, Yamaoka R, Touhara K. 2009. Highly selective tuning of a silkworm olfactory receptor to a key mulberry leaf volatile. Curr Biol 19: 881-890.

      Wang Q, Dicke M, Haverkamp A. 2023. Sympatric Pieris butterfly species exhibit a high conservation of chemoreceptors. Front Cell Neurosci 17: 1155405.

      Xiao S, Ye X, Wang S, Yang Y, Fang Q, Wang F, Ye G. 2023. Genome assembly of the ectoparasitoid wasp Theocolax elegans. Sci Data 10: 159.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      The authors aim to understand, in the context of leaf shape, how the constraints imposed by development inform evolution. Leaf shape is a good place to study the influence of development on evolution because it is a trait that exhibits a lot of diversity, and the developmental mechanisms that give rise to leaf shapes are apparently rather conserved across angiosperms.

      As part of the motivation for their work, the authors cite a previous study (Geeta et al), which found that in angiosperm phylogenies, transitions from complex to simple leaf shapes occur through evolution more often than transitions in the opposite direction. Is this due to developmental constraints or adaptation?

      The authors undertake two parallel lines of work:

      (1) Extending the study of Geeta et al with more data, consisting of both phylogenies and a shape classification dataset. The conclusion from this line of inquiry is that transitions from lobed to unlobed leaves are more common than transitions away from unlobed leaves.

      (2) The authors conduct evolution simulations in a computational model of leaf development. Here, they look at {\it neutral} mutations and whether simply neutral evolution is sufficient to drive the observed trend.

      The conclusion of the second part of the work is that the driver of the evolution toward simple leaf shape is entropy: there are more ways to make unlobed leaves than to make lobed leaves (at least in terms of gene regulation parameters that will produce the two leaf types). The argument is that random gene regulatory networks are more likely to produce unlobed leaves than lobed leaves; therefore, neutral evolution drives this trend.

      Data Analysis

      Roughly $9000$ images of leaves were classified into 4 categories: unlobed, lobed, dissected, and compound. These labels were applied to the tips of 5 phylogenetic trees of angiosperms (3 resolved at the genus level and 2 at the species level). By fitting a continuous-time Markov chain to the labelled trees, the authors claim that there is a significantly higher rate of transition to the unlobed leaf shape compared to transitions to more complex shapes.

      Simulation

      First, the authors validate a computational model (Runions et al) for leaf growth on an experimental dataset. By changing parameters in the model, they can recapitulate the morphological changes in the shapes of Arabidopsis leaves engendered by expression of two particular genes.

      Then the authors run an evolutionary model (without selection, just random mutations) on top of the computational leaf development model. As the random walk in parameter space reaches a stationary distribution, they look at both the proportions of the leaf categories in the steady state as well as the transition rates between different categories. The result is that transitions to unlobed leaves are more common than from unlobed leaves.

      We thank the reviewer for the helpful and clear summary of our work.

      General Comments

      The authors use angiosperm phylogenies from other works as the basis for the data analysis part of their work. Given the centrality of these phylogenies for their conclusions, more information is needed about how these phylogenies were constructed and what they mean. What is the timescale that they span? What method is used to infer them? What regions of DNA were sequenced in order to build the phylogenies? Also, maybe some more discussion of angiosperm evolution (e.g., when was the most recent common ancestor of all angiosperms?) would help put the study in context.

      We also need a more in-depth discussion of the computational model. What are all the $>100$ parameters doing, and what informs the seemingly strange mutational model that changes parameters by 3 orders of magnitude?

      I am confused about how the rates of transitions were inferred from the phylogeny. Here, one has a phylogeny inferred by some method (which needs to be described in more detail), and just the leaves are labelled. It is stated in the methods that BayesTraits was used to infer the transition rates. I realize this method is probably documented elsewhere, but a bit of a summary of how it works and how to interpret its results would (1) make the paper more selfcontained and (2) if the algorithm is credible, make the results firmer.

      We thank the referee for the suggestion to make the paper more accessible. The tool we use to infer transition rates from the phylogenies, BayesTraits, is standard in the field. However, the referee is right that for an interdisciplinary journal, it may be helpful to more fully flesh out how these methods work. To that end, we have added an additional section S2.A "Phylogenetic rate inference" in the supplementary information that includes a longer description of how BayesTraits works, and how we used it to infer transition rates from phylogenies.

      All trees are shown in the supplementary information section S2.B "Phylogenetic trees" with scale bars showing the amount of time or genetic change that the trees span. We have added details of the specific genes used to construct the trees in our analysis in Methods section F. For a broader discussion of angiosperm evolution, there is supplementary information section S4 "A short literature review of the adaptive significance of leaf shape".

      Regarding the more in-depth discussion of the computational model, we have added supplementary information section S1.A "Leaf model details" to give a more detailed description of the leaf model. We chose our mutational scheme over other methods, such as uniform or Latin hypercube sampling, as the biologically relevant ranges for each parameter were unknown. Mutations of multiple orders of magnitude are a way to sample both parameters with large and small ranges with the same scheme.

      Additionally, larger mutations help to move a walk out of a local region if it is stuck while small mutations ensure sensitive parameters are still varied. We use multiple schemes for additional robustness.

      I am a bit skeptical of the authors' interpretation of the biological trend (of complex to simple leaf shapes) as being driven by neutral evolution. Why does one expect that the mutations generated by the random walk models described in the work are in fact neutral mutations?

      A random walk is a well-established way of modelling the dynamics of neutral evolution in the monomorphic regime, where the population has a narrow diversity of different genotypes. In the higher mutation rate polymorphic regime, where the diversity of genotypes in the population is larger, we also expect that a random walk should still recapitulate the correct average transition rates. The purpose of the simulations is not to model every aspect of population genetics, but to ask whether developmental bias alone is sufficient to generate the observed directional asymmetry. By assigning equal fitness to all viable leaves, we isolate the contribution of development from that of selection. The agreement with the phylogenetic transition rates therefore demonstrates sufficiency rather than exclusivity: selection may also contribute, but it is not required to explain the observed bias. We discuss the evidence for the role of adaptation in leaf shape further in supplementary information section S4 "A short literature review of the adaptive significance of leaf shape".

      - If the entropy of simple leaf shapes is higher than that of complex leaf shapes, why did we have complex leaves at all? I suspect the authors might argue that this is due to selection. In that case, what allows these complex shapes to become simpler? Wouldn't they be losing the selective advantage that drove them to be more complex in the first place? Or maybe the idea is that the rates are inferred assuming some steady state that generates the phylogeny? I did not understand this point.

      The entropy language is a useful framing. Within that framework, one can view our study as showing that the entropy (defined here as the logarithm of the volume of parameter space mapping to a phenotype) of simple leaf shapes is higher than that of complex leaf shapes. If this entropy were to be ignored, and were we not to take fitness differences into account, then all states would be equally likely in our simulations. What we show is that the differences in entropy, which are related to differences in volumes of the parameter space that map to different phenotypes, also affect the rates. The inferred transition rates for both simulation and phylogeny from unlobed to more complex shapes are lower than the reverse but not zero. Therefore, complex leaf shapes arise stochastically through mutation and in this model would eventually reach a steady-state proportion, even in the absence of selection. This steady state proportion for complex leaves would be smaller than that of unlobed leaves, but non-zero.

      Are the rates of transitions between leaf types inferred for the phylogeny assuming that the phylogeny is generated by the steady state of some Markov process? (I think the answer is no: in that case, how does one explain the initial condition?)

      The tool we use to infer transition rates from phylogenies—BayesTraits—allows the initial state at the root of the tree to vary during the numerical optimisation (Pagel, 1994). Therefore, it is not assumed that the initial state is generated by the steady state of the Markov process.

      If I take the mutation model (random walk) seriously, then shouldn't I expect that this steady state obeys detailed balance? In that case I should have $p_i r_{i\to j} = p_j r_{j\to i}$ for each of the occupancies $\{ p_i\}$ and transition rates $r_{i\to j}$ for the shape categories. How close are the rates inferred from the phylogenies to obeying detailed balance? Presumably, the Markov chain fitted to the simulation data obeys detailed balance because the mutation model itself does?

      BayesTraits allows off-diagonal transition rates of the rate matrix to vary freely during numerical optimisation (Pagel, 1994). Therefore, there is no requirement for detailed balance to hold for the inferred rate matrix. For our simulations, the mutations are symmetric at the parameter level, therefore at this level, the process would be expected to obey detailed balance. We investigated this further by calculating the posterior signed equilibrium flux difference $\pi_iq_{ij}-\pi_jq_{ji}$ for all inferred rate matrices (see new material in supplementary information Fig S23). The posterior signed equilibrium fluxes for each transition pair in the simulations have 95% credible intervals overlapping with 0, which is consistent with detailed balance. Some phylogenetic state pairs are inconsistent with detailed balance. This could be due to something other than symmetric neutral drift acting on these specific transitions, such as selection or mutation biases not captured by the model. However, the identity of the transition pairs that are inconsistent with detailed balance varies between phylogenies, indicating that these apparent violations could be noise due to phylogenetic uncertainty. In any case, a violation of detailed balance does not disprove a developmental bias explanation, it just suggests that the underlying process is more complex than the reversible evolutionary algorithm we use in our leaf-model simulations. However, introducing non-reversible mutation dynamics into our leaf-model simulations would require additional assumptions and parameters describing mutational asymmetries, which are not necessary to reproduce the key bias towards unlobed.

      I find it hard to take the discussion of development seriously without some consideration of mechanics. Presumably, the mechanics are hidden in the computational leaf development model, but this model is not discussed in enough detail for the reader to know. It seems to me that the interesting question is: what are the {\it mechanical} constraints on development that drive the apparent trend in evolution towards simpler leaf shapes? Maybe it is something about the type of differential growth needed to make complex leaf shapes less robust to mutation. But in this case, I would assume that selection plays a role in the complexity of shape. In any case, a better understanding (or explanation) of the computational model is needed to make this interpretation.

      We thank the referee for the suggestion to make the paper more accessible. We have added a new, more detailed and pedagogical description of the model from (Runions, Tsiantis and Prusinkiewicz, 2017) in the supplementary information section S1.A “Leaf model details". We also note that Fig. 5 in the methods gives an overview of how the model works, including some mechanical aspects of development and growth.

      More generally, mechanics is one component of the developmental map that determines which parameter combinations produce viable leaf morphologies. Our analysis concerns the geometry of this complete developmental map, irrespective of whether its constraints arise from gene regulation, tissue mechanics, or their interaction.

      On the interesting question of what is causal, perhaps the example in figure 2 is helpful. We focus on two parameters, a morphogen repression strength, and a duration of growth. A key physical process here is called webbing, where cellular growth fills in the gaps between branching veins. This process flattens the leaf structure and creates a continuous, solid leaf blade (lamina). Strong webbing, characterized by a significant resistance to stretching and bending, results in a smoother margin (Runions, Tsiantis and Prusinkiewicz, 2017). The morphogen repression strength affects the physical parameters that determine how strong the webbing is. The duration of growth determines how long the leaf has to grow. If an unlobed leaf has some marginal patterning that results in small protrusions, such as serrations, increasing the duration of growth will amplify these protrusions, eventually forming lobes. Similarly, increasing the strength of morphogens that repress growth along the margin will deepen the sinuses between protrusions, resulting in lobes. Combinations can result in highly dissected and compound leaves, as illustrated in figure 2. Conversely, decreasing either or both will result in a smoother margin and eventually leaves with an unlobed shape. Thus, varying these two developmental parameters varies the physical processes that determine leaf shape. The mechanics of growth operate downstream of these parameters that we vary in our evolutionary simulations according to the details of the leaf developmental model.

      Some discussion of timescales is needed, especially when invoking neutral evolutionary arguments. If a neutral mutation occurs, its time to fix in a population of size $N$ is $\sim N$ generations. What are the relevant angiosperm population sizes and the number of mutations that separate branches on the tree? Are timescales remotely consistent with e.g., the age of angiosperms on Earth?

      Neutral processes have a well-established role in key aspects of angiosperm evolution, for example genome complexity (Lynch and Conery, 2003). This would suggest that the relevant timescales and generation times are not completely prohibitive of neutral processes also playing a role in the evolution of angiosperm leaf shape. Effective population sizes in plants are highly variable but estimates span 10^3-10^6. Assuming diploidy (and therefore average fixation time of 4Ne) and generation times of 1-10 years, this gives fixation timescales of 10^3-10^7 years. This is within the timescales of the trees we analyse, which span >150 million years.

      Reviewer #2 (Public review):

      Strengths:

      The paper's underlying question is interesting, extending the authors' prior work on RNA along similar conceptual lines. The paper combines both image analysis of leaves and a computational analysis of a simple model of leaf development.

      Weaknesses:

      The entire paper is based on the Runion model. More intuition about the Runion model would be useful for a broader readership that cares about the evolutionary aspect of this, but may not know the developmental model in question. Obviously, this is prior well-established work, but 2 - 3 sentences highlighting the key structural aspects of such a model would be great.

      Currently, that intuition is found implicitly in a sentence on page 2 ("complex leaf shapes need more specificity in their GRNs than their simpler unlobed leaf shape"), but the reader is left wondering - is the Runion model a detailed mechanistic one with multiple interacting genes/proteins? If so, how many? Or is it just 2 - 3 genes but with complexity entirely in how long they are each expressed/when they are turned off, etc.

      We thank the referee for the suggestion to make the paper more useful for a broader readership. To that end, we have added a more detailed description of the (Runions, Tsiantis and Prusinkiewicz, 2017) model in supplementary information section S1.A "Leaf model details".

      The Runions model has nearly 100 free parameters. Random walks in 100dimensional spaces have generic properties like a tendency to move toward regions of larger volume that have nothing to do with leaf biology. How do you disentangle the geometry of high-dimensional random walks from genuinely biological developmental bias? Would a toy model with 100 parameters and arbitrary phenotype categories also show "bias toward simplicity" if "simple" phenotypes occupy more volume?

      Our argument is largely independent of the number of parameters. While it is true that most of the volume is near the surface in a high-dimensional space, our argument is about the relative volumes of the sets of parameters that map to each of the four phenotypes, an entropic argument if you wish. The basic intuition is that a simple phenotype needs fewer parameters to be fine-tuned, and so a larger volume of parameter space will map to a simpler phenotype.

      The question about a toy model with arbitrary phenotypes is helpful because it allows us to clarify that what we are illustrating here with the biologically realistic example of leaf shapes is a much more generic principle. We can say with confidence that if the toy model generates a many-to-one set of outputs (phenotypes) through an algorithmic process whose description length does not grow faster than logarithmically with the size of the genotype space, then it should produce a bias towards simplicity regardless of the number of dimensions, see for example Johnston et al. (2022) and Dingle, Camargo and Louis (2018) for a longer discussion of this more general point which is based on arguments from algorithmic information theory (AIT). We do not use that framing in the current paper because the basic intuition for GRNs, that more complex phenotypes need more parameters to be fine-tuned and so have relatively smaller volumes, is more straightforward to understand than the more abstract AIT arguments. Our general prediction that this principle should hold more widely for GRNs can be made both by the more formal AIT route, or via the more heuristic fine-tuned parameter route.

      It is also true that random walks can have biases towards regions of parameter space with high robustness (Van Nimwegen et al., 1999). For our model, this would mean a bias towards valid leaves, however we have no reason to expect this would bias the rates between different valid leaf shapes. We address this point in methods section C.

      The discussion of Figure 4 (PCA of parameter space) uses "area" loosely when what's actually being measured is bin count in a 2D projection of a highdimensional space. I would think that, in general, PCA projections can be misleading about volume in the full parameter space, but I can't tell if that's an issue in this case. Some comments/thoughts here would be useful.

      The quantitative estimate of phenotype frequencies is computed directly in the full parameter space and does not depend on PCA. We estimate that the total volume of viable leaves maps to simple unlobed leaves about 80% of the time. However, the volume is extremely high-dimensional, and so hard to visualise. PCA is used solely to provide an interpretable visualization of this otherwise high-dimensional structure. The PCA plots in Fig 4 and Fig S16 are there to be illustrative, not quantitative. Because the volume differences are large, we do not think that the projections of the main PCA components would be misleading on at least the ordering of the sizes of the parameter space components that map to each leaf shape. We provided a similar analysis for other projections -- PC1-PC6 (supplementary information section S3.B "PCA occupancy for higher dimensions"), finding the same trend. To make this point clearer, we have now changed the sentence in the Fig. 4 caption slightly “This (reveals that --> illustrates how) unlobed leaves occupy a larger region of model parameter space than more complex shapes and that this larger space also contains the majority of more complex leaves.”

      The classifier validation section is in the Methods section, but it seems critical to the whole story. The < 80% agreement with manual classification could propagate to the rest of the estimates in the paper. Again, some comments/thoughts here would be useful.

      The review raises a valid concern. In response, we have repeated the analysis of the agreement between by-eye and automatic morphometric classification and produced a confusion matrix for the two classification methods to make the uncertainty clearer (see supplementary information Fig S7, section S1.E). The confusion matrices show that the agreement between the by-eye and automatic morphometric methods is high for unlobed, dissected and compound. The main source of disagreement is leaves that were classified as lobed by eye being classified as either unlobed or dissected by the automatic morphometric method. The proportion of by-eye lobed leaves classified by the automatic-morphometric method as either unlobed (27%) or dissected (23%) is relatively balanced, which we think will cancel out some error as well. Moreover, we find that the agreement between the automatic-morphometric method and by-eye classification increases to 90.0% when using the categories unlobed and all other categories grouped into one (complex). This is the most important classification for our finding that development and phylogeny are both biased towards unlobed.

      The authors should explain Mut2 and Mut5 in the main paper with a sentence or two, at least schematically, because how you mutate is obviously very relevant to interpreting a paper about biases in variation.

      We agree that this information should be readily available in the main text. In response, we have added a sentence to the results section C for more detail on the random walk.

      "[We mutated the initial sample using a random walk algorithm with two different mutational schemes, MUT2 (alg. 1) and MUT5 (alg. S2).] These algorithms work by iterating through model parameters one by one and perturbing the value by a small amount. We then [automatically classified the resulting shapes...]"

      However, we note that in methods section C there is already a more detailed description of both algorithms.

      “MUT2 (alg. 1) iterates through the parameters in a random order, and attempts to change the parameter by a value selected at random from an array of numbers randomly generated at 3 different orders of magnitude. MUT5 (alg. S2) is the same as MUT2 except that each mutation is additionally scaled by 10% of the current parameter’s range within the initial leaves (fig. S6). The aim here was to provide some way of accounting for the biologically relevant sampling range."

      Moreover, the MUT2 algorithm is described in pseudocode in Algorithm 1 in the main text, and the pseudocode for MUT5 is in supplementary information section S1.C, as algorithm S2.

      The two mutational schemes use additive perturbations to individual parameters. Real mutations presumably affect regulatory networks in more structured ways (e.g., changing binding affinities that affect multiple parameters simultaneously). How sensitive are the results to the assumption of independent single-parameter mutations?

      The referee raises an interesting and well-known issue concerning this widely studied class of GRN models. Without a detailed understanding of how individual genetic mutations map onto model parameters, it is difficult to determine with confidence whether a mutation would produce correlated changes in certain sets of parameters. Our main argument, however, is that the primary source of the observed bias is geometric: the volume of parameter space (or equivalently, the entropy) corresponding to simple leaf morphologies is substantially larger than that corresponding to complex morphologies. As long as mutations explore parameter space approximately symmetrically, even if they involve correlated changes in multiple parameters, larger phenotype regions will tend to be encountered more frequently and retained for longer than smaller regions. We therefore expect the observed bias to be robust to many alternative mutation models, as is already supported by the agreement between our two mutational schemes, although quantifying this robustness is an interesting direction for future work.

      The connectedness argument is made using a 2D PCA projection. Is there a way to check this statement in the full parameter space or perhaps in higherdimensional projections to test the robustness of this result? Connected components can merge/split under different projections.

      We agree that the 2D projection alone is limited. We therefore performed a new analysis using the same method but in the full dimensional parameter space. The nearest neighbour graph for the full-dimensional data has the following numbers of connected components: unlobed-146, lobed-273, dissected-255, compound-315. This follows the same pattern identified for the PC1-PC2 projection, that unlobed splits into fewer connected components than other leaf shape categories. We have added this result to the caption in figure 9.

      References:

      Dingle, K., Camargo, C.Q. and Louis, A.A. (2018) ‘Input–output maps are strongly biased towards simple outputs’, Nature Communications, 9(1), p. 761. Available at: https://doi.org/10.1038/s41467-018-03101-6.

      Johnston, I.G. et al. (2022) ‘Symmetry and simplicity spontaneously emerge from the algorithmic nature of evolution’, Proceedings of the National Academy of Sciences, 119(11), p. e2113883119. Available at: https://doi.org/10.1073/pnas.2113883119.

      Lynch, M. and Conery, J.S. (2003) ‘The Origins of Genome Complexity’, Science, 302(5649), pp. 1401–1404. Available at: https://doi.org/10.1126/science.1089370.

      Pagel, M. (1994) ‘Detecting correlated evolution on phylogenies: a general method for the comparative analysis of discrete characters’, Proceedings of the Royal Society of London. Series B: Biological Sciences, 255(1342), pp. 37–45. Available at: https://doi.org/10.1098/rspb.1994.0006.

      Runions, A., Tsiantis, M. and Prusinkiewicz, P. (2017) ‘A common developmental program can produce diverse leaf shapes’, New Phytologist, 216(2), pp. 401–418. Available at: https://doi.org/10.1111/nph.14449.

      Van Nimwegen, E., Crutchfield, J.P. and Huynen, M. (1999) ‘Neutral evolution of mutational robustness’, Proceedings of the National Academy of Sciences, 96(17), pp. 9716–9720. Available at: https://doi.org/10.1073/pnas.96.17.9716.

    1. Author response:

      The following is the authors’ response to the previous reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      The authors collect extensive behavioral data and show that preference vary between animals and days, but little insight is provided into what underlies these changes and to what extent they reflect "preference". Two animals drank equal amounts of sucrose and quinine on day one of preference testing, suggesting that behavior does not reflect preference but (lack of) habituation to/proficiency with the testing environment.

      Rats underwent several days of habituation and were checked for lick proficiency before testing. A note regarding this fact has been added to the text, and to the fact that day one consumption of NaCl and water was high in the rat that did not lick much for sucrose, making it clear that the rat was proficiently licking for tastes that it wanted (lines 102-104). We have also added prose to the Discussion section about what lick data tells us about preferences (lines 360-371).

      Recordings were performed only after multiple days of preference testing, and preferences were not tested in between/following recording sessions. This design precludes a direct comparison between neural and behavioral responses.

      The proposed experiment is suggested as a future direction (lines 389-393); performing this experiment is currently impossible, as the experimenters involved have moved on.

      Similarly, correlations between neural responses and behavioral measures are not analyzed/reported on an animal-by-animal basis.

      Although this is an excellent idea, the limitations of the current dataset render the analysis impossible. This is now explained in the Discussion (389-393).

      Reviewer #3 (Public review):

      The authors state that "no differences in effects were observed between taste batteries" (Methods), but it is not clear which analyses were performed to determine this, especially considering that many of the analyses are within-animal. Without more clarity, it is difficult to evaluate whether the interaction of different tastes within the sets of stimuli bias the main conclusions.

      Alas, we are unable to address this concern, although the robustness of our results renders it unlikely that we are observing a phenomenon that is particularly sensitive to specifics of the taste battery.

      It is not clear how the analyses in Figure 3 emerge from the behavioral patterns across Figures 2A2 and 2B2. Along these lines, citric acid responses for R1 and R2 and saccharine responses for R7 and R8 are not shown in Figures 2A2 and 2B2, thus, we cannot determine if they change from the first to final BAT sessions. Salt, even at low concentrations, may not be palatable when rats are in a water-restricted state. It would be interesting to see Figure 3's analysis exclusively for sweet or for bitter tastes.

      We have clarified the text in the results (line 149), methods (lines 531-548), and figure legend (lines 639-644) to better explain Figure 3. The figure itself was updated such that each taste is now color coded, and an analysis looking exclusively at sweet or bitter tests has been run (and found nonsignificant; lines 157-158).

      A potential reason why a single taste experience session causes taste palatability responses in GC neurons to revert to a reflection of canonical palatability ranks, as is seemingly shown in Figure 6, is not discussed.

      This prose, which we apologize for failing to include previously, has been added to the Discussion section (lines 364-371).

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      The current study is a follow-up to a previously published study by the same research group (Nold et al. 2025). In the previous study, the authors had included a set of exploratory analyses which assessed the effects of fitness level (denominated by a relative FTP), sex, and drug treatment (Naxolone versus placebo). In this previous study, the authors state that "exploratory analysis showed a significant main effect of fitness level on differences in pain ratings in the [saline] condition... suggesting increased hypoalgesia with increasing fitness levels, pooled across all stimulus intensities".

      In the current study, the authors have recruited an additional 22 female participants (21 included in analysis) from local cycling clubs to assess if fitness level does indeed impact exercise-induced hypoalgesia responses to experimental thermal and pressure pain models.

      Strengths:

      The current study has the potential to present a convincing argument about the effect of fitness level and potentially other factors (e.g., sex) on exercise-induced hypoalgesia responses. Combining data across two of their primary studies would be highly fruitful to the research community interested in this area. Specifically, it has the potential to inform sports medicine practitioners and how they administer exercise protocols to help those experiencing pain with a further consideration for the fitness level (and maybe sex) of their patients.

      Weaknesses:

      However, the current study makes several bold claims about the role of fitness level and sex on exercise-induced hypoalgesia, which I do not believe that this study on its own - or in conjunction with the previously published study by the same authors - can make at present. Namely, the current study does not appear to conduct any specific analyses between the cohorts from either study (current and present). The results mention a difference in the group mean values in "fitness level" between cohorts, but the analysis itself on pain responses/exercise-induced hypoalgesia is limited only to the cohort from the current study. If the authors wanted to provide a convincing argument that fitness level has an effect on exercise-induced hypoalgesia, then the analysis of this study would have to include an analysis between the groups considered to be of "high" and "low" fitness level. I do not think the current study does this. Instead, it makes an assumption from the previous study (Nold et al. 2025) which only states that "exploratory analysis showed a significant main effect of fitness level on differences in pain ratings in the [saline] condition... suggesting increased hypoalgesia with increasing fitness levels, pooled across all stimulus intensities". The analysis of this study would have to include fitness level "high fitness" versus "low fitness" of participants across both studies in its statistical model to properly discern if fitness level has an impact on exercise-induced hypoalgesia.

      A similar comment can be made with respect to sex differences, as these have not been assessed in the analysis of this study either.

      Another area of weakness in this study is how "fitness level" has been demarcated across participants. One issue is how authors have assumed that the current cohort is 'fit', whereas the previous cohort was 'less fit', meaning that the authors could be coming to false conclusions about fitness level. In detail, figures within the current study show a large overlap between the 'fit' and 'less fit' cohorts, where some participants have a higher relative functional threshold power (FTP) in the 'less fit' cohort than the 'fit' cohort and vice versa. Therefore, I believe the authors should better demarcate between those that are in the 'more fit' and 'less fit' groups according to a validated and well-established criterion from the kinesiology and sport science literature. That being said, I think this may be problematic in some ways as FTP is considered a relatively poor measure to denote fitness levels, a limitation highlighted in the previous study's review.

      Altogether, whilst I commend the researchers on their body of work across the two studies, the current methods and analysis provide an incomplete assessment of their primary research question, and therefore, I would urge the authors to reconsider some of their methods/analysis and the framing of their results to better reflect the main research question they have attempted to answer. Likewise, I would recommend that readers ensure they consider the current results with caution until the authors have addressed some areas of concern which currently limit their main conclusions.

      We sincerely thank the reviewer for their thorough and insightful comments and for the time invested in reviewing our work. In response, we have made several important revisions, particularly to address the major concerns regarding fitness level and sex differences.

      Specifically, we have:

      (1) Conducted additional pooled analyses to directly evaluate fitness and sex effects.

      We pooled the data from the previous and current studies and conducted linear mixed-effects models investigating the effect of exercise intensity between the subgroups, as well as specifically testing the effect of fitness level and sex across the pooled data. This allowed us to directly test the effects of fitness level and sex on a common scale rather than infer these effects from separate cohorts. To quantify evidence both for and against the presence of exercise-induced pain modulation and its moderation by fitness, sex, and study sample, we estimated Bayes factors comparing nested models of increasing complexity. In addition, we examined the posterior distributions of the regression coefficients (β) and subgroup- specific (males from previous study, females from previous study, females from current study) exercise effects to estimate the magnitude and uncertainty of these effects. The Bayesian analyses provided some evidence that fitness level moderated exercise-induced pain modulation, but sex did not. Importantly, these findings were consistent with the overall pattern of results obtained in the frequentist analyses. All corresponding statistics in the main manuscript and Supplementary Materials have been updated accordingly. To improve transparency, the pooled analyses are now presented in the dedicated Results subsections and accompanied by new figures (Figures 4 and 5). Furthermore, we have adapted the Title, Discussion and Conclusion to more closely reflect the results.

      (2) Clarified the assessment of fitness level.

      We expanded our consideration of fitness level and training status by discussing training volume as an additional indicator of training status. We also acknowledge that fitness is a continuous construct and that some overlap in FTP values exists between cohorts. To address this concern, we conducted pooled analyses using FTP as a continuous predictor rather than relying solely on cohort membership. For consistency and comparability with the previous study, FTP remained our primary indicator of fitness level, while analyses using training volume are now reported in the Supplementary Materials.

      (3) Expanded the mechanistic background on the effect of fitness level and sex on EIH.

      We expanded the mechanistic background in both the Introduction and Discussion to provide a clearer theoretical rationale for how fitness level and sex may influence exercise-induced hypoalgesia (EIH), drawing on relevant experimental and clinical literature.

      Reviewer #2 (Public review):

      This study addresses an important question regarding exercise-induced modulation of pain in women, but the conclusions appear to be based on relatively limited and selective evidence. The authors report an interaction between exercise intensity and stimulus intensity, which they interpret as evidence for exercise-induced hypoalgesia and conclude that fitness, but not sex, modulates this effect. However, this main result relies on a relatively small interaction that emerges only under specific conditions, with inconsistent findings across pain modalities and stimulus intensities, and an analysis approach that does not fully exploit the continuous pain ratings collected. The lack of a baseline condition further limits the interpretability of the findings as reflecting hypoalgesia, and overall, the data provide a rather constrained basis for drawing broader conclusions.

      Strengths:

      (1) The focus on women is important and timely, particularly given the ambiguity in prior findings and the historical bias toward male-dominated samples.

      (2) The attempt to revisit previous findings in a new cohort is valuable in principle.

      Weaknesses:

      (1) The core interpretation may not be fully supported by the data

      The central claim-that the results demonstrate exercise-induced hypoalgesia and its dependence on fitness but not sex-does not appear to be fully supported by the evidence presented.

      (1.1) Lack of baseline condition

      The absence of a no-exercise baseline substantially limits interpretation. The study compares high- and low-intensity exercise, but without a baseline, it is not possible to determine whether either condition produces hypoalgesia or hyperalgesia relative to calibration. The observed HI-LI difference, therefore, reflects only a relative contrast between exercise intensities, not an absolute reduction in pain. As a result, attributing the findings to "hypoalgesia" may be difficult to justify fully.

      (1.2) Lack of internal replication across conditions

      The reported effect is highly specific and does not clearly generalise across the experimental design. It emerges significantly only for heat pain at the highest stimulus intensity, with no clear effects for other intensities and for pressure pain. Moreover, the main statistical result is a relatively small interaction effect with a modest p value, which translates into a difference of approximately 6-8 VAS units on a 150 scale. This combination-a small effect size, limited statistical strength, and restriction to a single condition-substantially weakens the evidence for a robust or generalisable effect.

      (1.3) Deviations from the original study and selective use of data

      Although framed as a follow-up to previous work, the current study introduces substantial methodological changes, particularly in the acquisition and scaling of pain ratings (continuous vs post-hoc ratings, modified VAS with sub-threshold range). Despite collecting rich continuous data, the analysis focuses on peak responses to approximate the previous study. While this may aid comparability, it results in a strong emphasis on a single data point (highest intensity), rather than leveraging the full dataset. This limits both interpretability and comparability.

      (1.4) Over-reliance on null results regarding sex differences

      The conclusion that fitness, but not sex, modulates exercise-induced pain may not be directly supported by the data presented. The current study includes only highly fit women, and comparisons with men or less-fit women rely on non-significant differences in a previous cohort. The absence of a significant difference does not provide evidence for equivalence, and no formal statistical support for a null effect is provided. As such, conclusions about the absence of sex differences would unfortunately benefit from more cautious interpretation.

      (2) Limited sample and lack of diversity

      The dataset is narrow in scope, comprising a small sample (N = 21) of healthy, highly fit women. Key demographic characteristics (e.g. age range, BMI distribution) are not fully presented, explored or discussed. This limits generalisability and makes it difficult to draw broader conclusions about exercise-induced pain modulation in women, as the main focus of the study.

      (3) Methodological choices limit the interpretability of the data

      Several methodological decisions would benefit from stronger justification:

      (3.1) The use of a non-standard VAS scale (0-150 with a fixed pain threshold at 50) is unconventional and may influence how participants report pain, while limiting comparability with related literature.

      (3.2) Participants explicitly reported expecting exercise to reduce pain, introducing a potential confound that is not presently addressed.

      (3.3) A more comprehensive use of the full time series of pain ratings would provide a stronger and more transparent basis for interpretation of the present findings.

      We sincerely thank the reviewer for their time and effort invested in reviewing our manuscript and appreciate the comments. In response to the points raised by the reviewer, we have now updated our work. Specifically, we have:

      (1) Pooled samples and strengthened inferential framework:

      We pooled the current and previous datasets to provide a stronger basis for the primary interpretation of the findings. On this combined dataset, we conducted both frequentist linear mixed-effects models and complementary Bayesian analyses, allowing us to directly test effects of fitness level, sex, and exercise intensity within a unified framework and to quantify both effect sizes and evidence for/against key hypotheses. The Title, Results, Methods and Discussion have been adapted to more closely reflect the results.

      (2) Addressed sample limitations through pooled analysis:

      To mitigate limitations related to sample size and composition in the individual studies, we extended all primary inferential analyses to the pooled dataset. This approach increases statistical power, improves the stability of estimates, and enables a more reliable examination of between-group effects across fitness level and sex, thereby strengthening the generalisability of the findings.

      (3) Expanded analyses of continuous pain ratings:

      To address methodological concerns regarding the use of a summary pain metric, we supplemented the primary peak-based analyses with additional linear mixed-effects models on the full time-series data. Specifically, we modelled time × exercise intensity interactions for both heat and pressure pain, thereby capturing the dynamic structure of pain responses and ensuring that conclusions are supported by the richness of the continuous rating data. These analyses have been added to the Supplementary Materials.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      Synopsis

      The current study is a follow-up to a previously published study by the same research group (Nold et al. 2025). In the previous study, the authors had included a set of exploratory analyses which assessed the effects of fitness level (denominated by a relative FTP), sex, and drug treatment (Naxolone versus placebo).

      In the current study, the authors have recruited an additional 22 female participants (21 included in analysis) from local cycling clubs to assess if fitness level impacts exercise-induced hypoalgesia responses to experimental thermal and pressure pain models.

      All the analysis of this study seems to be specific to the "fit" cohort from this study. No analysis or figures seem to show differences between cohorts from the current and previous studies. For this study, the authors found that maximum pain ratings after application of a thermal stimulus and pressure pain stimulus were lower after a high-intensity exercise compared to a lower-intensity exercise. There was also an exercise intensity × stimulus intensity interaction when thermal stimulations were applied, suggesting that the exercise-induced hypoalgesia response varies across exercise intensities as the stimulus intensity increases/decreases. The same cannot be said for pressure pain according the statistical analysis outputs of this study, although inspection of Figure 3B (top row) does illustrate that at higher stimulus intensities, there is a difference between exercise intensities for maximal pain ratings, whereas there is no difference at lower stimulus intensities (30 and 50 VAS). However, observing the changes in maximum pain ratings (Figure 3C) does show similar changes across all stimulus intensities for pressure pain, unlike thermal pain. Therefore, the authors claim that there is an effect of fitness level on the exercise-induced hypoalgesia response.

      Overall, the authors have completed a neat supplementary study to their previous study. However, there are several areas that I believe should be addressed within the current manuscript.

      First, the authors regularly state "...the hypoalgesic response to exercise depends on fitness level but not on sex". As mentioned earlier, the results section of the previous study states that "exploratory analysis showed a significant main effect of fitness level on differences in pain ratings in the [saline] condition... suggesting increased hypoalgesia with increasing fitness levels, pooled across all stimulus intensities". In this study, the authors do not seem to have completed a direct comparison between the two study cohorts. The results for the current study only seem to discuss the effects of exercise intensity within this study cohort. If this study is to be treated as a stand-alone study, then the data that is presented should make it clear that the effect of fitness level is being assessed. Currently, the results and the figures only illustrate the effects of exercise intensity and stimulus intensity, not fitness level (or sex), which are mentioned in the title, abstract, and most discussions.

      Second, on the topic of sex-related effects, as authors repeatedly state ""...the hypoalgesic response to exercise depends on fitness level but not on sex", I think it is worth noting that this statement would require an a priori assessment of sex differences on exercise-induced hypoalgesia responses. As the previous study (exploratory) and this study (no sex difference analysis) do not include this a priori assessment, I do not think they can conclude that sex is not a factor in the exercise-induced hypoalgesia response, though they can surmise that fitness level may have an influencing role if it was specifically tested in this study. If the authors wish to judge the role of sex, there ought to analysis on this specifically.

      Third, whilst the authors have tested the effects of "fitness level", I urge the authors to consider how they have demarcated between fitness levels in this study and any other (validated) criterion that could be used in place of their current method to distinguish between "fit" and "less fit" participants. To explain the cohort of the current study is judged to be "fitter" than the previous study based on the group mean relative FTP. Yet, observing Figure 1, there are several participants with lower relative FTP in the "fit" cohort than the "less fit" cohort, and vice versa. I would recommend the authors to consult with some kinesiologists/sport scientists about this issue. As the central topic of this study is the effect of fitness level, this warrants careful consideration, as the current method to split the groups is problematic, especially as there is clear overlap between the two groups in the metric that the authors have used (relative FTP).

      Fourth, I think it would be highly beneficial for the authors to add more discussion around the theoretical and mechanistic accounts about why fitness level (and sex) would impact exerciseinduced hypoalgesia responses. The current manuscript provides a nice account of the current literature in terms of the direction of each study's results, yet they do not explore why fitness level or sex has such effects. This would be highly valuable to a reader to set the tone of the study rationale in the introduction and provide more depth to the authors' discussion of their results.

      Below I have highlighted all my comments that have been separated into MAJOR and MINOR comment sections.

      I hope my comments are of use to the authors, and I would like to thank them and the journal for the opportunity to review their paper on a truly interesting and insightful topic.

      We thank the reviewer for their insightful comments and appreciate the time invested in reviewing our work. In the following, we have addressed all comments raised by the reviewer and marked all changes in the manuscript.

      Major Comments

      (1) In my opinion, it would enhance the manuscript if the authors provided a theoretical or mechanistic account of why fitness levels or sex would impact the exercise-related hypoalgesia effects. Though some reasoning about the mechanisms of fitness level and sex is mentioned in the discussion of the previous study (Nold et al. 2025), and even if the overall research findings are mixed at present, I do not think it would be overkill to provide the rationale for why the authors do/do not predict a certain response in the current study after their analyses. On this note, the authors may argue that the manuscript content from L52-61 is an account of the previous literature. However, whilst this literature sets out the directions of previous research findings, as I read this, I do not think there is a theoretical framework to underpin why fitness level or sex would impact exercise-induced hypoalgesia (EIH). References already included in the manuscript should have some discussions around this (e.g., Sluka et al. 2018; Koltyn 2000; Koltyn et al. 2014).

      We thank the reviewer for their comment. We agree that the mechanistic rationale for why fitness level and sex may influence EIH could be described in more detail. Accordingly, we have expanded the Introduction/Discussion to provide a more comprehensive overview of the potential mechanisms underlying these effects, drawing on previous EIH literature (e.g., Sluka et al., 2018; Koltyn, 2000; Koltyn et al., 2014) as well as evidence relating to changes in endogenous modulatory systems due to repeated exercise (Anderson & Shivakumar, 2013; Gajic et al., 2026; Matei et al., 2023; Saanijoki et al., 2022; Song et al., 2022) as well as sex differences in these neuromodulatory systems potentially contributing to sex differences in EIH (Blanton et al., 2021; Castelli et al., 2014; Fullerton et al., 2018; Levine et al., 2021; Loyd et al., 2008; Zubieta et al., 2002).

      (2) The study sets out an aim, but I do not see any (a priori) hypotheses in the intro or methods. If no hypotheses were registered, this can be reported in the discussion and factored into the discussion about why certain results would/would not be expected.

      The reviewer is correct that no formal, pre-registered hypotheses were specified for this study. As this study was designed as a follow-up to our previous study, which reported no exercise-induced pain modulation in relatively less fit females, the present investigation was primarily exploratory in nature and aimed to examine whether exercise-induced pain modulations would be observed in a sample of females with significantly higher fitness levels. We have now clarified this in the discussion and acknowledge the exploratory nature of the study when interpreting the findings.

      (3) Is there a sample size justification, sensitivity analysis, or post-hoc calculation for the additional 21 participants to detect effects for fitness level and sex?

      We thank the reviewer for this question. No formal a priori sample size calculation was performed for the recruitment of the additional 21 participants. The current study was designed as a follow-up to our previous work, in which female participants were, on average, slightly less fit than male participants. To better disentangle the effects of fitness and sex, we therefore aimed to recruit a comparable number of female participants with higher fitness levels. Accordingly, we targeted a sample size similar to that of the female subgroup in the previous study.

      (4) I have a wider question about where there has truly been a test between fitness levels.

      Definition and measurement of "fitness level".

      Is there an appropriate rationale that relative FTP is an appropriate measure to distinguish between fitness levels? Understandably, this is done for consistency between the two studies, and there may be mention of the use of the FTP measure in the original study; however, it would be worth justifying the use of the relative FTP measure to categorise fitness level with previous literature to back this up.

      We thank the reviewer for this very valid and important point regarding both the validity of FTP as a proxy for fitness and the distinction between fitness levels. Previous research has shown that the FTP and FTP20 tests are reliable and convenient methods to estimate approximate measures of VO2max (Denham et al., 2020) and that the FTP test is a useful test for performance prediction in moderately trained cyclists (Sørensen et al., 2019). Furthermore, we argue that FTP represents a continuous performance measure in our studies instead of a categorical variable distinguishing between fit and unfit individuals, and we have strengthened the manuscript by providing a clearer justification for its use as a field-based proxy of endurance fitness, supported by previous literature linking FTP to more direct physiological markers such as VO<sub>2max</sub> (Denham et al., 2020). Since we have used FTP in the previous sample as a measure of fitness level, we maintained this for consistency in the current study.

      We also acknowledge that, despite statistically significant group differences, there is meaningful overlap between the males of the previous study and the females of the current study and that “fitness level” should be interpreted as a continuum rather than a strict categorical separation. Accordingly, the labels “fit” and “unfit” should be interpreted relative to the samples included in the current and previous studies rather than as absolute classifications. To reflect this more accurately, we have revised the manuscript to refer to participants as having higher or lower fitness levels, which should be interpreted within the context of the pooled sample rather than as discrete fitness categories.

      Classification of fitness level.

      In L110-111 - The statistical analysis does show a difference between groups, but Figure 1A does show that there is a crossover with around half the sample from each study cohort. That is, the current study had ~16 participants who had a lower relative FTP than the highest relative FTP from the previous study. When removing the highest participant (outlier) in the previous study, there are still 7 participants (a third of the sample) with a lower relative FTP than participants considered of a 'lower' fitness level than the previous study.

      Essentially, on the group level, there is a statistical difference in relative FTP, but there is notable overlap between the two groups.

      We thank the reviewer for this observation. Our aim was not to create entirely non-overlapping fitness categories, but rather to recruit a female sample with significantly higher average fitness levels than the females included in the previous study. As shown in the revised manuscript, females from the current study had, on average, significantly higher relative FTP values than females from the previous study, whereas no significant difference was observed between females from the current study and males from the previous study. We also report training volume as an additional indicator of training status; however, because training volume was self-reported, we consider FTP to provide a more objective and sensitive measure of fitness. The partial overlap in FTP values between samples is not unexpected and, in fact, facilitates comparisons across studies by ensuring that the samples are not entirely distinct populations.

      Could another distinction be made based on:

      - A set value (e.g., 2.0 W/kg-1);

      - Another value from previous literature, and the analysis be re-run with this classification of participants? The approach to use a set value is consistent with kinesiology literature that uses set values to demarcate fitness level for other more common, measures like VO2max (see ACSM guidelines and de Pauw et al. 2013);

      - Or by dissociating between training volume and slightly tweaking the wording to "training status/volume" (although I am cognisant that this would introduce an incongruence in terminology between the authors' studies, but other studies that have been referenced [e.g., Geva and Defrin, do specifically test between training volume]).

      We thank the reviewer for their suggestions. We would like to refrain from making another distinction based on a set value and dividing the group into “fit” and “unfit” individuals. Instead, we have pooled the samples and treated FTP as a continuous variable, which preserves statistical power and avoids the loss of information associated with dichotomising a continuous measure.

      To address the reviewers' suggestion of including training volume as a measure of fitness level, we have repeated our new analyses, namely the LMER model using training volume as a predictor for difference pain ratings (LI – HI Exercise pain ratings), in the pooled sample. These analyses yielded no significant effects for training volume, the interaction of training volume x sex, or training volume x subgroup in either heat or pressure pain. Furthermore, the training volume is potentially influenced by outliers in the current study sample. For completeness, we have added these analyses and according visualisation to the Supplements (Fig. S6).

      We believe that the FTP provides a more sensitive and objective measure of cardiovascular fitness level in our study, as it is not susceptible to recall bias, differences in training intensity and differences in training efficacy. We also note that other studies (Geva & Defrin, 2013) did not rely solely on self-reported training volume as a measure of fitness level, but recruited participants based on training history and athletic status (e.g. competitive triathletes vs. active controls).

      For these reasons, we consider the FTP the most appropriate primary indicator of fitness level in the current (and previous) study, while still reporting training volume in the main manuscript to consider.

      The above suggestions would also allow to select matched pairs from the male cohort when comparing effects between sexes. Altogether, though, I believe this comment to be the most important in my review of this paper, as the primary question depends strongly on how fitness level is defined and categorised by the researchers, and this requires careful consideration and validation from previous literature if such decisive conclusions are to be drawn from the results. Therefore, a clearer description of the reason why certain effects are expected (theory/mechanisms) and how participants have been categorised will be highly valuable for readers. It may be useful for the authors to reach out to kinesiologists/sport scientists within their peer groups to help with this comment.

      To further address the concern regarding between-cohort comparability, we have now pooled the samples from the previous and current study and re-analysed the data fitness level as a continuous variable rather than relying on cohort-based comparisons. Specifically, we conducted regression analyses examining fitness level, sex, and their interaction, as well as subgroup analyses including males from the previous study, females from the previous study, and females from the current study. These analyses were complemented by Bayesian model comparison and posterior inference. The results are now reported in the Results section. We also acknowledge that fitness is best viewed as a continuum rather than a discrete characteristic and have revised the manuscript accordingly, replacing references to “fit” and “unfit” participants with descriptions of relatively higher and lower fitness levels within the pooled sample.

      Finally, as mentioned in the previous comment (major comment #1), we have expanded the Introduction and Discussion to more clearly outline the mechanistic and theoretical rationale for expecting effects of fitness level and sex on exercise-induced pain modulation, drawing on relevant literature (see major comment #1). We believe these additions substantially strengthen both the conceptual justification and the analytical robustness of the manuscript.

      (5) The abstract states that "...further investigation to determine if and to what extent exercise induced hypoalgesia depends on fitness level and/or sex." However, I cannot see any analysis relating to sex in the results of this study that takes the female sample of this study and the male sample of the previous study and then carries out another LNER model? I also see no report of results about sex in any of the figures/tables. If sex is part of the abstract and main research question, then I would argue it ought to be in the results and feature in figures within the main manuscript, not supplementary material.

      We agree with the reviewer that, given the emphasis on fitness and sex in the Abstract and research aims, analyses directly examining sex effects should be presented in the main manuscript. In response, we pooled the samples from the previous and current studies and repeated the linear mixed-effects regression analyses used in the previous study to examine the effects of fitness and sex on exercise-induced pain modulation. We further complemented these analyses with Bayesian model comparison and parameter estimation to assess the moderating effects of fitness level and sex in the pooled dataset. The results of these pooled analyses are now reported in the corresponding Results section and are presented in the main manuscript as Figure 5. The Abstract, Results, Discussion, and Conclusions have been revised accordingly.

      (6) The current abstract and main manuscript make it seem that this study completed an additional analysis on the effect of sex, but this does not appear to be the case. Statements like "together with our previous findings, this suggests that exercise-induced hypoalgesia depends on fitness level but not on sex" are quite decisive, although it does not seem that any analysis was completed between sexes in an a priori fashion. The only data I can see that assesses between sex effects is an exploratory analysis from the previous study, which was part of a larger exploration of sex - fitness level - and drug interactions.

      Therefore could the authors either:

      - Run this analysis between sexes;

      - Or make it explicit that this study did not conduct any specific a priori analysis on sex differences in EIH at high and low intensities.

      - And/or temper how decisive their conclusions on the (null) effects for sex, unless there are statistical analyses to support this.

      We thank the reviewer for this suggestion. We agree that the manuscript did not include a dedicated analysis of sex effects in the combined dataset. In response, we pooled the samples from the previous and current studies and conducted additional frequentist (LMER) and Bayesian (Bayes Factor and posterior distributions) analyses examining the effects of fitness and sex on exercise-induced pain modulation. The frequentist analyses indicated an association between fitness and EIH, but not sex, while the Bayesian analyses similarly provided little evidence for sex-dependent effects. These new analyses have been added to the manuscript, and the Abstract, Results, Discussion, and Conclusions have been revised accordingly.

      Section-specific Comments:

      (1) Abstract

      L38-40: See major comment #6 above.

      As described above, we have now conducted additional analyses on the moderating effect of fitness level and sex using frequentist and Bayesian analyses and adapted the Abstract accordingly.

      (2) Introduction

      L68 - What is meant by "robust" in this sentence? Robust to describe the direction and magnitude of the differences in effects between sexes seems a little misrepresentative.

      We thank the reviewer for their comment and agree that the wording is vague. To emphasise clarity, we have rephrased this to “[…] whereas others (Koltyn, 2000; Sternberg et al., 2001; Vaegter et al., 2014) suggest that hypoalgesia following exercise is more pronounced in females, but overall results remain inconclusive (Rice et al., 2019).”

      (3) Results

      L124 - What is the online rating scale? It is the word "online" in particular that is confusing here, as it is described in the methods, but just seems to be a standard handheld device with a cursor.

      We thank the reviewer for their comment. In this case, “online” refers to the continuous ratings whilst the stimulus is ongoing, using a handheld rating device and using button presses. We clarified this further at the beginning of the Results and Methods sections to include “real-time (continuous) pain ratings” to avoid confusion.

      L136 - I think there is a missing word here before the set of parentheses. RPE?

      We thank the reviewer for detecting this and have added “RPE” before the parentheses.

      L136-138 - I would amend to read something like... "This confirms the exercise intensity protocols elicited a different output, relative power, physiological demand (HR), and perceived demand (RPE)", just to be clear on what the differences have been physiologically and psychologically for the participants when exercising at the two intensities.

      We agree with the reviewer and have rephrased the sentence according to their suggestion for clarity.

      (4) Discussion

      L190 - "results suggest that fit females show a hypoalgesic response to HI compared to LI exercise". I think there is a word missing in this sentence to make it clear what the results are.

      We have revised the sentence in accordance with the new (pooled) analysis results.

      L250-253 - The authors have given a fantastic account of the previous literature and the trends that each study has observed. However, in line with major comment #1, could the authors include some discussion to speculate why there are expected differences between training level/fitness level and sex (plus interactions)? Some studies that are referenced are theoretical papers, and even if the current literature is unsure about the likely mechanisms behind fitness and sex differences in EIH responses, stating this would also be useful to a reader but the authors could signpost them to specific references that would broaden their understanding after reading this study.

      We have now provided a more detailed account of the potential mechanistic background on why fitness level and/or sex could influence exercise-induced modulation in the Discussion (see major comment #1).

      (5) Limitations

      L258-259 - If I have understood this sentence correctly and the content in L301-304, the heat stimulus (temperature of the thermal probe) that was applied to induce a 30 VAS pain intensity rating at rest actually induced no pain at all, as 30 VAS is considered below the pain threshold of "minimally painful". In retrospect, this seems like an odd choice of measurement.

      It means that 30 VAS is simply a measure of warm (non-painful but detecting heat) and perturbation to the skin (pressure but not hurting) in the heat and pressure pain conditions, respectively. Therefore, to include the 30 VAS values in the analysis to dissociate whether HIGH or LIGHT intensities, fitness level, or sex have an impact on EIH seems misplaced, as there is no actual pain for which a hypoalgesia response can be tested at this intensity.

      Making this clearer in the results or discussion would be worthwhile for the readers, in my opinion.

      We thank the reviewer for highlighting this. In both the previous and current studies, participants were calibrated using the same procedure and rating scale (0 – 100) to identify painful stimulus intensities corresponding to VAS 30, 50, and 70. On the main experimental day, participants in the current study rated on a modified scale ranging from 0 to 150, with 50 marking the pain threshold, such that ratings below 50 reflected a non-painful rating. Importantly, the calibrated VAS 30, 50, and 70 stimuli refer to the target pain intensities established during the calibration procedure and not to the numerical values displayed on the experimental rating scale. Participants were familiarised with the scale and anchor points prior to testing and viewed only the visual analogue scale rather than numerical values during the experiment. We have adapted the wording, referring to VAS 30, 50, and 70 as intensities and not numerical ratings.

      (6) Conclusion

      L276-277 - Similar mention as before, can the authors please make it clear if there is a sex effect in their analyses or how this has properly been tested in a prior study through an a priori assessment to be certain that "fitness level rather than sex plays a central role in modulating EIH".

      We have now tested the effect of sex in frequentist and Bayesian analyses in the pooled samples and revised the conclusion in accordance with the results.

      (7) Methods

      L284 - What denotes an individual being "physically active"?

      We thank the reviewer for this question. “Physically active” was defined based on training volume, operationalised as regular participation in structured cycling training sessions (i.e., consistent engagement in planned cycling training units per week). This criterion was used to ensure that participants had an established and ongoing training routine relevant to the study context. We have clarified this in the referenced section.

      Table 1 - Female participants in the current study are noticeably older than the other cohorts from the previous study. While all are considered "young" (<40 y.o.), if one were to take a matched pair of females from each cohort (previous vs current) in terms of relative FTP, then the years of experience and exposure to training are likely a strong influence on EIH responses, not "fitness level" as it is described in this study. Just a speculative thought.

      The reviewer raises an interesting point. However, since we have not acquired any information on the years of training and volume, we are unable to answer this question in the current framework. Future research should investigate the effect of training years (which potentially strongly correlates with fitness level) on exercise-induced pain modulation.

      L313-315 - For future reference, there are some nice papers on how to administer the RPE scales with clear instructions to be certain that perceived effort is being measured appropriately (Halperin & Emanuel 2020; Halperin & Visgotsky 2025; Malleron et al. 2023). I always have a habit of signposting to these studies with regard to RPE because it can often be misrepresented in many different areas of research where RPE scales are used.

      We thank the reviewer for this suggestion and for highlighting these relevant papers. In the present study, participants were extensively familiarised with the rating of perceived exertion scale, and the instructions closely followed the original definition and recommendations provided by Borg (1998). The scale was presented in accordance with its intended anchor points to promote accurate reporting of perceived exertion. We have now added a citation (Borg, 1998) in the Methods section to clarify this procedure.

      (8) Code Availability

      Thank you for including open source code in your submission. I am very appreciative of researchers who champion open research principles.

      We appreciate the reviewer’s comment and support of open research practices. We have updated the code containing the updated analyses and datasets.

      Reviewer #2 (Recommendations for the authors):

      (1) Core interpretation may not be fully supported by the data

      We thank the reviewer for this comment. To investigate the role of fitness level and sex in exercise-induced pain modulation, we have now pooled the samples from the previous and current study and conducted frequentist (linear mixed effects models) analyses. Specifically, we tested for the effect of exercise intensity between the subgroups, as well as (consistent with those conducted in the previous study (Nold et al., 2026) testing the effect of fitness level and sex across the pooled data. This allowed us to directly test the effects of fitness level and sex on a common scale rather than infer these effects from separate cohorts. Furthermore, we conducted Bayesian analyses to quantify evidence both for and against the presence of exercise-induced pain modulation and its moderation by fitness, sex, and study sample, utilising the Bayes factors comparing nested models of increasing complexity. In addition, we examined the posterior distributions of the regression coefficients (β) and subgroup-specific exercise effects to estimate the magnitude and uncertainty of these effects. The Bayesian analyses provided some evidence that fitness level moderated exercise-induced pain modulation, but sex did not. Importantly, these findings were consistent with the overall pattern of results obtained in the frequentist analyses. All corresponding statistics in the main manuscript and Supplementary Materials have been updated accordingly. To improve clarity, the pooled analyses are now presented in dedicated Result subsections and accompanied by new figures (Fig. 4 and Fig. 5).

      (1.1) Lack of baseline condition

      We thank the reviewer for this important comment. We agree that, in the absence of a no-exercise control condition, our design does not allow us to determine whether either exercise condition produced hypoalgesia or hyperalgesia relative to no exercise. Rather, the observed differences reflect the relative effects of high- versus low-intensity exercise on pain ratings.

      Our study was not designed to assess the overall effect of exercise compared with rest, but rather to investigate whether exercise intensity influences exercise-induced pain modulation. Specifically, we hypothesised that high-intensity exercise would produce greater pain modulation than low-intensity exercise. This approach was motivated by previous work demonstrating intensity-dependent differences in post-exercise pain responses (Jones et al., 2019; Vaegter et al., 2014).

      In response to the reviewer's comment, we have revised the manuscript to clarify this distinction and have replaced several instances of "exercise-induced hypoalgesia" with the more neutral term "exercise-induced pain modulation" where appropriate. We also explicitly acknowledge in the Limitations that the lack of a no-exercise condition precludes conclusions regarding absolute hypoalgesic/hyperalgesic effects of either exercise condition.

      (1.2) Lack of internal replication across conditions

      We thank the reviewer for this comment. We agree that the observed effect was most pronounced for heat pain at the highest stimulus intensity and was not consistently observed across all stimulus intensities or pain modalities. Importantly, however, this pattern mirrors the findings of our previous study, in which exercise intensity effects were likewise evident for heat pain but not pressure pain. We therefore interpret the current findings as a replication of the modality-specific pattern observed previously rather than an isolated positive result.

      To further address concerns regarding robustness and sample size, we have now pooled the data from the previous and current studies and conducted additional frequentist and Bayesian analyses examining the moderating roles of fitness level and sex on exercise-induced pain modulation. These analyses yielded converging evidence that fitness level contributes to variability in exercise-induced pain modulation, thereby strengthening confidence in the overall findings.

      With respect to pressure pain, previous meta-analyses have reported comparable or even larger exercise effects for pressure pain than heat pain (Naugle et al., 2012). However, most studies included in these analyses employed handheld pressure algometry, whereas our study used cuff pressure stimulation. Consequently, the pressure pain measures used here may not be directly comparable to those reported in the broader literature.

      (1.3) Deviations from the original study and selective use of data

      We agree with the reviewer that we have adapted the rating scale to reflect a real-time pain rating. To provide a comprehensive account of participants’ pain experience, we have included analyses corresponding to the visualisations on how online ratings evolve over the course of the pain administered in Supplemental Figure S7 – S8. Specifically, we conducted LMER models with exercise intensity × time on heat and pressure pain ratings, separately (Supplemental Fig. S7). The results yielded a significant interaction of exercise intensity × time on heat (β = -0.13, SE = 0. 06, t(7577) = 2.12, P = 0.03) but not pressure pain ratings (β = -0.07, SE = 0.10, t(7956) = -0.71, P = 0.48). Furthermore, we conducted LMER models with exercise intensity × time × stimulus intensity on heat and pressure pain ratings (Supplemental Fig. S8), suggesting no significant interaction on pressure pain ratings (β = -0.0002, SE = 0.004, t(2353) = -0.06, P = 0.95) but a significant interaction on heat pain ratings (β = -0.01, SE = 0.003, t(2201) = -3.24, P = 0.001).

      As the reviewer correctly notes, to facilitate comparison with the previous study, we conducted our primary analyses using peak pain ratings. We acknowledge that this approach does not fully capture the richness of the continuous data but allows for comparability.

      (1.4) Over-reliance on null results regarding sex differences

      We thank the reviewer for this important point regarding the interpretation of null effects, particularly in relation to sex differences. We agree that the absence of a statistically significant difference does not, in itself, provide evidence for equivalence between groups.

      To address this issue, we have pooled the samples and supplemented our frequentist analyses with Bayesian analyses. Bayes factors were computed to quantify the relative evidence for the null versus alternative hypotheses, providing a continuous measure of support that complements frequentist inference, particularly in cases of non-significant effects where evidence for the absence of an effect is of interest. Furthermore, posterior distributions of the regression coefficient of interest (in this case, the moderating role of sex on exercise-induced pain modulation) provided no evidence for a moderating role of sex on exercise-induced pain modulation. This approach allows for a more nuanced interpretation of the data, especially concerning null effects. We have adapted the Methods, Results, and Discussion accordingly.

      (2) Limited sample and lack of diversity

      We thank the reviewer for this comment. The study was intentionally designed to include only female participants with significantly higher fitness levels compared to the females from the previous study, as our previous study included females who were slightly less fit than males, making it difficult to separate the effects of sex and fitness. We, therefore, aimed to examine exercise-induced pain modulation in a more homogeneous sample. However, much of the EIH literature has been conducted in highly trained male participants (Janal et al., 1984; Saanijoki et al., 2022; Scheef et al., 2012). As such, studies in women of higher fitness are important to improve our understanding of potential sex differences in exercise-induced pain modulation. While the present findings should be interpreted within the context of the sample studied, when analysed and considered alongside our previous work, they contribute to a broader understanding of exercise-induced pain modulation across sexes and fitness levels.

      (3) Methodological choices limit the interpretability of the data

      (3.1) The use of a non-standard VAS scale (0-150 with a fixed pain threshold at 50) is unconventional and may influence how participants report pain, while limiting comparability with related literature.

      We thank the reviewer for their comment. Since we introduced real-time pain ratings in the current study, while the pain is ongoing, we aimed to introduce a scale that allowed us to pinpoint the period when a painful stimulus reaches painfulness (exceeds 50 on the scale). To allow for comparability between the studies, we have calculated the peak pain rating provided during the real-time pain ratings, as this corresponds to the instruction participants received in the previous study to rate the most painful point of the previous stimulation. Previous research (Koyama et al., 2004) has shown that, in heat pain, real-time ratings account for R<sup>2</sup> = 0.89 of the variability of post-stimulus rating, where much of the variability for the post-stimulus intensity pain rating is accounted for by the peak response during the online ratings (adj. R<sup>2</sup> = 0.3 – 0.4), suggesting good comparability of both pain measures. Furthermore, as we have now pooled the samples and conducted analyses, we rescaled the maximum pain ratings so that ratings below 50 (below the pain threshold) were set to 0, corresponding to VAS 0 in the previous study, resulting in pain ratings ranging between 0 and 100.

      (3.2) Participants explicitly reported expecting exercise to reduce pain, introducing a potential confound that is not presently addressed.

      We thank the reviewer for this comment. Indeed, participants reported expecting lower whole-body pain in response to acute aerobic exercise, but no changes in joint or muscle pain. In the context of exercise, previous research (Colloca et al., 2018) showed that exercise-unrelated expectations and exercise itself induce comparable hypoalgesic effects, though they might work through distinct mechanisms. Studies directly manipulating exercise-related expectations showed that education about EIH, compared with general education about exercise and pain, could induce hypoalgesia following aerobic exercise (Jones et al., 2017). Interestingly, another study (Vaegter et al., 2020) investigated the interplay of exercise-related expectations (through verbal instructions) and resistance exercise on pain perception and showed that only explicit negative instructions induced hyperalgesia, whereas positive or neutral exercise-related instructions did not change the magnitude of EIH.

      Since participants in the current study reported highly specific positive expectations only for whole-body pain, but not for joint or muscle pain, expectations are unlikely to fully explain our findings. Consistent with this, in our previous study using the same prospective expectation questionnaire, we found no significant expectation effects for any pain domain (Nold et al., 2025), although we acknowledge that the samples differed, especially with respect to fitness levels.

      Nevertheless, the current study was not designed to disentangle the effects of exercise and expectations, as expectation ratings were measured prospectively but not manipulated. Therefore, we cannot determine to what extent positive expectations of exercise have contributed to the observed effects, and we have now acknowledged this as a limitation in the Discussion.

      (3.3) A more comprehensive use of the full time series of pain ratings would provide a stronger and more transparent basis for interpretation of the present findings.

      We thank the reviewer for this suggestion. As noted in our response to Comment 1.3, we have included analyses and visualisations of the full time series of online pain ratings in the Supplementary Materials (Fig. S7–S8), providing a more comprehensive understanding of pain dynamics over time.

      Figures are very low in quality - artefacts, small text, insufficient labelling.

      We thank the reviewer for highlighting this and, indeed, rendering the PDF reduced the quality of the images. For the reviewed version, we have been specifically attentive to image quality by increasing font sizes and adding labels.

      There was not enough detail in the methods section for the number of cycling blocks, and how low and high intensity were distributed throughout the session.

      We thank the reviewer for their comment. Participants completed four cycling blocks in total, two HI and two LI exercise blocks, presented in a pseudo-randomised order in the session. To improve clarity, we have added the relevant details to the Methods section.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Major Comments:

      (1) "Wounding/fighting" evidence is confounding.

      Unless I am mistaken, a large part of the argument for inflammation-driven perinodal fat pad atrophy and LN expansion relies on spontaneous fighting injuries in co-housed CCR2-/- males, including animals "culled...due to excessive wounding." Because wound severity, duration, infection load, stress, and cage dynamics are uncontrolled, isn't it difficult to assign causality to "cutaneous inflammation"?

      We thank the reviewer for this point and fully understand the concerns here. We have carefully gone through the text now and ensured that we refer to wounding-associated inflammation throughout. This therefore takes into account potential wound infections etc. We are also confident that the phenotype relates to cutaneous inflammation because it is only seen in lymph nodes and fat pads draining inflamed skin. We have adapted the discussion accordingly to address this important issue (lines 169-172 of the revised text).

      (2) The "CCR2-independent macrophage" conclusion.

      The manuscript interprets persistence/accumulation of macrophages despite reduced inflammatory monocytes as CCR2-independent recruitment or local proliferation. However, CCR2 deficiency can alter immune baselines and long-term tissue remodelling. Perhaps consider bone marrow chimeras (WT to CCR2-/-, CCR2-/- to WT ????) or an inducible CCR2 deletion approach to separate developmental/systemic effects from acute inflammation-driven mechanisms. If "in situ proliferation" is proposed, include a direct readout (e.g., Ki67 in ATMs in the fat pad).

      We have previously published that CCR2-/- mice display no alterations in any myeloid or lymphoid cell subsets with the exception of Ly6C+ monocytes. We have now referred to this in the revised text (lines 135 and 136) and hope that this addresses the reviewer’s concerns. In terms of whether the CCR2-independent increase in macrophages as a consequence of recruitment or local proliferation, the fact that the macrophages are CD11b+, along with the relative increase in inflammatory monocyte content in co-housed CCR2-/- mouse skin, strongly suggests that they derive from peripheral blood monocytes and therefore from recruited cells. We have clarified these points on page 7 of the revised text.

      (3) IMQ and systemic effects.

      The work relies on topical Aldara/imiquimod as an "inflammation without antigen" driver of distal LN/fat-pad remodelling. But IMQ is well known (and cited by the authors) to enter circulation and drive systemic responses, which could blur whether effects are truly draining-site specific vs systemic metabolic/inflammatory effects. It would be ideal to provide systemic context: plasma cytokines and/or metabolic readouts (e.g., circulating FFAs) to distinguish local vs systemic drivers.

      This is an important point. We have now included plasma cytokine data showing that these are indeed elevated systemically in Aldara-treated mice (new Supplementary Figure 5). We have altered our discussion of this point to reflect these new data (lines 228-229 of the revised text).

      (4) Macrophage dependence is inferred from CSF1R inhibitor treatment.

      However, validation of macrophage depletion and specificity is incomplete. The manuscript uses AZD7507 (CSF1R inhibitor) and observes partial rescue of fat pad/LN phenotype while skin severity (PASI) is unaffected. But, to this reviewer, the data shown do not clearly quantify actual macrophage depletion efficiency in the target fat pad, and LN at endpoint, and CSF1R blockade can affect multiple myeloid populations. Therefore, show absolute macrophage counts (and likely other myeloid populations) in fat pad and LN with/without AZD7507 at the analysed timepoints, not only outcome weights. (The methods describe dosing but not endpoint depletion quantification??)

      We have now added these data (new Figure 7D and Supplementary Figure S6 and discussed on page 13 of the revised manuscript). What we show is that fat pads from Aldara-treated mice show a large reduction in macrophages and also a reduction in dendritic cells, although the number of dendritic cells was already low in the fat pad of Aldara-treated females. The lymph nodes of Aldara-treated females with AZD7507 also show reduced macrophage counts, but the reduction is also seen in all other immune subsets (lymph nodes were smaller so reduced counts in all subsets). We hope that these new data satisfy the reviewer’s concerns.

      (5) Fat pad atrophy/LN expansion is a correlation.

      The paper emphasises negative correlations between fat pad and LN weights/cellularity at baseline and with inflammation. But correlation does not establish whether fat pad lipolysis drives LN expansion, whether LN changes drive fat remodelling, or whether both reflect systemic mediators. Add tissue-level evidence distinguishing true adipocyte loss vs other contributors to "weight change" (e.g., oedema/fibrosis).

      We agree that our data do not establish a direct causal relationship between adipose tissue loss and LN expansion, but the observations do demonstrate a strong temporal association. As seen from the added graph (new Figure 8B and related text on page 13 of the revised manuscript), the rapid and concurrent occurrence of both processes (approximately 25% reduction in fat pad weight and 30% increase in LN size within 24 h of Aldara treatment) suggests that they are closely linked biological events occurring within the same tissue microenvironment. Determining whether these changes arise through direct local interactions or reflect broader inflammatory mediators would require additional mechanistic investigation.

      (6) Evidence for "fatty acid donation" from fat pad to LN.

      The lipid data are described as "exemplary," and the inference that LN fatty acids originate from the fat pad is based on temporal ordering and relative abundance. This does not rule out plasma spillover, LN-intrinsic metabolism, or altered lymph flow.

      We agree with reviewer and have amended our discussion of this point appropriately (page 16 of the revised manuscript).

      Reviewer #2 (Public review):

      The authors aim to demonstrate skin inflammation is associated with fat pad atrophy and lymph node expansion. They further propose that these phenotypes are driven by the recruitment and lipid metabolism of CCR2-independent macrophages.

      The authors took advantage of two skin inflammation models, fight-induced and imauimod-induced skin inflammation and analyzed multiple tissues, including skin, fat pads, and lymph nodes. Using a macropahge-depletion method (e.g., CSF-1R inhibitor), the authors further suggest the inverse correlation between fat pads atrophy and lymph node expansion is macropahge-dependent. While the study identifies this intriguing inverse correlation during skin inflammation, the causal pathway linking fat pad atrophy and lymph nodes enlargement has not been clearly established.

      To improve the rigor of the manuscript, the authors address the following concerns;

      (1) CCR2-deficient mice showed reduced inflammatory monocytes and monocyte-derived macrophages (PMID:16462739; 16341265). During tissue inflammation, CCR2+ classical monocytes are typically recruited to the injured peripheral tissues, including skin, where they differentiate into monocyte-derived macrophages (PMID:38474365). While inflammatory monocytes were reduced in the skin (Figure 3 d), fat pads (Figure 4a, S2D) of CCR2-deficient mice, macrophage numbers were significantly increased in these mice. It remains unclear whether CCR2-independent macrophages were newly recruited from alternative sources or tissue-resident macrophages underwent local self-proliferation to compensate for the loss of CCR2+ monocyte-derived macrophages.

      We agree with reviewer and have expanded our discussion of this important point (see text on pages 7 and 8 of the revised manuscript). As mentioned in response to reviewer 1 we have inferred from the expression of CD11b and c on recruited macrophages that they are derived from peripheral blood monocytes and therefore ultimately are recruited and have not arisen due to local proliferation. We hope that the reviewer is happy with this expanded discussion.

      (2) In line 258, the authors state that there was "a significant reduction in CD11C- CD206+ anti-inflammatory macrophages (Figure 4b i-iii)". However, the quantification data in Figure 4b iii do not appear to show any reduction in anti-inflammatory macrophages in either males or females. Please reconcile this discrepancy between the text and the figure

      We apologise for our carelessness here and this is the consequence of not having normalised some of the data presented. We have now done this and updated the graph which now, hopefully, more convincingly demonstrate reduction in CD11c- macrophages.

      (3) Although CD11C and CD206 were historically used as markers of inflammatory and anti-inflammatory markers, respectively. These markers are no longer considered sufficient to define the macrophage polarization state, particularly in adipose tissue, where they are constitutively expressed by resident macrophages (PMID:34210853). Numerous studies have demonstrated substantial macrophage diversity/heterogeneity across iWAT, eWAT, and brown fat tissues. The authors should discuss adipose macrophage diversity beyond the outdated M1/M2 frame.

      We thank the reviewer for pointing this out and apologise for the superficial way in which we have addressed macrophage heterogeneity in the fat pads. We selected CD11c, as it is clearly an important discriminatory marker for tissue macrophages, and CD206 as it presents itself as a common marker of both CD11c-positive and CD11c-negative macrophages in our analyses. We fully acknowledge that the understanding of macrophages has moved on beyond the simple pro-and anti-inflammatory categories have therefore amended the discussion appropriately (please see text on page 8 of the revised manuscript). We hope that these changes are satisfactory for the reviewer.

      Minor issues

      (1) Clarify which claims are "antigen-independent" vs "no intentional antigen." The introduction/abstract emphasises "absence of antigen presentation," but inflammation models (wounds/IMQ) do not exclude endogenous/self-antigens. Rephrase or add controls aligned to the claim.

      We fully accept reviewer’s point here and have removed references to ‘antigen-independent’ throughout.

      (2) Provide more explicit randomisation/blinding details for subjective readouts (e.g., PASI scoring).

      We agree that additional methodological detail would improve transparency. Inflammation scoring was performed by an independent collaborator blinded to treatment allocation. Animals were not formally randomized between groups because AZD-treated mice required additional gavage procedures and handling distinct from control animals. We have now included additional details in the Materials and Methods section (see page 22 of the revised text).

      (3) Increase transparency on sample sizes and independence when pooling tissues (e.g., pooled fat pads, pooled macrophage RNA samples).

      Lymph nodes and fat pads were used for different analyses throughout the study, resulting in differences in sample processing and pooling strategies between experiments. Information regarding biological replication and any sample pooling is provided within the corresponding figure legends for each experiment.

      In most cases, both fat pads and lymph nodes of each mouse were pooled for analysis, this is specified in each figure legend (i.e. ‘each point represents the combined weight of both inguinal lymph nodes/fat pads for each mouse’

      Pooling of fat pads from multiple individual mice was only done for RNA sequencing due to low numbers of adipose tissue macrophages. Again, details are in the figure legends.

      We hope that this is acceptable to the reviewer.

      (4) Quantify systemic effects of IMQ (weight loss is mentioned in monitoring; include the data and interpret its relevance).

      Body weight was monitored throughout the study for animal welfare purposes but was not systematically recorded for analysis. While we cannot formally exclude systemic effects, we believe the observed phenotype is unlikely to be driven primarily by general sickness behaviour, as substantial tissue changes were already evident by day 1 following treatment, including an approximately 25% reduction in fat pad weight and a 30% increase in lymph node weight (please see revised figure 8B). The rapid onset and tissue-specific nature of these changes suggest an early biological response rather than a secondary consequence of generalized illness.

      (5) Tone down mechanistic language ("donation," "feeds the LN") unless tracer/intervention experiments are added; keep as "consistent with" until proven.

      We thank the reviewer for pointing this out and have amended the language appropriately.

      Recommendations for the authors:

      Reviewer #2 (Recommendations for the authors):

      Minor concerns;

      (1) Please delete 'i-iii' from Figure 3b, as these panel labels are not referenced anywhere in the manuscript.

      We have carefully edited, and improved, figures throughout the text and hope that they are now acceptable.

      (2) Please change '1D' to '2D' in Figure S2.

      This has now been done and we apologise for this carelessness.

    1. Author response:

      Thank you for providing detailed and positive feedback. This will help us to improve manuscript and its accessibility for a broad audience.

      We first want to highlight what we believe is the main aspect, and therefore novelty, of our work: Combining cell-cell mechanics, mechanical regulation of growth and stochastic cell fate decisions leads to a stable population of stem cells in a stable balance with more differentiated cells, avoiding neutral drift, extinction or overgrowth. Furthermore, this combination leads to stable clusters, i.e. without further coarsening. We call these structures “niche-like”, as we believe stability is fundamental for biological function.

      As the referees point out, this work builds on previous works in the literature, and highlighting the differences and advances will benefit the manuscript. As referee 3 points out, homeostatic regulation by mechanics, in particular pressure, has been discussed intensively in the literature, by us and many others. The novelty in our work is that we apply this regulatory mechanism to a multi-component tissue, and there can stabilize not only the total number of cells, but also their relative composition. In particular, we derive analytical equations relating composition to differentiation rates, and demonstrate their validity in agent-based simulations. In the revised manuscript we will highlight more clearly that this is an application of previous works on a novel system.

      Referee 2 points to Klein et al. (2008). We do agree that their model also shows clustering, and therefore that we should have compared and contrasted our model more thoroughly with this work. However, as we will show more clearly in a revised manuscript, our results differ crucially from this form of clustering without detailed mechanical interactions. As also discussed in the original work by Klein et al., the mechanism therein results in clusters which are not stable, but continue to grow indefinitely over time (although at a slow rate). We show that our simulations display stable clusters which do not grow further, even when simulating for very long time scales, and that these clusters are well-defined, by structurally different correlation functions showing clear inter-cluster separation. In the revision, we will demonstrate that even when starting from a perfect cluster, the stem cells separate, resulting in finite stable clustering. Thus, our clusters are true “fix points” of the stem cell dynamics. Referee 3 rightfully recommends that we should identify more clearly which mechanism is responsible for the stable niche-like structures. To this end, we will compare more closely to Klein2008 as a model without mechanics leading to log(t) coarsening, and our earlier work (Krämer et al., 2024) where stem cells were immortal. There, we had found that mechanics alone produces the reverse result, i.e. leads to enhanced separation of stem cells, which anti-cluster and are dispersed as single cells. We will add new simulations as an additional control that contain cell-cell mechanics, but no mechanical regulation of growth. This combination will allow us to disentangle how the combination of cell mechanics, mechanical feedback on growth and stochastic differentiation results in the formation of stable niche-like structures.

      Note that neither Klein2008 nor Krämer2024 have a physical mechanism that maintains the overall stem cell population number stable. Krämer2024 simply fixes the number of stem cells, whereas the model in Klein 2008 results in stochastic drift in stem cell number.

      Evidentially, we will also address the more technical weaknesses of the manuscript identified by the referees. In particular, we will demonstrate more clearly that the observed structures are genuine emergent features of the model rather than artefacts of modelling assumptions or analysis choices, especially with respect to the patching technique used to obtain large simulations.

    1. Author response:

      The following is the authors’ response to the original reviews.

      eLife Assessment:

      This useful study employs optogenetics, genetically-encoded dopamine and serotonin sensors, and patch-clamp electrophysiology to investigate modulations of neurotransmitter release between striatal dopamine and serotonin neurons - a topic of interest to neuroscientists studying the basal ganglia. The results suggest that the dopamine and serotonin systems operate largely in parallel, with the activation of serotonin neurons resulting in a small, transient dopamine release. The authors suggest that this interaction occurs via glutamate release in the ventral tegmental area, findings that are closely related to previous work. Some conclusions are incomplete requiring larger samples-sizes and controls.

      We sincerely thank the editor and reviewers for their thoughtful and constructive comments. Addressing their concerns required extensive additional experimental work and the involvement of new personnel. We increased sample sizes, completed previously missing experimental groups, generated a largely new dataset, and performed additional anatomical experiments and analyses. We also removed the patch-clamp electrophysiology experiments to sharpen the study’s focus and extensively revised and reorganized the manuscript to address methodological and interpretative inconsistencies. Although the central concept remains unchanged, the revised manuscript provides a substantially more rigorous and consistent account of the limited and directionally asymmetric circuit-level coupling between striatal dopamine and serotonin release.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      In this study, Liu et al use optogenetics and genetically encoded neuromodulator sensors to test the extent to which dopamine neuron stimulation produces striatal serotonin release, and vice versa. The study is timely given growing interest in dopamine/serotonin interactions and in the context of recent work showing bidirectional and dynamic regulation of striatal dopamine by another neuromodulator, acetylcholine. The authors find that striatal dopamine and serotonin afferents function largely independently, with dopamine neuron stimulation producing no striatal serotonin release and serotonin neuron stimulation producing minimal striatal dopamine release. This work will inform future work seeking to dissect the contributions of striatal dopamine, serotonin, and their interactions to various motivated behaviors. While the paper's main conclusions are adequately supported (see Strengths), additional controls and experiments would significantly broaden the paper's impact (see Weaknesses). Finally, this draft of the work is poorly presented with numerous errors, omissions, and inconsistencies evident throughout the text and the figures that should be addressed.

      Strengths:

      The study employs optogenetic stimulation simultaneously with fiber photometry recording of dopamine or serotonin release measured with genetically encoded sensors. These methods are state-of-the-art, offering tighter temporal control compared to pharmacological methods for manipulating dopamine and serotonin and improved selectivity over techniques like electrochemistry and microdialysis used to record neuromodulator release in previous studies on the subject. As a result, the paper's main conclusions are well supported.

      Weaknesses:

      (1) The electrophysiology experiments in Figure 3 are only tangentially related to the focus of the study, and their findings are almost entirely irrelevant to the paper's main conclusions. The results of these experiments are also not novel. Glutamate corelease from 5-HT neurons has been previously shown, including in the OFC and VTA (Ren et al, 2018, Cell, McDevitt et al, 2014, Cell Rep, Liu et al 2014, Neuron; and others). The authors should explain more clearly what they think these data add to the manuscript and/or consider removing them altogether.

      We thank the reviewer for their insightful comments regarding the patch-clamp electrophysiology data. We acknowledge the concerns raised by multiple reviewers and have therefore removed these data from the revised manuscript to improve clarity and focus.

      (2) Related to the point above, as far as I can tell, the only value the electrophysiology data add is to suggest that perhaps activation of serotonin neurons may drive minimal striatal dopamine release via glutamate corelease in the VTA. The evidence provided in this version of the manuscript is insufficient to support that claim, but the manuscript would be significantly strengthened if the authors tested this hypothesis more directly. One way to do that could be to stimulate serotonin axons in the striatum (as opposed to the serotonin cell bodies) and record striatal dopamine release.

      This is an interesting approach. However, given the divergent projection of serotonin fibers and the need for a strict spectral separation between excitatory opsin and transmitter sensor fluorescence, we retained the current approach, which allows us to investigate circuit-level interactions while minimizing technical confounds.

      A complementary anatomical approach would be to use retrograde tracing to test whether the DR 5-HT neurons projecting to the striatum are the same or different from the VTA projecting population.

      We performed the suggested experiment and have included the new data in the revised manuscript (Figure 1F–H). This approach revealed a clear topographical organization. These results indicate that the identified neuronal populations are largely segregated.

      (3) The findings would be strengthened by the addition of a fluorophore-only control group lacking opsin expression in all experiments in Figures 1 and 2.

      We thank the reviewer for this important suggestion. We requested authorization to add an opsin-negative control cohort, but this request was not approved under the applicable animal-welfare regulations. We therefore cannot fully exclude nonspecific physiological effects of light delivery and now acknowledge this limitation in the Discussion. Nevertheless, the stimulation-locked response was confined to the biosensor channel and absent from the isosbestic channel, arguing against direct optical contamination. Moreover, application of the same optical stimulation protocol in the VTA did not generate a detectable stimulation-locked 5-HT signal. Although these observations do not fully replace an opsin-negative control, they support the interpretation that the response reflects a biological signal rather than direct optical interference.

      (4) The experiment of stimulating serotonin neurons and recording serotonin release in the NAc was not performed. It would be useful to be able to compare the magnitudes of evoked serotonin release in these two striatal regions, though it is not central to the main claims of the paper.

      This point has now been addressed with additional experiments, and the figure has been reformatted accordingly in the revised manuscript.

      (5) The interpretation of the results from Figure 2 is described inconsistently throughout the manuscript. The title implies there is significant crosstalk between the dopamine and serotonin systems. The abstract calls the crosstalk "transient", which is a description of its temporal dynamics, not its magnitude. Then the introduction figures and discussion all suggest the crosstalk is minimal. I suggest the authors describe the main findings - minimal crosstalk between the dopamine and serotonin systems - clearly and consistently in the title, abstract, and main text.

      We agree with the reviewer and have revised the title, abstract, Results, figure legends, and Discussion to describe the magnitude and directionality of the interaction consistently. The revised manuscript now emphasizes that striatal dopamine and serotonin release operate largely in parallel, with limited and asymmetric crosstalk: activation of VTA dopamine neurons did not produce detectable serotonin release, whereas activation of dorsal raphe serotonergic neurons induced only a weak, stimulation-locked dopamine signal without a sustained increase in dopamine amplitude. The revised title, “Asymmetric Circuit-Level Crosstalk Between Dopamine and Serotonin Release in the Striatum,” and the corresponding changes throughout the manuscript now more accurately reflect these findings.

      Reviewer #2 (Public review):

      Summary:

      This brief communication aims to clarify interactions between the dopamine (DA) and serotonin (5-HT) systems of mice. The authors use optogenetic stimulation of DA neurons in the VTA or of 5-HT neurons in the DRN, while monitoring the fluorescence of DA and 5-HT sensors in the nucleus accumbens (NAc) and dorsal striatum (DS) using fiber photometry. The authors report on a small release of DA in the NAc following DRN stimulation, which they attribute to glutamate co-release onto VTA DA neurons using slice electrophysiology. The authors also report on cocaine-induced 5-HT release in the striatum.

      Strengths:

      This is a topic well worth studying.

      Weaknesses:

      In its current form, this is an incomplete and underpowered study that does little to clarify the complicated relationship that exists between DA and 5-HT in the mammalian brain under physiological conditions or during cocaine use.

      We appreciate the reviewer’s thorough evaluation and constructive efforts. We acknowledge that the original manuscript did not meet the expected standards and have therefore undertaken a complete revision. We hope that the revised version addresses the concerns raised and provides a clearer and more rigorous presentation of our findings.

      Reviewer #3 (Public review):

      The authors suggest that the small release of DA may be due to a release of glutamate from DRN 5-HT neurons to the VTA that stimulates weakly and in a transient fashion the VTA DA neurons, which in the end, produce a transient and small release of DA in the NAc.

      Their findings give more information on the previously reported complex and partial known crosstalk between 5-HT and DA in the NAc.

      I only have some minor concerns about the manuscript:

      (1) In Figure 2F, there is a missing curve for 5-HT in NAc. Besides, the legend shows n=2, making it difficult to perform statistical analysis with that data.

      We repeated the experiments and analysis with a new and expanded dataset. We believe this revised dataset now provides sufficient power for robust statistical analysis.

      (2) In Figure 3, the use of NBQX/AP5 is shown, but it is not mentioned either in the methodology or in the discussion. What is the meaning of those results?

      Based on the reviewers’ suggestions, we have removed this figure entirely from the revised manuscript.

      (3) Line 98 compares results from two different places of stimulation. The results are related to stimulation in the VTA, but the comparison indicates that the stimulation was made in the DRN.

      The manuscript has been extensively revised, and all relevant sections of the text have been updated accordingly.

      (4) If the release of 5-HT in Nac does not occur, it needs to be precise in the abstract that 5-HT is released in the dorsal striatum (DS) but not in the NAc (line 19).

      We performed an additional set of experiments and confirmed the presence of 5-HT release in the NAc.

      (5) Be consistent with the way you mention the 5-HT neurons. For example, in lines from 106 to 119, SERT neurons are used. Previously, 5-HT neurons were used.

      We have carefully considered this issue throughout the revised manuscript and have taken steps to ensure consistency, as highlighted by the reviewer.

      (6) There are several points of confusion when referring to the figures, making the text difficult to follow because the text explains something that is not shown in the figure cited.

      We have carefully considered this issue throughout the revised manuscript and have taken steps to ensure consistency, as highlighted by the reviewer.

      Recommendations for the authors:

      Reviewing Editor Comments:

      Additional comments from the reviewers recommend that the authors increase sample sizes, carry out control experiments to exclude non-specific effects, and modify the title and abstract to reflect the minimal cross-talk observed between dopamine and serotonin. Finally, we note that the text of the manuscript does not meet minimum standards in the field for clarity, interpretability, or reproducibility.

      We acquired a new experimental cohort, and performed additional experiments suggested by the reviewer. The manuscript has been revised and reformatted, incorporating all reviewer comments. We hope that this new version now meets the expected standards for clarity, interpretability, and reproducibility in the field.

      Reviewer #1 (Recommendations for the authors):

      (1) For angled stereotactic injections, the direction of the angle (ML, AP, etc) is not defined.

      Added to the revised manuscript.

      (2) The manuscript is full of grammatical errors and is very difficult to follow in some places, especially the results section for Figures 2 and 3. The following is an incomplete list of the most obvious errors to give examples of what I mean, but I strongly urge the authors to thoroughly revise the entire text.

      (a) There appear to be photometry traces copied and pasted by mistake over the x-axis labels in the bar graph in Figure 1E.

      (b) Line 41 states that fiber photometry recordings were used in reference 17, which is a human study that used voltammetry.

      (c) Figures are referenced out of order throughout.

      (d) Acronyms are used without being defined on the first usage.

      (e) Lines 54-56, missing references.

      (f) Line 82, the crosstalk reported in this paper is unidirectional, not bidirectional.

      (g) Line 92 describes the virus as AAV-dLIGHTX.XX, where presumably the exes are placeholders for numbers that were never replaced.

      (h) The text of the results section for Figure 2 in some cases directly contradicts the data it describes, and likely has some mistaken figure panel references.

      (i) Line 123 is missing a reference and just has the placeholder REF.

      (j) Lines 182-183 are a copy-paste mistake from lines 185-186.

      (k) Scalebars in figure legends are in units of micromolar, not micrometers.

      The manuscript has been extensively rewritten to address and incorporate the reviewers’ comments.

      Reviewer #2 (Recommendations for the authors):

      This is one of the least impressive and compelling manuscripts I have ever been asked to review. It reads in many ways like a first draft, not like a document that was meticulously prepared and proofread prior to submission. The data and analyses are shockingly light (with some conclusions supported by an N of 1 or 2) yet frustratingly difficult to interpret. The text and figures are full of typos, inconsistencies, and factual errors in interpretation. Most concerningly, this study does little to clarify the complicated relationship that exists between DA and 5-HT, including providing compelling evidence for their key finding of 'crosstalk' between both modulators or mechanistically implicating glutamate co-release. In fact, it might add to the noise. It is therefore unclear what the value is of this study in its current form.

      We thank the reviewer for their detailed and thorough comments, which we saw as an opportunity to substantially improve the manuscript. We have therefore undertaken a comprehensive revision to improve clarity, coherence, and overall quality. As part of these revisions, we have removed the original Figure 3 presenting the in vitro patch-clamp electrophysiology data. We hope that the extensive changes implemented in the revised manuscript adequately address the reviewer’s concerns and significantly strengthen the study.

      General comments:

      (1) Limited scope: the design of the experiments performed offers very few opportunities for identifying 'crosstalk' between DA and 5-HT:

      (a) To most, such cross-talk might best be imagined at the level of cells expressing receptors for both modulators, yet this is not studied. Cross-talk may also manifest in complex circuit-level interactions, downstream of brain areas directly targeted by DA and 5-HT. This is not studied either. Instead, only one type of experiment is performed: optogenetically stimulating cell bodies in the midbrain while monitoring DA/5-HT levels in the striatum. Opportunities for 'cross-talk' in this preparation are exceedingly limited. For example, the only way that optogenetically-evoked DA release may impact 5-HT levels (assuming classical, direct projections from DA neurons to the striatum) is via presynaptic modulation of 5-HT release from axons. Though potentially interesting, it is not exhaustive.

      We agree that many types of crosstalk can be investigated; however, we chose to first adopt a broader approach that integrates neuronal circuit-level mechanisms. We believe that an important discrepancy remains in the literature that needs to be addressed. While our findings do not exclude the involvement of other forms of crosstalk, they aim to clarify whether crosstalk already exists at the level of neuronal circuits, which our results support.

      (b) Any negative modulation of DA or 5-HT release would require a baseline tone of either modulator within the dynamic range of the sensor, which is not demonstrated. Thus, in both cases, a negative influence cannot be excluded, limiting any finding to 'positive' modulation. This is problematic for a study set on setting the record straight on 'cross-talk' between DA and 5-HT, given that prior studies pointed to antagonistic influences.

      Previous studies using the same type of sensor have already demonstrated inhibitory crosstalk. For example, the study “Opponent Control of Reinforcement by Striatal Dopamine and Serotonin” successfully used this approach to reveal opposing interactions between dopaminergic and serotonergic signalling. Therefore, our findings are consistent with the possibility of circuit-level crosstalk and further contribute to resolving this ongoing question.

      (c) Only one stimulation paradigm is tested, and its biological (ir)relevance is not discussed.

      The stimulation paradigm used in this study has been extensively validated in multiple publications from our laboratory and has consistently been shown to promote reinforcement. Our recent review provides a comprehensive overview of this approach and its established behavioral effects. (Lüscher et al, Neuron, 2026, PMID: 42462721).

      (d) Only one brain region is investigated (striatum), with little justification for omitting other regions where both modulators coexist (e.g., amygdala, cortex, DRN).

      Not all brain structures can be investigated within the scope of a single study, and we acknowledge this limitation in the Discussion section.

      (e) The suitability of the chosen behavior and cocaine administration to reveal interactions is not mentioned.

      We have now clarified the use of i.p. cocaine injection to study the different temporal dynamics of 5-HT and DA release.

      (2) Scarcity of data and questionable analyses and interpretation:

      We thank the reviewer for the detailed comments listed below (a-m). In response, we repeated many experiments, increased sample sizes, completed the experimental groups, fully reanalysed the dataset, and removed the patch-clamp electrophysiology data. The manuscript has been extensively rewritten and reformatted based on a largely new dataset. In addition, we now focus specifically on one form of crosstalk and have expanded the discussion to address other potential mechanisms, as suggested by the reviewer. We hope this revised version adequately addresses the concerns raised. Because of the many changes in the text, the concerns listed below were addressed.

      (a) Conclusions for Figures 3B and C are based on a N of 1 whole cell recording each.

      (b) The relevance of data in Figures 3D and 3E to test the proposed hypothesis is unclear.

      (c) Figure 2F is an average of N=2 recordings.

      (d) Lines 98-100: Concluding statement not supported by experiment performed.

      (e) Apparent contraction: Lines 112-113 indicate that 5-HT neuron stimulation failed to evoke 'any significant change in DA', while lines 117-118 talk about a small but significant increase in DA in response to the same manipulation.

      (f) Line 114: conclusion not supported by data; Figure 2E points to DA, not 5-HT, and Figure 2F-H only shows 5-HT in DS, not NAc. Legend specifies that only 2 recordings are averaged in Figure 2F, and n=4 are quantified in Figures G and H, despite the plot containing 5 data points. What is going on?

      (g) The key finding of this study is a transient, barely-detectable increase in NAc DA for ~1s during the 10s stimulation of 5-HT neurons in N=4 mice (Figure 2D). It is not clear if a significant increase was observed in all mice tested, or if this increase is significantly different from what is seen in DS. Was this effect seen in multiple testing sessions?

      (h) Concerningly, the authors do not exclude the possibility of a 'startle' response to strong light delivery in mice expressing tdTomato-only. This is an essential control that is missing.

      (i) Very few details regarding this DA response are offered. How soon does it appear following DRN stimulation? If mediated by glutamate co-release, it ought to appear with the very first light stimulus.

      (j) The physiological significance of this stimulation paradigm is not established. Comparing it to cocaine-evoked DA release is not satisfactory, as cocaine elevates DA beyond levels encountered physiologically.

      (k) Correlative evidence to implicate glutamate is insufficient. Does co-release depress when driven with the same stimulus train as that applied in vivo? Is it strong enough to drive DA neuron firing? Does it not affect DS-projecting DA neurons? Does this DA 'blip' disappear in mice genetically deficient in glutamate co-release (using SERT-Cre vglut2-floxed mice, which are commercially available)?

      (l) The authors don't find evidence for DA stimulation affecting 5-HT release in the striatum. Is this sufficient to exclude any influence of DA on 5-HT? Isn't the fact that cocaine evokes 5-HT release evidence of an interaction? As such, it is unclear if the experiments performed significantly advance our understanding of whether and how DA and 5-HT influence one another.

      We respectfully disagree with this statement. Cocaine directly binds to the serotonin transporter (SERT), thereby blocking serotonin reuptake into the presynaptic terminal and increasing extracellular 5-HT levels in the synaptic cleft. Furthermore, dopamine and serotonin release exhibit distinct temporal dynamics, suggesting that their release is mediated through different molecular mechanisms and neural circuit pathways rather than through a single shared process.

      (m) The evidence that 5-HT stimulation alters DA release in the striatum is not compelling, but also not sufficient to exclude or support cross-talk between both modulators. The evidence provided is simply insufficient to strongly validate or challenge earlier studies.

      (3) Minor:

      In this revised manuscript, we have carefully implemented the reviewers’ suggestions and addressed the concerns they raised. We believe that this revised version addresses a significant proportion of the reviewers’ concerns and hope that these fundamental improvements are fully recognized during the evaluation.

      Because of the many changes in the revised manuscript, the concerns listed below do no longer apply or were addressed.

      (a) In the intro paragraph, line 19, specify that you are monitoring DA/5-HT in the striatum of mice.

      (b) In the results section, indicate the preparation: in vivo, awake, what were the mice doing...

      (c) Inconsistent nomenclature: VTA dopamine neurons are referred to as 'VTA DA', while dorsal raphe serotonergic neurons are referred to as 'DRN SERT' or 'DR SERT'. Why the difference? Is there any reason to believe that SERT-Cre mice label non-serotonergic neurons? Please adopt a consistent nomenclature and/or justify your choice. Also, if neurons are optogenetically stimulated, specify the word 'neuron' (e.g., line 118 refers to 'DR SERT stimulation', which could be interpreted to suggest the transporter is being activated).

      (d) Line 103 and elsewhere: Confusing terminology referring to VTA DA neurons stimulation as 'modulating' or 'altering' DA release in the striatum. Isn't it directly evoked by the stimulation of DA-releasing neurons? Please change the terminology so as not to make it unnecessarily vague.

      (e) Lines 111-112: comparison between DA and 5-HT fluorescence devoid of biological meaning. Relative increases in the fluorescence of 2 sensors that are molecularly distinct and separately-expressed in different cohorts of mice cannot be meaningfully compared.

      (f) The timeline in Figure 1A suggests that the optogenetic stimulation protocol is initiated 5 min prior to cocaine injection. Figure 1D (right) plots this 5 min baseline, yet little/no DA release can be seen, despite Figure 1F indicating peak DA ratios of 0.5-1. Please explain. Since both sets of recordings were performed back to back and are directly compared, make sure to show them both on the same graph for direct comparison.

      (g) Figure 1E contains 2 misplaced data traces.

      (h) Figure 2D. Please repeat for the full stimulation window, not just for the few seconds where a tiny change in DA is seen.

      (i) Figure 2E is misleading. It suggests that the peak extracellular DA concentration in NAC following DRN stimulation is approximately half of what cocaine evokes and similar to what VTA DA stim evokes (Figure 1F). But this is simply not true. There must be an error in calculation, and one should wait more than 20 minutes to properly estimate peak DA concentration in cocaine.

      (j) What is the value of comparing optogenetically-evoked neuromodulator release to cocaine-evoked release? Can the authors be sure that the DA levels reached in cocaine are not saturating the DA sensor? Wouldn't this be required to permit comparison?

      (k) Line 123: Please include a citation. Rephrase the sentence to avoid sounding dismissive.

      (l) Line 124: Vague/confusing sentence. What is meant by 'optogenetic projection targeting' and 'parsing the synaptic currents in identified regions'?

      (m) Figures 1D, 1G, 2C, 2F: confirm y-axis unit of measure. Are DA transients really only 0.2% in amplitude?

      (n) Figure 3B, 3C: number of recordings performed in DA and NAcSh, anterior not specified. Only one trace showed, and no summary plot. Insufficient data presented to draw conclusion.

      (o) How does the presence of EPSCs in OFC or NAc help support the author's finding of a brief elevation of DA upon DRN stimulation?

      (p) Line 358: Wrong unit.

      Reviewer #3 (Recommendations for the authors):

      Some minor concerns are the following:

      (1) In line 31, define what DS is.

      (2) In line 57, the word "neurons" is missing in the phrase ".....decreases 5-HT neuron spontaneous firing in DRN,...".

      (3) In line 111, the comparison needs to be between 5-HT release due to optogenetic stimulation with the 5-HT release due to cocaine infusion, not with DA release due to cocaine infusion.

      (4) In line 112, it should be Figure 2F.

      (5) In line 114, instead of 5-HT, it should be DA. In addition, it is not Figure 2E, but 2C.

      (6) In line 123, add the appropriate reference instead of "REF".

      (7) In lines 182 and 183, the text is out of context.

      (8) In lines 250 - 251, the text is out of context.

      (9) Why was Rabit anti-GFP if you do not use GFP in the procedures?

      While the manuscript underwent a complete comprehensive revision to improve clarity, coherence, and overall quality, we have carefully implemented the reviewers’ suggestions and addressed the concerns they raised.

    1. Author response:

      The following is the authors’ response to the previous reviews.

      Public Reviews:

      [Editors' note: Overall, the reviewing editor and reviewers agreed that authors rigorously addressed reviewers' major scientific concerns.]

      Reviewer #1 (Public review):

      Hanako and colleagues demonstrated that glycolipid MPIase is essential for the TAT system, and they successfully reconstituted the TAT system in vitro for the first time. This will facilitate the understanding of the mechanism of the TAT system.

      Comments on revised version from Reviewer 1 and the Reviewing Editor:

      In Reviewer 1's points 1 and 2 regarding statistical significance of immunoblotting data (in recommendation to authors), authors stated that they repeated the experiments three times in the rebuttal letter but not in the figure legends. We recommend authors to add a statement such as "errors denote +-SD (N = 3)" in the final version, which will make the data more solid and reliable.

      Thank you for the comments. We added the suggested sentence.

      Reviewer #2 (Public review):

      Summary:

      In this manuscript, the authors investigated the relationship between the Tat system and MPIase, a glycolipid that facilitates protein integration into the bacterial cell membrane. The TAT (twin-arginine translocation) system is a unique membrane transport machinery that exports fully folded proteins containing a twin-arginine signal peptide. Using both in vivo and in vitro approaches, the authors demonstrated that a sufficient amount of MPIase is required for Tat-dependent protein translocation. Furthermore, the authors successfully reconstituted the Tat transport system by combining recombinant TatA, TatB, TatC, MPIase, and FoF1-ATP synthase.

      Strengths:

      The reconstituted system clearly demonstrated the requirement for each component, as substrate translocation occurred only when all components were present. Based on these findings, the authors proposed a mechanistic role for MPIase in facilitating Tat-mediated membrane translocation. Previous studies have shown that MPIase is involved in Sec-dependent protein translocation and membrane protein integration, as well as YidC-dependent membrane insertion. The present study further demonstrated that MPIase also plays an essential role in the Tat translocation pathway. Overall, this work highlights the central importance of MPIase in bacterial membrane protein biogenesis and provides new insights into the molecular mechanism of Tat-dependent protein transport.

      Comments on revised version from Reviewer 2 and Reviewing Editor:

      (Reviewer 2) It is nice to find the mistake in Fig. 4B (RR, EK413, (not +MPIase)) and corrected it in the revised version. However, the data of Fig. 4B and the related modified text on P.9 L256-269 are not very easy to understand what the authors are trying to argue. This reviewer believes that the magnitudes of MPIase expression level are Ek413 > +MPIase > delta-MPIase. Therefore, the means of supernatant in the delta-MPIase and EK413 represents mostly cytosol and periplasm, respectively. On the other hand, the +MPIase shows less supernatant that means a large part of TorA-GFP are trapped nearby membrane but not aggressively transported. Similar results are found also in (KK) case, whereas the sup level in EK413 is lower than that of (RR) case due to the lack of twin-arginine motif in the substrate.

      Although these results are convincing in explaining the model in Figure 5, authors might be able to attempt to refine them more understandable. Especially, the revised text on P.9 L256-269 is not enough for leading readers to the author's claim. So that, the authors should revise the text about Fig. 4B again and the related description in the manuscript. Another option is it would be possible to delete whole Fig. 4B, because Fig. 4A, C already well support the model in Fig. 5.

      (Reviewing Editor) I agree with Reviewer 2. The first paragraph in the section "MPIase serves as the TAT signal receptor" runs very long and the clarity of the descriptions on Fig. 4B could be further improved. Fig. 4A, C would sufficiently support author's arguments. I recommend that authors consider these options for the final version.

      We appreciate the critical comments. In Fig. 4B, we aimed to show that the amount of membrane-targeted TorA-GFP would increase due to the overproduction of MPIase caused by TatABC. At the same time, TorA-GFP translocation was also stimulated. However, since the translocated TorA-GFP was recovered in the same fractions as the cytosolic TorA-GFP, interpreting the results would be complicated. Therefore, we deleted Fig. 4B, as suggested by the reviewer and editor. The corresponding text and the right-hand side of Fig. S9 were also deleted.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      This study uses high-throughput bacterial cell-surface display to identify LC3B-interacting peptides in the human proteome. The screen is unbiased, and this type of assay has not previously been used for selecting LC3B-interacting peptides. The screen was done with a library of 500,000 peptides, and they ended up with 427 peptides that they scored as high-confidence LC3B binders. The experiments performed are solid, and data are analyzed using well-documented methods and statistics.

      The aim of the authors was to isolate LC3B-interacting peptides from the human proteome, and the screen succeeded in doing so. The selected set of peptides included several previously reported LIR motifs, but also many novel LC3B binding peptides that either contained or did not contain the canonical core LIR motif [WFY]xx[LVI].

      Another aim was to identify binding determinants important for the LC3B interaction, and they made an interesting sequence logo based on selected LIR-containing peptides. However, this study does not really extend our knowledge related to binding determinants essential for LIR motifs in LC3B binding. They basically verify known characteristics, including the importance of varied types of electrostatic interactions supporting the docking of the core LIR into the LDS of LC3B.

      Strengths:

      The approach used here (high-throughput bacterial-surface-display) is new. The screen is unbiased, and the fact that peptides are directly tested for LC3B binding may facilitate the discovery of non-canonical LIR motifs. The screen appears to be highly selective and manages to distinguish between peptides that interact with LC3B and peptides that do not interact.

      Weaknesses:

      It is a limitation that no proteins are analyzed in this study. Further work is therefore needed to verify that identified LIR motifs are functional in full-length proteins and in cells.

      Reviewer #2 (Public review):

      Summary:

      To discover peptides that interact with autophagy-related protein LC3B and profile the key binding determinants, the authors screened a library of ~500,000 36-residue peptides derived from the human proteome using bacterial cell-surface display. Analysis of the screening data revealed exceptions to the reported LIR motif and a strong preference for negatively charged residues adjacent to the LIR.

      These results support a refinement of the LIR motif definition and expand the network of candidate LC3B interaction partners.

      Strengths:

      High-throughput approach.

      Weaknesses:

      Lack of in vitro data and molecular dynamics simulations.

      Reviewer #3 (Public review):

      Summary:

      The LC3 family of proteins, which includes LC3B, are ubiquitin-like proteins that are covalently linked to phosphatidylethanolamine in the expanding autophagosomal membrane during autophagy. LC3 family members bind to short sequences of amino acids that reside within dynamic regions in a wide variety of proteins. These sequences, termed LC3 Interacting Regions (LIRs), were initially thought to function primarily to link LIR-containing autophagy cargo receptors to LC3 family members to help facilitate their capture during autophagy. However, the functional importance of LIRs in autophagy has broadened to include more general functions in autophagy as well. While a general consensus for LIR sequences has been described as [FWY]0-X1-X2-[LVI]3, recent work has suggested that additional sequences outside of the canonical LIR sequence can bind LC3 family members and play important roles in autophagy. In this manuscript by Kosmatka et al, the authors perform a high-throughput screen using bacterial surface display coupled with fluorescence-associated cell sorting to identify which human sequences can bind to LC3B. They identify a variety of peptides capable of binding LC3B, including peptides from proteins that have not previously been described as LC3B-binding proteins. The results from the bacterial surface display were then used to guide sequence analysis, mutational analysis, and structural studies to further characterize the range of LIR sequences that are capable of binding LC3B. Taken together, this work adds to the growing knowledge of how LIR sequences interact with LC3 family members and demonstrates which amino acids both inside and outside of the LIR sequence aid in binding. This work also identifies new potential LC3 binding proteins, which may play unknown roles in autophagy regulation. Lastly, this work reinforces the importance of alternative LIR sequences such as the [WFY]0-X1-X2-[WFY]3 sequence, which the authors have dubbed the LIR+ sequence.

      Strengths:

      The manuscript uses a robust approach to identify and characterize different peptide sequences that can interact with LC3B. They validate a large number of sequences using biolayer interferometry (BLI) and attempt to correlate different amino acids with their binding affinity for LC3B. The large number of LC3B binding sequences and their dissociation constants adds significant new information to the field that will help others understand what sequences can bind to LC3B. The authors are also very careful to accurately report on their data and not overly interpret their findings.

      Weaknesses:

      After the authors identify proteins from their bacterial display assay, the remainder of the manuscript is focused on characterizing the different types of sequences that are identified in addition to validating the LC3B-LIR interactions using biochemical approaches, including BLI and X-ray crystallography. However, it's not entirely clear if the screen identified novel LC3B binders that interact with LC3B in cells. While I acknowledge that the focus of the manuscript is on the characterization of LIR sequences that can bind LC3B, it seems like a missed opportunity not to validate a few of the novel LC3B binders in vivo. This may result in the demonstration of novel binders of LC3B in cells and may further demonstrate the strength of this approach for identifying LC3 family member binding partners. Therefore, it would be helpful to look at a few proteins identified in the HC set that have not previously been identified as LC3B binders in cells to determine if they CO-IP with LC3B or interact with LC3B using a different approach.

      The reviewers appreciated the contribution of our screen and our biochemical analyses and indicated there would be additional value in performing follow-up studies in cells to investigate the functional relevance of interactions we detected. We agree that such work will be important, but it is beyond the scope of our current study. We expect the data and analyses included in this paper, and the lists of peptide binders that we identified, will inspire such future efforts.

      We appreciate the reviewers’ careful reading of our manuscript, and we have revised the text and figures to improve the clarity and presentation of the data in accordance with their recommendations.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      Main comments:

      (1) In the abstract, the authors correctly conclude in the final sentence: "our results refine the LIR motif definition and expand the network of candidate LC3B interaction partners", but I disagree that their study "highlights how mutations at the LC3B-LIR interface can modulate affinity and specificity". They probably refer to the data in Figure 5, where they found that some peptides were positively affected by a mutation of the LDS in LC3B. This is interesting, but four peptides are listed in Figure 5B, and for these peptides, no experimental data are included to verify that their interactions with LC3B are LIR-LDS interactions. LIR-mutated peptides are, for instance, not tested. Therefore, it is possible that these interactions are not LIR-LDS interactions but depend on another binding surface in LC3B than LDS.

      Although LIR-mutated peptides were not tested in the experiments reported in Figure 5B, the LIR docking site (LDS) mutations F52A/L53A change the peptide-LC3B affinity. This suggests that the LDS is involved in the binding interaction, even if the interaction is not with a LIR motif. We have changed the statement to “highlight how mutations at the LIR docking site can modulate affinity and specificity,” to be more explicit.

      (2) Another text line in the abstract is that their study "revealed exceptions to the reported LIR motif and a strong preference for negatively charged residues adjacent to the LIR", and I find this text line a bit misleading. Yes, their structural data for the BLM peptide nicely shows the importance of electrostatic interactions, and R70 in LC3B binds to an E in the +1 position. This is different from several other reported LIR-LDS structures where R70 in LC3B binds to an acidic +7 residue in the LIR motif. However, R70 is conserved in all human ATG8s (R67 in GABARAP) and in many reported ATG8-LIR structures found to interact with an E in the +1 position, exactly as shown for the LC3B-BLM structure shown in Figure 3. The presented structure is therefore a very typical example rather than an exception to previously reported LIR motifs. The authors also select peptides with a so-called LIR+ motif, but this is a previously reported variant, and the alphafold model for the CTSL2 peptide in Figure 4 suggests a quite normal LIR-LDS interaction, except that W is docked into pocket 2.

      While the structural analysis of the BLM peptide bound to LC3B supports the importance of electrostatic interactions, it is not the primary basis for the statement regarding a “strong preference for negatively charged residues adjacent to the LIR.” Rather, this conclusion results from the sequence features enriched across the selected peptides in the HC-set, which revealed a consistent enrichment of negatively charged residues flanking the core motif and in the +4 position.

      With respect to the statement that the study “revealed exceptions to the reported LIR motif,” the intent was not to suggest that these interactions are unprecedented in the literature, but rather that we expanded the number of known exceptions to the most canonically defined LIR motif ([FWY]xx[LVI]). We do not claim these are unprecedented; we cite prior examples of exceptions in the text (Li 2018, Knævelsrud 2013, Chatzichristofi 2023). To avoid confusion, we revised the abstract to state that the study “revealed exceptions to the canonical LIR motif ([FWY]xx[LVI]).”

      (3) A limitation related to the search for binding determinants can be that the screen is only performed with LC3B. The impact of several determinants beyond the core LIR is known to be ATG8 specific. For instance, LC3-specific R10 and R11 are known to form electrostatic interactions with acidic residues in positions -2, -3, and -4 relative to core LIR, and the -3 and -4 positions can be a determinant for LC3 binding (Rogov et al, 2023; Autophagy Rep. 2: 2188523). Here, the authors made a consensus peptide based on the sequence logo derived from HC-set (Figure 3C). It is interesting that this peptide had a very high affinity for LC3B (0,1 µM) that was found to depend on the D in position -3. In the sequence logo shown in Figure 3A, D, and E are strongly favored in position -3, but position -4 is not included in the logo. Are acidic residues similarly enriched in the -4 position?

      The high affinity of the consensus peptide for LC3B is not dependent on the D in position -3. The peptides pCONS<sub>W-Nterm-S</sub> (EEDDDDEDWEILDIDEDEDGSGNEFYE) and pCONS<sub>W-Nterm-S-D-A</sub>(EEDDDAEDWEILDIDEDEDGSGNEFYE), where D in position -3 is mutated to A, have the same affinity (0.12 µM). The truncated peptide, pCONS<sub>W-Nterm-L</sub> (EDWEILDIDEDEDGSGNEFYE), which lacks position -3, has a weaker affinity of 0.66 ± 0.1 µM. These results illustrate that the flanking acidic residues, rather than specifically D in position -3, contribute to affinity (Figure 3C, Supplementary Table 3). The logo corresponding to the entire consensus peptide is shown in Supplementary Figure 5A. Acidic residues are not as enriched in the -4 position as they are in positions -1 through -3, although D is still the predominant residue in position -4 and is thus present in the consensus peptide.

      Extending this type of screen and analysis to other ATG8 family members has the potential to illuminate interesting paralog-specific differences.

      (4) Will the full list of peptides in the HC-set be included in a final manuscript? This is a very interesting set of peptides for scientists interested in LC3B-interacting proteins, and this includes those interested in noncanonical LIR interactions.

      Yes, all Supplementary Files (1-5) are available at Zenodo (10.5281/zenodo.17943925). Supplementary File 4 contains all of the peptides that were enriched through the sixth sort, and those peptides where “Average Z-score Across Sorts 4-6” is greater than or equal to (≥) 1.70 correspond to the full list of peptides in the HC-set.

      Minor comments:

      (5) When reading the result section, it is confusing that the bacterial membrane protein is named "circularly permuted OmpX" in the text on page 2, and "eCPX" in the figure legend. I suggest including both names in at least one place, as done in the methods section.

      We changed the text on page 2 to use the full name, which is “enhanced circularly permuted OmpX (eCPX)”, to address the confusion.

      (6) Figure S3A: The list of 10 peptides in the input library that have a KD in the LIRcentral database includes 7 with a KD below 5 µm (if I am correct), but is said to be 6 in the text on page 3.

      We corrected the text on page 3 to 7 peptides.

      (7) Error in the text. Data for the BLM peptide is shown in Figure 2B, but replaced by MAP1B in the text on page 3.

      We tested four peptides reported to co-immunoprecipitate with LC3B without an experimentally validated LIR motif (MAP1B<sup>823-858</sup>, ATG4A<sup>363-398</sup>, SCYL1<sup>640-675</sup>, and HEAT3<sup>377-412</sup>). Of these four, binding of three (ATG4A<sup>363-398</sup>, SCYL1<sup>640-675</sup>, and HEAT3<sup>377-412</sup>) is illustrated in Figure 2B, in addition to BLM<sup>552-587</sup>, which has not been previously reported to co-IP with LC3B. We added a note that not all curves are shown. Dissociation constants for these 5 peptides are included in Supplementary Table 1.

      Reviewer #2 (Recommendations for the authors):

      Human MAP1LC3B (LC3B) binds proteins involved in autophagy and other cellular processes using a short linear motif known as the LC3-interacting region (LIR).

      To discover peptides that interact with LC3B and profile the key binding determinants, the authors screened a library of ~500,000 36-residue peptides derived from the human proteome using bacterial cell-surface display. Analysis of the screening data, coupled with structural studies and site-directed mutagenesis, revealed exceptions to the reported LIR motif and a strong preference for negatively charged residues adjacent to the LIR.

      The authors also suggest that mutations in LC3B, shown to abrogate binding of LIR-containing peptides, instead alter LC3B binding specificity, leading to enhanced binding of some LIR-containing sequences.

      This is an interesting study, well structured, with solid data.

      My major concern is that the conclusion about the effect of known LC3B mutations on the binding of LIR-containing proteins is not strongly supported by the presented data. Did the authors try molecular dynamics simulations in such LC3B mutations to examine if F52A/L53A substitutions create alternative hydrophobic interfaces that modulate LIR motif peptide binding in a sequence-dependent manner?

      Figure 5C includes data that demonstrate that mutations to the LIR docking site (F52A, L53A) change the binding affinity of several peptides. Our structural analysis of the F52A/L53A LC3B mutants using ChimeraX (Figure 5A) provides a model for the changes in the hydrophobic pockets and a possible explanation for how these mutations introduce altered hydrophobic contacts and sequence specificity at the LDS. It would be challenging to exhaustively sample binding modes for peptides with different sequences using MD, which is best suited for exploring local minima. We do not claim to have a detailed structural explanation for the observed changes in binding specificity.

      Additionally, in vitro cellular data on the expression and localization of some of their strongest LC3B binding proteins (and their relevant novel residue mutations) would be useful.

      Assessing the expression and localization of our strongest LC3B-binding proteins and testing the effects of novel residue mutations in cells would be a valuable follow-up to further explore the implications of our findings. However, these experiments are beyond the scope of the current study, which focuses on high-throughput characterization of LC3B binding determinants using biochemical methods. We close the paper with a statement highlighting this as a promising direction for future investigation.

      Finally, the suggested refinement of the LIR motif sequence is not easily identifiable in the main text.

      We added a clause to clarify this in the Discussion: “Although a small number of LC3B-binding peptides bearing this LIR+ motif have been reported (~1% of cataloged hAtg8-binding peptides) (Li et al., 2018; Chatzichristofi et al., 2023), their prevalence appears underappreciated given their relatively high frequency in the HC-set (Supplementary Figure 10), leading to the refined motif [FWY]xx[LVIFWY].”

      Reviewer #3 (Recommendations for the authors):

      Please find my specific comments below.

      (1) The authors identify a large number of peptides from their screen, including several strong binders as shown in Figure 2C, that appear to bind LC3B but are from proteins that have not been previously annotated as LC3B binders in cells. Therefore, it would be helpful to validate whether some of these proteins are indeed LC3B binders in cells using CO-IPs or another related technique. This would significantly strengthen the manuscript, further validate their approach for characterizing LIR LC3B binding interactions, and demonstrate novel potential autophagy regulators.

      Validating candidate LC3B binders in cells using co-immunoprecipitation or related techniques will be a valuable follow-up and could provide important insight into novel autophagy regulators. Such experiments are beyond the scope of the current manuscript, which focuses on the high-throughput characterization of LC3B binding determinants in vitro. We mention this in the discussion as a promising avenue for future investigation.

      (2) In Figure 2C, there are two proteins that have high mean-Z scores but no detectable binding to LC3B (top right quadrant). It would be helpful for the authors to acknowledge this and speculate on why binders are isolated but cannot have detectable binding. Is this expected for a screen of this size? Is this below the non-specific binding expected or above? 

      Some apparent false-positive binders may have been isolated and exhibit high mean Z-scores due to avidity effects from the pre-tetramerized LC3B used in the bacterial display screen. Binding was validated using monomeric LC3B in BLI experiments, which eliminates these multivalent effects. Consequently, weak interactions stabilized by LC3B tetramerization that enrich in the bacterial display assay may not be detectable at the monomeric LC3B concentrations tested in BLI. Given the differences in multimerization between the screening and validation assays, as well as the large size of the library, both false positives and false negatives are expected. We added a comment about the apparent false positives to section Strongly enriched peptides include novel candidate LC3B interactors.

      (3) In Figure 2C, it says four peptides are colored as in 1C, but I can only see three colored that way, and the yellow one is very faint and hard to see.

      We corrected the text in Figure 2C to three peptides and have darkened the yellow point for easier visualization.

      (4) The authors determine the crystal structure of a peptide from BLM bound to LC3B. However, no electron density is shown in the manuscript. Therefore, it is unclear how ordered the side chains are that are shown, including for D564-D566. The authors should include an electron density omit map for the BLM peptide so that readers can accurately interpret how ordered each side chain is in the peptide.

      Supplementary Figure 9 shows an ensemble of conformations consistent with the diffraction data, as well as an electron density omit map. Data to support visualization of the electron density for the structure is included with the PDB deposition (structure 9p3e).

      (5) In Figure 3C, the authors include numbers in the bar graph. What are the numbers that are included? Is this the mean Kd value? If so, the numbers may be misleading without a second significant figure since some values of 0.1 are far away from 0.2, while others are very close to 0.2. In addition, if these values are the Kd values, it would be helpful to include these values in all other bar graphs throughout the manuscript, including Figures 4A and 5C.

      The values reported are the mean K<sub>D</sub> values, in micromolar, which is now indicated in the legend of Figure 3C; we also added a second significant figure. The mean K<sub>D</sub> values have also been included for the bar graphs in Figures 4A and 5C.

      (6) On page 7, the authors state that "we found strong evidence for enrichment of LIR sequences, but not for these closely related motifs, indicating that whereas such LIR-related motifs may support binding in some sequence contexts, they are not sufficiently strong binding determinants to be enriched in our screen". I found this statement to be unclear. Do the authors mean that while LIR sequences were strongly enriched in the HC-set, LIR+ sequences were not? This statement should be clarified.

      The statement on page 7 is in reference to Supplementary Figure 10, which shows that peptides containing the canonical LIR [FWY]xx[LVI] are enriched in the HC-set relative to their presence in the input library. In contrast, peptides containing LIR-related motifs ([WFY]xx[WFY], [LVI]xx[FWY], and [LVI]xx[LVI]) are not strongly enriched in the HC-set relative to their presence in the input library. We clarified this statement to read “We found strong evidence that canonical LIR motifs ([FWY]xx[LVI]) are enriched in the HC-set relative to their frequency in the input library, whereas LIR-related motifs ([WFY]xx[WFY], [LVI]xx[FWY], [LVI]xx[LVI]) are not (Supplementary Figure 10), indicating that although LIR-related motifs can support LC3B binding in certain sequence contexts, they are not sufficiently strong determinants to drive enrichment in our screen.”

      (7) How different is the alphafold prediction of the LIR+ engaging with LC3 compared to the LIR LC3 interaction? Are they largely similar or are there unique features to each? Does the presence of a second large aromatic residue push the backbone of the peptide farther away from the hydrophobic binding pocket?

      To address this, we predicted structures of the LIR+ motif of CTSL2 (EEDWEVFDPY) and a canonical LIR version (EEDWEVIDPY) to LC3B using AlphaFold3. Structural superposition shows that LC3B adopts a conserved conformation in both complexes (Cα RMSD 1.55 Å). The backbones of the core LIR / LIR+ motif also align closely to each other (1.39 Å RMSD), indicating preservation of the canonical binding mode. The LIR+ peptide exhibits a modest increase (~2 Å) in Cα distance between the aromatic residue Phe and LC3B F52 in HP2 compared to the corresponding Ile in the canonical LIR (8.3 Å vs 6.3 Å). Thus, a subtle backbone repositioning is predicted to accommodate the aromatic side chain. We added a comment about this to the section Highly enriched peptides lacking a canonical LIR can bind LC3B.

    1. Author response:

      Reviewer #1 (Public review):

      Summary:

      The authors present the most comprehensive phylogenomic study of free-living kinetoplastids to date, including newly generated transcriptomic data from 11 species. This dataset provides a solid foundation for future comparative evolutionary studies of kinetoplastids, a group that includes important human pathogens such as Trypanosoma brucei.

      Strengths:

      The study is clearly written, and the analyses are thoroughly described, well documented, and reproducible. The phylogenomic dataset comprises 444 proteins, which is larger than those used in many comparable phylogenomic studies. The main strength of the study is the substantially improved taxon sampling of neobodonids, which provides a much stronger framework for resolving evolutionary relationships among free-living kinetoplastids.

      Weaknesses:

      The phylogenomic analysis is based on a newly assembled dataset comprising 444 single-copy orthogroups. Using an established phylogenomic dataset, expanded to include the newly studied species, to confirm the inferred relationships would provide additional support for the robustness of the recovered topology.

      We thank the reviewer for their comments on our work. We appreciate the suggestion to confirm the topology that we recovered by using an established phylogenomic dataset. We note that we did not choose to use an established dataset for the main phylogenomic analysis, as we found that free-living kinetoplastid orthologs are systematically excluded from commonly used “universal pan-eukaryotic” datasets (e.g., Fig. S4), despite the fact that we were able to identify sufficient orthologous proteins to robustly reconstruct interspecies relationships among euglenozoans. In our revised manuscript, we will implement the reviewer’s suggestion by comparing our orthogroup set with commonly used pan-eukaryotic orthogroup sets.

      Reviewer #2 (Public review):

      Summary:

      This is a highly competent and very throough phylogenomic study of the position of neobodonids within the Kinetoplastid phylogeny. The addition of new transcriptomic data for diverse neobodonids allows their relationships to be better understood, leading to convincing changes to neobodonid taxonomy.

      Strengths:

      The generation of transcriptomic data produces more phylogenetic characters than ever before from several, diverse neobodonid lineages. This represents a substantial increase in the data available for this relatively unstudied group. The methodology used to define the character set and then estimate the phylogeny is conventional, very thoroughly described and expertly executed. The phylogeny is highly robust, and we can be very confident of the result.

      Weaknesses:

      These changes to neobodonid taxonomy, or essentially the discovery that some 'neobodonids' actually represent distinct lineages at the base of the Metakinetoplastida, are not surprising. So undersampled are the Kinetoplastida, both in terms of molecular markers and phyletic diversity, that an investment in sampling on this scale is always likely to bring about changes. The significance of these changes is not immediately apparent. Since they do not concern the Eubodonidae, they have no implications for the trypanosomatids and the new Metakinetoplastid lineages are very distant from the origins of parasitism, such that comments on "preadaptations for disease" are not compelling.

      We agree that comments and discussion on how our study may shed light on the preadaptations of trypanosomatids to parasitism were excessive. We were influenced by prior studies of free-living metakinetoplastids, which highlighted their importance and applied value in the context of understanding evolution of parasitism in kinetoplastids (Deschamps et al., 2011; Dolezel et al., 2000; Flegontova et al., 2017). In our revised manuscript, we will remove/shorten the corresponding parts of discussion and results, and place more emphasis on the relevance of our study to understand the multiple origins of parasitism in metakinetoplastids, not just trypanosomatids.

      The datasets published in our study can be used in the future to investigate, for example, how gene repertoire of trypanosomatids differs from the free-living species, or how specific gene families evolved, and whether their diversification/origin predated the origin of the largest parasitic clade. We acknowledge that the data from the closest free-living relative of trypanosomatids that was available before our study is already extremely valuable, and that our datasets would be of most use for reconstructing relatively ancient preadaptations.

      Reviewer #3 (Public review):

      Summary:

      The manuscript by Zavadska et al. presents a phylogenomic study focused on the relationships among metakinetoplastids, specifically addressing the question whether Neobodonida are monophyletic. The authors collected eleven kinetoplastid strains affiliated with five out of six neobodonid clades identified in previous studies and sequenced their transcriptomes. These data along with SRAs available from public databases were processed via assembly, annotation and decontamination. The final dataset, representing all (non-trypanosomatid) kinetoplastids with genome and/or transcriptome data available as well as selected trypanosomatids and discoban outgroups, was used for protein orthology inference and identification of single-copy orthologs present in the majority of taxa, followed by phylogenetic analysis in maximum likelihood and Bayesian frameworks.

      Strengths:

      I find the new data and resulting phylogenetic reconstruction valuable and interesting, particularly given the paucity of genomic/transcriptomic data from free-living kinetoplastids. The study is well-designed methodologically, and the main finding (paraphyly of Neobodonida) appears indisputable, considering the provided phylogenimic evidence. Following best practices, the authors shared their primary data, scripts, and files resulting from the conducted analyses.

      Weaknesses:

      Several aspects of the presentation and interpretation would benefit from revision. In particular, the composition of the neobodonid lineages central to the study is insufficiently explained, and an 18S rRNA gene-based tree showing these lineages and the placement of the newly analysed strains would substantially improve the clarity of the study. The Introduction would also benefit from a more concise and better-structured account of previous phylogenetic evidence and a clearer explanation of the broader biological significance of kinetoplastids, while the Methods could be streamlined by removing redundant information and presenting some details in tables. Finally, the rationale for including the electron microscopy images in the supplement should be clarified, as these are currently not discussed in the text and represent only a single studied strain.

      We thank the reviewer for their suggestions on how our manuscript could be improved. Regarding the selection of species, our study followed a common procedure in protistology: we attempted to isolate, culture and sequence as many free-living kinetoplastids as possible, and the resulting manuscript includes all the cases in which we were successful. We appreciate the reviewer’s suggestion of including an 18S rRNA gene tree, which we will implement in our revised manuscript. We will revise the introduction to improve the presentation of previous phylogenetic evidence in metakinetoplastids and to provide a more clear explanation of their broader significance. We also plan to reduce redundant information in the Methods and relocate information on strains and culturing conditions to tables.

      Electron microscopy images in the Supplement display the ultrastructure of an isolate from the 1D clade. They were included because the information on morphology of this clade remains scarce in comparison to other clades; thus, we added these images because we believe they could be useful for the community. We intend to clarify this in our revised manuscript.

      References

      Deschamps P, Lara E, Marande W, López-García P, Ekelund F, Moreira D (2011) Phylogenomic analysis of kinetoplastids supports that trypanosomatids arose from within bodonids Mol Biol Evol 28:53-58 https://doi.org/10.1093/molbev/msq289

      Dolezel D, Jirků M, Maslov DA, Lukes J (2000) Phylogeny of the bodonid flagellates (Kinetoplastida) based on small-subunit rRNA gene sequences Int J Syst Evol Microbiol 50:1943-1951 https://doi.org/10.1099/00207713-50-5-1943

      Flegontova O, Flegontov P, Malviya S, Poulain J, de Vargas C, Bowler C, Lukeš J, Horák A (2018) Neobodonids are dominant kinetoplastids in the global ocean Environ Microbiol 20:878-889 https://doi.org/10.1111/1462-2920.14034

    1. Author response:

      We thank the editors and both reviewers for their careful evaluation and for recognizing the value of examining the wider behavioral repertoire after aversive learning. Our aim is to follow what an individual does after danger and intervention, rather than infer recovery from a decline in one defensive response. The reviews identify where the present computational account needs stronger connections to observed behavior, experimental comparisons, and subsequent outcomes. We are preparing a substantive revision addressing these issues. This provisional response outlines the work planned; it does not report completed revisions or new findings.

      Response to Reviewer 1:

      (1) Four-state versus eight-state resolution

      We agree that the better held-out performance of K=8 must be central to the interpretation. K=4 is a theory-guided coarse descriptive scale, not the predictively optimal model or evidence that behavior contains exactly four natural states. We will explain this distinction more clearly and show what the additional states resolve, particularly within the low-event-output configurations. Comparisons of experimental change at both resolutions will help establish which conclusions depend on the coarse scale and which persist at finer resolution. We will not treat agreement within one emission representation as proof of a universal four-mode organization.

      (2) Interpreting Quiescent

      The reviewer's concern is important: Quiescent denotes low vocal and lever output, not an absence of freezing, a safe internal state, or successful recovery. Likewise, a decline in Fear/Danger occupancy does not establish that defensive responding has disappeared. We will present raw freezing, vocalizations, and lever pressing alongside state occupancy, with experimental groups distinguished. The higher-resolution subdivision of count-silent observations will make differences in freezing more visible. These comparisons can describe residual defensive behavior, but cannot by themselves determine whether quietness reflects rest, inhibition, anxiety, or another internal condition. We will retain these alternatives explicitly rather than infer safety from silence.

      (3) The ethological meaning of functional recovery

      We appreciate the distinction between returning to a previously rewarded action and adapting appropriately after danger. Resuming food-directed responding in the original setting is one task-specific outcome, not a necessary or sufficient definition of recovery. Avoiding that location or pursuing resources elsewhere could also be adaptive. The present task does not offer the alternatives needed to distinguish those possibilities. We will therefore frame the measured repertoire as an assay of context-dependent functional change, not a universal standard to which animals should return. The translational question remains whether an intervention changes the broader organization of behavior, but judging successful adaptation also requires evidence about the opportunities and risks available to the individual. Pooled state percentages will not be presented as normal or desirable recovery targets.

      (4) Shock versus no-shock comparisons

      We will report direct comparisons between shock and no-shock animals for the raw channels and inferred occupancies, including changes over conditioning. This will allow the reader to distinguish changes associated with aversive conditioning from changes shared with unshocked animals, such as familiarization or declining novelty. The revision will also separate extinction from time-matched exposure and present renewal by group rather than pooling treatment histories. Comparisons will use rats as the experimental units, report uncertainty, and make differences in observation coverage explicit.

      (5) Connecting post-extinction behavior to later outcomes

      We will examine whether the available paired records permit associations between post-extinction configurations and subsequent defensive responding, alongside the corresponding raw behavioral measures. These analyses will respect test chronology and intervening treatment. They will be identified as retrospective and exploratory, not as independent validation of individual prediction: the current shared representation was fitted using the full dataset. We will report limited sample size, missing modalities, or insufficient variation when these prevent a question from being estimated. A failure to establish an association will not be treated as evidence that no biological relationship exists. If these data cannot support a prognostic claim, we will state that limitation and identify the prospective test needed.

      Response to Reviewer 2:

      (1) Emission-family dependence

      We agree that the count-native sensitivities materially limit the interpretation. Alternative emission models also retain temporal dependence; their disagreement with the Gaussian model therefore does not show that temporal modeling uniquely produces the four labels, or that the Gaussian account is biologically privileged. We will explain the count transformation and scaling, and distinguish numerical fit eligibility from recovery of the complete behavioral-label configuration. We will also make clearer which findings are conditional on the Gaussian representation. Stable classification within that representation is useful evidence for a reproducible reference, but is not evidence for an emission-family-invariant taxonomy.

      (2) Generalizability and independent transfer

      All animals were male and the experiments came from one laboratory. Recurrence across related study datasets, including a retest of the same animals, does not substitute for transfer to independent subjects or settings. We will strengthen the prospective validation roadmap: fix preprocessing and model parameters before testing independent animals, include both sexes and an independent setting, measure individual baselines, and evaluate later outcomes without using those outcomes to fit the representation. Direct exploration measures and tests of instrumental outcome sensitivity would provide independent checks on functional interpretation. This is a proposed validation design, not generalization demonstrated by the present study.

      (3) The appropriate level of abstraction

      The revision will distinguish predictive resolution from interpretive scale throughout, as described in our response to Reviewer 1. K=8's advantage will remain explicit. The relevant question for K=4 is whether it offers an informative coarse summary of experimental change, not whether it wins model selection. Conclusions that require a finer distinction will be presented at that resolution rather than forced into four categories.

      (4) Vocal and instrumental labels

      We agree that 50-kHz calls are a context-sensitive vocal measure, not a direct observation of exploration or a unique indicator of positive affect. We will qualify the Exploratory label consistently by its measured emission pattern. Similarly, food-reinforced lever pressing establishes instrumental responding in this task; without outcome-sensitivity tests it does not establish goal-directed rather than habitual control in the technical sense. The labels will describe observed behavioral configurations, not subjective feelings, neural mechanisms, or independently validated motivational states. A simplified behavior-to-model mapping will make these distinctions easier to follow.

      Together, these revisions will place the raw behavior and experimental contrasts alongside the model, clarify the limits of the labels and recovery interpretation, and make the next validation steps concrete. The intended contribution is a reproducible framework for describing history-dependent changes in the measured repertoire and testing their functional relevance, without equating a model category with recovery or claiming individualized prognosis that the present evidence has not established.

    1. Author response:

      We thank the reviewers for their thoughtful comments. We will address the substantive concerns by broadening our evaluation to additional 3D datasets, strengthening comparisons against competitive baselines, and systematically ablating Penumbria's architectural components. We are confident that these experiments will establish Penumbria as a state-of-the-art 3D instance-segmentation method across a substantially broader range of segmentation challenges in biological imaging, without the pronounced dataset-specific failure modes observed for several competing approaches.

      Scope and dataset difficulty.

      We will expand our benchmark to include additional 3D datasets spanning nuclei, whole cells, and organelles. However, we do not accept two assertions made in the review: first, that nuclear segmentation is inherently easier than whole-cell segmentation; and second, that our existing datasets contain “mostly convex-ish and well-separated” objects (which we address separately below). Parhyale illustrates why the first assertion is unwarranted: despite being a nuclear-label dataset, its nuclei are extremely densely packed, with boundaries frequently so poorly distinguishable that even manual identification of individual instances is challenging. Historically, StarDist-3D has been the clear state-of-the-art method on this dataset, with little effective competition, whereas Penumbria matches its performance without imposing a star-convex shape prior. Conversely, the PlantSeg study reported an Adapted Rand error of only 0.075 on 3D cell-wall-labelled leaf tissue and approximately 90–99% correctly segmented whole cells across six leaf-surface specimens [1].

      Segmentation difficulty is an empirical property, not a consequence of what is being segmented or how it is stained.

      Diversity in biological targets or staining modalities does not necessarily translate into diversity of segmentation challenges, let alone greater difficulty. Constructing a meaningful benchmark therefore requires expert judgment in selecting datasets spanning challenging conditions, including irregular morphology, crowding, poor contrast, anisotropy, and imaging artifacts, informed by previous benchmarking results. The same empirical standard must apply to the reviewers' characterization of our datasets as “mostly convex-ish and well-separated.” Neither characterization is supported by quantitative evidence or relevant citations, and even if both were established, they would not by themselves demonstrate that the datasets are easy to segment. We will therefore quantitatively characterize the datasets, including their morphology and crowding, and examine how these properties relate to segmentation performance across methods.

      Zero-shot generalization.

      We will evaluate Cellpose-SAM zero-shot across all datasets, using segmentation accuracy (SA) at IoU 0.5 below 0.30 as a deliberately permissive indicator of severe instance-segmentation failure. Even at this threshold, substantial merging or missed instances can make the output unsuitable for reliable instance-level quantitative analysis without extensive correction.

      Cell pose-SAM comparison and baselines.

      We appreciate that the reviewers have since acknowledged the baseline training configurations reported in our Supplementary Material, which specified that Cellpose-SAM was fine-tuned from pretrained weights, while StarDist-3D was trained from scratch. In retrospect, these details would have benefited from greater visibility in the main text, and we will move them there in the revision. We also identified an important omission in our Cellpose-SAM inference configuration. The Cellpose-SAM paper specifies 1,000 dynamics iterations, flow3D_smooth=2, and removal of masks below 1,000 pixels for its 3D experiments. These settings differ substantially from generic API defaults and materially improve performance on several of our datasets. We will therefore repeat the evaluation using the published 3D settings and transparently report both the original and corrected configurations, with the latter serving as the principal comparison where applicable.

      u-Segment3D.

      The reviewers recommend u-Segment3D because it “reports large improvements,” without specifying over which methods. Its comparisons with Cellpose involve earlier cyto models, not Cellpose-SAM, which was introduced nearly a year after u-Segment3D's original preprint. Moreover, u-Segment3D is a 2D-to-3D aggregation framework rather than an independent segmentation model. Its supplementary material reports dataset-specific gradient smoothing and a 200-voxel size filter, without documenting equivalent settings for its Cellpose 3D baseline. As our own experiments demonstrate, such settings can materially affect 3D accuracy. The reported improvements therefore do not establish competitiveness with a properly configured and fine-tuned Cellpose-SAM. We will instead prioritize StarDist-3D, micro-SAM, and a corrected Cellpose-SAM comparison, reporting all inference configurations transparently.

      Architectural testing.

      While distance-transform regression is an established technique, as acknowledged in our manuscript, Penumbria's principal methodological contributions lie in its architecture and the integration of its components. We will expand our ablations by removing key architectural elements individually and measuring the resulting changes in performance. These experiments will quantify the contribution of each element within the complete pipeline. We look forward to submitting the revised manuscript incorporating these improvements.

      (1) Wolny, A., Cerrone, L., Vijayan, A., Tofanelli, R., Barro, A. V., Louveaux, M., et al. (2020). Accurate and versatile 3D segmentation of plant tissues at cellular resolution. eLife, 9, e57613.

    1. Author response:

      Reviewer #1 (Public review):

      (1) The full-length conclusions rest on FD3-FD3 being the dominant domain contact. The water-interaction correction applies only to the disordered regions, so the folded domains retain standard Martini 3 behavior, which is known to overestimate protein association (e.g., Thomasen et al., J. Chem. Theory Comput. 2022). The contact maps are also normalized per bead, which favors a small domain such as FD3. Please test whether FD3-FD3 dominance survives a folded-domain correction, and show raw contact counts next to the normalized maps. Without this test, and without experimental evidence that this domain self-associates, frame the FD3 result as a model prediction.

      We thank the reviewer for highlighting this important concern. We agree that the apparent prominence of FD3–FD3 interactions in the full-length simulations requires careful examination, particularly because the folded domains retain the standard Martini 3 protein–protein interaction strength whereas the water-interaction correction used in this study was applied to the disordered regions. We also agree that per-bead normalization may influence the apparent relative contributions of domains of different sizes.

      In the revised manuscript, we will examine the robustness of the FD3-centered interaction pattern to the treatment of folded-domain interactions. We will also report raw contact counts alongside the normalized contact maps and explicitly evaluate how domain size and normalization affect the relative contact frequencies.

      More generally, we agree that the simulations alone do not establish FD3 self-association as an experimentally validated property of HDAC6 condensates. We will therefore distinguish more clearly between simulation-derived predictions and experimentally established conclusions and will frame the proposed FD3-centered interaction network as a model prediction where appropriate.

      (2) The ligand-treated IDR1 slabs are single trajectories with no statistical uncertainty on the saturation concentrations or on the contact-difference maps. The full-length systems have three replicates; contact numbers are still rising at the end of several trajectories (Figure S9), and most differences between Nexturastat A and HPOB overlap within error. The wild-type controls also reverse the ligand ordering (Figs. S12, S14), which suggests that trajectory-to-trajectory variation may drive the domain-level differences. Please add independent replicas for the ligand comparisons, show convergence over consecutive time blocks, and report uncertainties on the difference maps. Claims should then be limited to the differences that are resolved.

      We agree that additional statistical characterization is required for the ligand-dependent comparisons. In particular, the current ligand-treated IDR1 slab simulations do not provide sufficient information about trajectory-to-trajectory variability, and differences between Nexturastat A and HPOB in the full-length simulations should not be interpreted without considering the uncertainty across independent trajectories.

      In the revised manuscript, we will rigorously assess the convergence and statistical robustness of the current simulations, including time-block analyses of the saturation concentrations and contact patterns. We will additionally perform independent replicate slab simulations to evaluate the robustness of the estimated saturation concentrations and interaction patterns. We will also increase the independent sampling of the full-length multichain systems to better characterize trajectory-to-trajectory variability and the robustness of the domain-level interaction patterns. Together, these analyses will allow us to provide uncertainty estimates and determine which ligand-dependent differences are reproducibly resolved.

      We will also reassess the differences attributed to Nexturastat A and HPOB in light of these uncertainties. Where the differences are not statistically resolved, we will refrain from assigning ligand-specific mechanistic interpretations and will revise the corresponding conclusions accordingly.

      (3) The Discussion presents the simulations as explaining why Nexturastat A suppresses HDAC6 condensation more strongly than HPOB. However, every full-length system assembles at a high protein concentration, and total contacts and morphologies are similar across conditions, so the simulations do not show suppression. The IDR-level and domain-level mechanisms are studied in separate systems, and ligand distribution and IDR1 contacts are not analyzed in the full-length assemblies, so the coupling of the two layers named in the title is not tested. Please add an analysis that bears on condensation propensity and on this coupling, or recast "explains" as "is consistent with" and revise the title and abstract accordingly.

      We agree that the current full-length simulations do not directly demonstrate suppression of condensation by either ligand. All full-length systems were simulated under conditions in which assemblies form, and similarities in the overall contact numbers and morphologies do not provide a direct measure of differences in saturation concentration or phase-separation propensity.

      We will therefore revise the title, Abstract, Results, and Discussion where necessary to avoid implying that the full-length simulations directly explain the experimentally observed suppression of HDAC6 condensation. Instead, we will describe the simulated interaction-network changes as being consistent with, or as providing a possible molecular basis for, the experimentally observed effects.

      We also agree that the coupling between the IDR-level and domain-level regulatory mechanisms needs to be more clearly established. We will extend the analysis of the full-length simulations to examine ligand distributions and interactions involving IDR1 and the folded domains and will assess whether conditional or correlated contact patterns provide quantitative evidence linking these interaction networks. If such analyses do not provide sufficient evidence for direct coupling, we will revise the terminology accordingly and describe the results as condition-dependent reorganization of multiple interaction networks rather than as a demonstrated coupled mechanism.

      (4) For phosphorylation, the IDR1 fragment is strongly basic, so a simple reduction of net charge could lower the saturation concentration without a position-specific contact node. The phosphoserine charge state used is also lower than expected at neutral pH. Moving the same charge to a distal serine, and testing the fully charged phosphoserine, would distinguish these readings. For the ligands, the coarse-grained models show only weak pocket engagement, lack a non-pocket control, have unvalidated nonbonded parameters, and are simulated at millimolar concentrations. The ligand-IDR1 mechanism could therefore reflect nonspecific association. Please add a non-pocket surface control, validate the ligand parameters, and relate the simulated concentrations to those of the motivating experiments.

      We thank the reviewer for raising these important points regarding the interpretation of both the phosphorylation- and ligand-dependent effects.

      For the phosphorylation-dependent mechanism, we would like to clarify that our simulations were motivated by prior experimental observations showing that phosphorylation at different serine residues of HDAC6 does not produce equivalent effects on phase separation. In particular, phosphorylation at S22 was found to have a pronounced effect on HDAC6 phase separation, whereas phosphorylation at the other tested serine sites did not show a comparable effect. These experimental observations argue against a simple model in which the effect of phosphorylation is determined solely by an increase in the overall negative charge of the protein, and instead indicate that S22 represents a site-specific regulatory position.

      Our simulations were therefore designed to explore the molecular basis of this experimentally established site specificity, rather than to establish S22 specificity from the simulations alone. In this context, the enhanced contacts involving the phosphorylated S22-containing region and positively charged segments of IDR1 provide a possible molecular explanation for why phosphorylation at this particular site can have a distinct effect on phase separation. We will clarify this experimental motivation and the scope of our interpretation in the revised manuscript, and will avoid implying that the simulations alone demonstrate the site specificity of S22 phosphorylation.

      We nevertheless agree that the representation of the phosphoserine charge is an important modeling consideration. We will examine the sensitivity of the phosphorylation-dependent results to the phosphoserine charge state and clarify the corresponding limitations of the coarse-grained representation in the revised manuscript.

      We also agree that the ligand simulations require a clearer assessment of specificity. In the revised manuscript, we will compare ligand contacts with the catalytic pocket to contacts with non-pocket regions of HDAC6 and further evaluate the extent of nonspecific protein association. We will also validate the physical reasonableness of the coarse-grained ligand parameterization, with particular attention to the nonbonded parameters relevant to ligand-protein interactions, and report the validation in the revised manuscript. We will explicitly state the limitations of using these models to infer binding specificity or affinity

      Finally, we will clarify the relationship between the ligand concentrations used in the simulations and those used in the motivating experiments. The high ligand concentrations used in the simulations were chosen to obtain sufficient sampling of ligand-protein encounters on accessible simulation timescales, and we will make clear that these simulations should not be interpreted as reproducing experimental binding equilibria at the corresponding concentrations.

      Reviewer #2 (Public review):

      When going through the manuscript, especially the result section, I sometimes found it challenging to distinguish what has already been reported experimentally (mostly from Lu et al., Nature Cancer) from what is newly learned from the simulations. I do appreciate that the authors mentioned which results reproduce experimental trends; however, this is often after all simulations. It may help if each subsection first briefly states the known experimental observation and then explains the specific question addressed by or new mechanisms learned by the simulation. For instance, experiments have shown that phosphorylation enhanced and ligand suppressed phase separation.

      We agree that the manuscript should more clearly separate the experimental observations reported previously from the questions addressed by the present simulations.

      In the revised manuscript, we will reorganize the relevant Results subsections so that each section first briefly states the pertinent experimental observation and then defines the specific mechanistic question addressed by the simulations. We will also distinguish more explicitly between trends reproduced by the simulations and hypotheses that emerge uniquely from the simulation analysis. This restructuring should make it clearer which conclusions are supported directly by prior experiments and which represent new mechanistic predictions of the present work.

      The authors directly used Automartini to generate the ligand parameters and then checked the contact fraction between the ligand and the pocket. Such analysis only tells whether the ligand visits the pocket but does not test either specificity or binding affinity, and therefore does not support the claim of ligand pocket recognition. The simulation concentration is also in the millimolar regime, probably much higher than the experimental range, so it's not surprising to see ~10% to 20% contact fraction. Considering that no native interactions are used to restrain the ligand-pocket interactions, I suspect the ligand might also have similar contacts to the other regions of HDAC. The authors might want to be careful about their discussions.

      We agree that observing contacts between the ligands and the catalytic pocket does not by itself establish specific recognition or binding affinity. The current coarse-grained simulations were designed primarily to examine how the presence of the inhibitors perturbs the protein interaction network rather than to calculate ligand-binding affinities.

      In response to this concern, we will analyze ligand interactions with non-pocket regions and compare these with the catalytic-pocket contacts, allowing us to better quantify the degree of preferential localization. We will also validate the physical reasonableness of the coarse-grained ligand parameterization, including the nonbonded parameters relevant to ligand-protein interactions, and report the validation and its limitations more explicitly in the revised manuscript.

      Throughout the manuscript, we will revise language implying that the coarse-grained simulations demonstrate specific ligand recognition or reproduce experimental binding affinities. We will also clarify the significance of the relatively high ligand concentrations used in the simulations and relate these conditions to the experimental concentrations.

      The claim regarding the IDR dimension might be problematic. It's still an open question whether a coarse-grained model, or even current all-atom force fields, can reliably resolve the effect of a single phosphorylation on IDR dimensions. I agree that all current results, including the error estimate, support that Rg do not change that much, but the authors might still want to be careful about such claim considering such small perturbation in the sequence.

      We appreciate this point and agree that the absence of a detectable change in radius of gyration in the present simulations should not be interpreted as evidence that a single phosphorylation cannot alter IDR dimensions more generally.

      We will provide appropriate uncertainty estimates and statistical comparisons for the single-chain conformational ensembles and revise the wording to state more narrowly that, within the resolution of the present Martini 3 simulations, we do not detect a substantial phosphorylation-dependent change in IDR1 dimensions. We will also acknowledge the limitations of current coarse-grained models in resolving subtle conformational effects associated with a single post-translational modification.

      The proposed electrostatic rewiring is based on the difference between the contact maps of WT and phosphorylation variant. It looks like the difference is relatively small to the contact probabilities. There is also no error estimation or pattern validation from multiple simulations. The authors might want to quantify the uncertainties of such patch-level relative changes by either checking some independent simulations or time-block variations.

      We agree that the relative changes visible in the phosphorylation-dependent contact maps need quantitative uncertainty estimates.

      In the revised manuscript, we will quantify the reproducibility of these contact changes using time-block analyses together with additional independent slab simulations, and provide uncertainty estimates for the difference maps. We will use these analyses to identify which phosphorylation-dependent contact changes are robust and will restrict the mechanistic interpretation to features that are reproducibly resolved.

      A similar comment applies to the claims on the charged-contact reorganization mechanism of two small inhibitors on LLLPS. Error estimates should be provided for these contacts when comparing different variant. In cases when errors are large (e.g. contact number with errors reported in Fig. 4K to N), statistical analysis (p-values) is needed to show the significance of the results.

      We agree that the same consideration applies to the comparison of the ligand-dependent interaction networks.

      We will report uncertainty estimates for the relevant contact observables and strengthen the statistical assessment using additional independent slab simulations together with expanded independent sampling of the full-length multichain systems. Statistical comparisons will be based on independent estimates, and where the variability is comparable to or greater than the apparent differences between conditions, we will explicitly report this and avoid assigning mechanistic significance to those differences.

      Regarding the proposed "phospho-S22-centered" contact network, I had some difficulty recognizing the specific regions discussed in Figures 2 and 3. It might be helpful to mark these regions directly on the contact maps. The authors may also wish to consider whether "S22-centered" is the most accurate description, or whether the observed changes are better described as involving a broader segment spanning several residues around S22. And since phosphorylation is introduced at S22, observing changes near S22 is not unexpected and may not be sufficient to establish phospho-S22-centered network.

      We appreciate this suggestion. We agree that describing the observed interaction changes as strictly "S22-centered" may be overly specific, because phosphorylation is introduced at S22 and the altered contacts involve a broader sequence region surrounding this residue.

      We will mark the relevant sequence regions directly on the contact maps to make these patterns easier to identify. We will also reconsider the terminology throughout the manuscript and, where more appropriate, describe the effect as a phosphorylation-responsive interaction region or network surrounding S22 rather than implying that S22 alone constitutes a discrete interaction node.

      Within the last result section, the authors argued that FD3 plays an important role in both phosphorylation- and ligand-regulated HDAC assembly. However, only contact-based analysis instead of saturation concentration was presented. I understand the substantial challenge of obtaining converged saturation concentration for such system with multiple domains, if so, the authors need to discuss such caveats.

      We agree that the full-length simulations provide information about the organization of the assembled state but do not directly determine the saturation concentration of full-length HDAC6. Given the size and complexity of the full-length system, obtaining converged coexistence concentrations would require substantially larger simulations and longer sampling than those performed here.

      We will make this distinction explicit in the revised manuscript and clarify that the full-length contact analysis addresses changes in the internal interaction network of the assembled state rather than directly measuring changes in phase-separation propensity.

      Though direct experimental evidence of such FD3-centered interaction network does not exist, the experimental paper did provide measurements for a couple domain-deletion constructs, including the deletion of the FD3 (BUZ) region. This might be worth discussing, considering the manuscript focuses on the role of FD3 region. In particular, deletion of the BUZ region did not appear to affect LLPS. This does not necessarily exclude a role for FD3 in phosphorylation- or ligand-dependent regulation. However, it may complicate the description of FD3 as the center of the condensate network. The authors might want to discuss how their model can be reconciled with these domain-deletion results and consider their corresponding conclusion.

      We appreciate the reviewer drawing attention to the previously reported BUZ/FD3 deletion experiments. We agree that the observation that deletion of the BUZ region does not abolish LLPS indicates that FD3 is not required for baseline phase separation.

      In the revised manuscript, we will discuss these experiments explicitly and will avoid describing FD3 as an obligatory center of the HDAC6 condensation network. Instead, we will discuss the possibility suggested by the simulations that FD3 contributes to the organization or regulation of interactions within the full-length assembly without being necessary for assembly itself. We will also clarify that this interpretation remains a model-derived hypothesis requiring experimental validation.

      Finally, the authors describe their mechanism as coupled networks. They might want to clarify the coupling they meant. If this refers to the coupling between different regions (e.g. S22 and FD3) or domains, they might want to consider more quantitive analysis, for instance by conditional/correlated contacts between domains. Changes in contact patterns at different conditions do not necessarily show the coupling between domains.

      We agree that condition-dependent changes in two interaction networks are not, by themselves, sufficient to demonstrate coupling between them.

      We will clarify what we mean by coupling and will examine whether conditional or correlated contact analyses in the full-length simulations provide quantitative evidence that changes involving one region or domain are associated with changes elsewhere in the interaction network. If these analyses do not support such a relationship, we will revise the terminology and describe the results more conservatively as coordinated or condition-dependent reorganization of multiple interaction networks.

      Reviewer #3 (Public review):

      (1) There are areas where statistical tests can improve the quantitative presentation of the work. Specifically, the difference in the IDR ensembles for the isolated chains should be assessed for statistical significance.

      We agree that the comparisons of the isolated-chain ensembles should include quantitative estimates of uncertainty and statistical support.

      In the revised manuscript, we will quantify the variability of the relevant conformational observables across independent simulations and perform appropriate statistical comparisons between the unmodified and phosphorylated IDR1 ensembles. We will use these results to refine the statement regarding the effect of phosphorylation on the single-chain dimensions and avoid interpreting differences that are not resolved within the uncertainty of the simulations.

      (2) There appears to be considerable finite-size effects in some of the slab simulations that may affect the conclusions. In particular, the chains along the long axis appear to be interacting across the periodic boundary. This can happen if the slab long axis is not long enough/if the ratio of dilute phase to dense phase is not large enough.

      We appreciate the reviewer raising this important issue. Interactions between the condensed slab and its periodic images could bias estimates of the dilute-phase concentration and therefore need to be explicitly evaluated.

      We will examine the trajectories and density profiles for evidence of interactions across the periodic boundary and quantify the separation between the condensed phase and its periodic images. We will also evaluate the sensitivity of the relevant conclusions to the simulation box dimensions and, where necessary, perform additional checks using enlarged simulation dimensions for representative systems. We will report the outcome of these tests and discuss any remaining finite-size limitations when interpreting the saturation concentrations.

      (3) Some decisions in the simulation conditions require further justification/explanation. More specifically, the concentrations of small molecules used, as well as the decision to conduct simulations at 295 K, should be adequately justified.

      We agree that these simulation conditions require clearer justification.

      The relatively high ligand concentrations were used to increase the number of ligand–protein encounters that can be sampled within the accessible coarse-grained simulation timescales, rather than to quantitatively reproduce the experimental ligand concentrations. In the revised manuscript, we will state this rationale more explicitly, compare the simulated concentrations with the experimental conditions, and discuss the implications of the elevated ligand concentrations for interpreting ligand–protein contact frequencies and possible nonspecific interactions.

      The simulations were conducted at 295 K to match the temperature used in the corresponding experimental measurements that motivated this study. We will clarify this point in the revised manuscript and explicitly state that the simulation temperature was chosen to maintain consistency with the experimental conditions.

      (4) Given the size of the full-length protein, it is understandable that the full dense phase is not probed for the full-length protein. However, it would be useful to comment on how the conclusions may change in the context of the full length. For instance, there is no real interface that the small molecules need to diffuse across and so discussions on the role of partitioning in the paper should be better contextualized in light of this.

      We agree that the full-length simulations should be distinguished more clearly from the slab simulations of IDR1. The full-length systems probe the organization of an assembled high-concentration state and do not contain a sufficiently large coexisting dilute phase and interface from which equilibrium partitioning or a saturation concentration can be determined.

      We will revise the relevant discussion of ligand partitioning to reflect this limitation. Where the current wording implies equilibrium partitioning between dilute and dense phases in the full-length simulations, we will instead describe the measured quantity directly—for example, ligand localization or enrichment within the simulated protein assembly.

      More generally, we will clarify throughout the manuscript which conclusions concern the internal organization of the full-length assembled state and which conclusions concern phase-separation propensity inferred from the IDR1 slab simulations.

    1. Author response:

      The following is the authors’ response to the previous reviews.

      Note from the authors:

      During review of the proofs and re-confirmation of all models and outcomes, we discovered that in the current version of the manuscript, the identity of the lagged time series in the exploratory cross-correlation analysis was misreported. In the cross-correlation plot (Fig. 4d), the posterior alpha time series was fixed and the frontal theta time series was lagged by the times indicated on the x-axis, not vice versa. The inset figures depicting the timeseries will be corrected accordingly in the Version of Record. The subsequent mediation model, in which we tested whether attention mediates the relationship between mnemonic prediction strength and cognitive control, was included as a follow-up to the previously reported cross-correlation outcomes and will therefore be removed. As noted in the Version of Record, the corrected interpretation of the temporal ordering is that in response to a strong mnemonic prediction error, increases in cognitive control precede increases in attention.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      This manuscript describes a multi-modal study of associative learning and memory in humans, that combines scalp EEG, pupillometry and behavioral analysis to explore the construct of mnemonic prediction errors (MPEs), in terms of their relationship to attention and cognitive control. Across two pooled studies, participants performed associative memory tasks in which they learned the relationship between a cue word (action verb) and subsequent picture (animate or inanimate) with a strong vs. weak (4 or 1 repetitions) encoding manipulation. At test, participants were encouraged to generate a prediction following the cue word to determine whether the subsequently presented picture was a match or mismatch.

      The timecourse of pupillary responses during match decisions were decomposed using temporal principal components analysis, which identified 6 distinct and overlapping processes. Some of the components (PC3/PC4) exhibited sensitivity to both the strength and mismatch conditions, as well as behavior (both RT and accuracy) and retrieval success on the subsequent trial. Furthermore, relationships were also observed between pupillary responses (specifically for PC4) and both frontal theta and posterior alpha power measures obtained from scalp EEG in Experiment 2, as well as for frontal theta and subsequent learning from mismatch stimuli (assessed using subsequent memory findings from a surprise recognition test). The authors suggest the findings indicate that MPEs elicit changes in attention, arousal and cognitive control which impact subsequent learning.

      Strengths:

      This manuscript has many strengths, including a clever study design, thoughtful integration of multiple neurocognitive measures, and a set of rigorous and technically sophisticated analyses, which reveal a large set of relationships among the measures and behavior. The findings demonstrating brain/physiology-behavior relationships are particularly important, in that they point to potential functional consequences of MPEs.

      Weaknesses:

      The technical proficiency and complexity of the study and analysis also presents a clear limitation and challenge for interpretation. It is likely that readers, even those that are quite knowledgeable about the methods, constructs, and questions being addressed will often struggle (as this reviewer did) to keep the large set of findings in mind and gain understanding of how they all fit together.

      Indeed, it seems like there many threads running together in the paper which make it challenging to find the through-line of the key findings. The authors do address some of the key questions motivating the paper in the Introduction, but the results are somewhat ambiguous with regard to the primary question of the study as to whether the detection of MPEs leads to interaction among cognitive control, attention, and arousal. To their credit, the authors tackle this question through both cross-correlation and formal mediation analyses, and summarize these in diagrammatic figures (Figure 3, Figure 6). Yet it is not resolved whether the results represent a clear answer pointing to independence, or rather a lack of statistical power, or ill-resolved formulation of the mediational relationship. In particular, the cross-correlation suggests that posterior alpha suppression in response to MPEs does precede frontal theta, yet this indirect relationship does not explain the variation in trial-by-trial RTs on mismatches. This suggests a potential model misspecification.

      In addition to the primary interaction issue mentioned above (between cognitive control, attention & arousal), the Introduction lays out a number of claims:

      (1) That pupil size will be more sensitive to strong than weak MPEs.

      (2) That MPE-linked increases in attention (indexed with posterior alpha suppression) and arousal (indexed with pupil size) will be linked to learning.

      (3) That MPE learning will vary as a function of prediction strength.

      Given the focus on learning, it is somewhat surprising that learning is not included in the mediation models. As the authors indicate in the Discussion, the use of trial-by-trial RT variation to drive the mediation model might be problematic, given that the RTs are sensitive to a range of factors beyond mnemonic prediction strength and also are under competing pressures (longer for mismatches than matches, due to surprise-linked slowing, but also faster following stronger rather than weaker mnemonic predictions). Thus, an alternative possibility might be to use trial-by-trial recognition of mismatches as the outcome variable in mediation models rather than trial-by-trial RT as the independent variable.

      A large component of the results (Sections 2 and 3) is devoted to analyses of cue-linked pupil and EEG processes that putatively reflect mnemonic predictions (i.e., occurring before picture probes are presented and match/mismatch detection, i.e., MPEs occur). Yet these Results and the subsequent pupillary PCA components (PC1 and PC5) that are elicited are not well-integrated with the primary themes of the paper or the causal hypotheses. One finding that does seem to figure prominently (in that it is mentioned in Abstract, Introduction & Discussion) relates to the amount of attention allocated to the mnemonic prediction generation. Yet this finding is not well emphasized in the Results themselves. Possibly it refers to the negative relationship between posterior alpha during memory retrieval and the magnitude of pupillary PC3 component, described in Section 3. But it was quite challenging to identify amongst the wealth of results described in this Section as well as the others. More generally, the large amount of findings described across all four lengthy Results sections makes it challenging for readers to discern what are the key ones that the authors would like to highlight.

      It is recommended that the authors do another pass through the paper to better highlight the most critical findings that they want to emphasize or which are most interpretable from a mechanistic and causal flow perspective and then de-emphasize or move other findings to the Supplemental Materials. Although the authors are to be commended for such a rigorous and comprehensive set of analyses, there are so many of them and findings, that the key points get buried and the reader needs to struggle potentially unnecessarily to identify the key take-away points.

      We thank Reviewer 1 for the helpful feedback on how the manuscript can be further strengthened. We recognize that the rich set of findings can overwhelm the reader, resulting in difficulty discerning the main take aways about the effects of mnemonic prediction errors. We particularly appreciate Reviewer 1’s encouragement to restructure the manuscript so as to focus on the findings reported in Sections 1 and 4 of the original revision; the current revision now focuses on these key observations.

      As part of this restructuring, Reviewer 1 also proposed moving the content from Sections 2 and 3 of the original revision to the Supplement. We agree with the Reviewer that the questions addressed in these sections on retrieval-related processes are not the main focus of the paper, but that they are informative in their own right. To avoid their getting lost in the Supplement, we decided that these results would be better served in a separate manuscript and thus we have removed them entirely. 

      We acknowledge in the revised manuscript that the mediation and cross-correlation analyses were exploratory and that these specific analyses may not be well powered in the current experiments. With respect to Reviewer 1’s concerns about the specification of the mediation models, we were motivated to test whether MPEs trigger an increase in cognitive control that in turn, triggers an increase in attention and/or arousal (Fig. 4a); as such, we designed the model to assess whether, on strong MPE trials, frontal theta mediates the relationship between prediction strength and attention/arousal. As noted in the manuscript and raised by Reviewer 1, mismatch RT here is an imperfect measure of trial-level prediction strength. Future experiments that selectively elicit strong MPEs and have a more controlled measure of trial-level prediction strength may be better equipped to address these questions about interactions between control, attention, and arousal. We agree with Reviewer 1 that models assessing subsequent memory as an outcome would be desirable. However, given that (a) we did not find strong evidence for interactions at the time of a strong MPE and (b) we only observed a relationship between frontal theta and subsequent memory (but not posterior alpha or pupil), subsequent memory mediation models do not appear to be well justified. Altogether, these findings illuminate open avenues for future research.

      Reviewer #2 (Public Review):

      Summary:

      The authors studied cognitive control and attention in response to mnemonic prediction errors (MPEs): situations in which the external reality violates internal memory-based predictions. The behavioral task first established strong versus weak predictions, and then either confirmed or violated these predictions. The authors examined markers of cognitive control (frontal theta) and attention (posterior alpha suppression, pupil response) while strong and weak predictions were confirmed or violated. They found increased cognitive control (frontal theta) for strong MPEs, which correlated with subsequent memory. Markers of attention (alpha suppression, pupil response) also accompanied strong MPEs but did not correlate with subsequent memory.

      Pupil response was investigated using an interesting approach that decomposes the response into different components, finding that different components respond earlier or later and show different correlations with MPEs and their strength. The authors also investigated how EEG, reaction time, and pupil responses correlated with one another, providing further insight into the mechanism underlying the response to MPEs. Together, the study points toward multiple control and attention mechanisms involved in MPE response and memory.

      Strengths:

      The study has a clear behavioral paradigm with multiple measures — behavioral, EEG, and pupillometry — that offer an investigation into different aspects of MPE response and memory.

      The study is also very comprehensive in looking at multiple phases in processing MPEs: the prediction phase (prior to the violation), the response to MPEs, and subsequent memory of MPEs, all within one study. Specifically, the link between neural mechanisms and subsequent memory is a major advancement, as most prior studies did not include this component. Mechanisms underlying subsequent memory of MPEs are theoretically important, as a primary function of MPEs is to promote learning and memory. As the authors mention, the different neural and pupillary signals are not robustly correlated, suggesting multiple mechanisms underlying MPE detections, which is interesting, offers avenues for future research, and can facilitate a better theory of how MPEs are processed in the brain. Finally, the decomposition of pupil response into different components and their correlation with behavior (RT during match/MPE detection) is interesting.

      Weaknesses:

      The methods are rigorous, and the data support the claims. The weaknesses are minor and are offered here as avenues for future research.

      (4) The relationships the authors find between brain measures and pupil components were largely not specific to mismatches/matches. Thus, the specificity of this relationship is untested.

      (5) The results with subsequent memory are important and address a major gap in the field that largely did not relate neural effects of MPE to subsequent memory. However, one major limitation of the study is that the authors did not test memory for matches. I understand the logic of avoiding testing matches. Because matches were repeated more times in the study, it’s not a fair comparison and could change participants’ overall criterion for old/new decisions. Future research could address this, e.g., by testing weak matches or potentially using a between-subject design.

      We appreciate Reviewer 2’s helpful feedback during the review process and encouraging comments on the strengths of the manuscript. We agree and note in the revision that it would be illuminating for future studies to contrast memory for events that violate and confirm mnemonic predictions.

      Comments on revised version

      The authors addressed all my concerns. I appreciate the authors’ thoughtful and detailed response.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      It was challenging to read the paper with key findings happening at the time of the MPE presented first, and then to go “backwards in time” to examine process that occurred at preceding time periods (i.e., prior to probe presentation), and then again forward in time to examine learning related processes.

      (1) Restructuring the Results

      In this regard two distinct recommendations are made:

      - Move Sections 2 and 3 to Supplemental Materials, to maintain the focus on the key findings related to detection of MPEs and their effects on subsequent learning.

      - An alternative structure would be to present the cue-locked findings first, which relate to mnemonic predictions, then to those that occur when those predictions get violated, and finally to the learning process that occur following MPEs and which can be detected with subsequent recognition tests.

      We thank the Reviewer for this encouragement to restructure the manuscript. To address concerns regarding the density of the paper and the cohesiveness of the findings, we removed the content that was in Sections 2 and 3 of the original revision. We will publish those results in a separate paper with additional analyses to more directly address previously raised questions regarding the mechanisms indexed by frontal theta and posterior alpha at the time of retrieval.  

      (2) Integration of the summary figures

      At the minimum, a recommendation would be to better integrate Figure 6, and maybe various versions of Figure 3, earlier into the text, preferably even in the Introduction, and then repeatedly refer to them throughout the results. For example, in Figure 6, linking the leftmost panel of the figure to Sections 2 and 3 is critical, and the righthand panel to Sections 1 with the rightmost part related to learning explicitly linked to Section 4.

      We moved the summary figure up to now be Figure 1; we reference this figure in the Introduction and throughout the manuscript; and we additionally make reference in the figure to the association between frontal theta and PC3 at the time of a strong MPE as well as the cross-correlation outcome. We hope these modifications further aid the reader in identifying the main findings of the manuscript.

      (3) Specification of the mediation models

      Additionally, for the mediation models it is quite unclear why mismatch RT is treated as the index of MPE magnitude, as this seems to be where the problem may lie in model fitting. Why not think of this as an outcome variable (since would seem to be a causal outcome of the underlying functional processes elicited by mismatch detection)?

      We thank the reviewer for these thoughtful comments. Our goal in designing the mediation models in Fig. 4a-c was to test our hypothesis that strong MPEs trigger an increase in cognitive control that, in turn, triggers an increase in attention and/or arousal; thus, attention/arousal should be the outcome and cognitive control should be the mediator. Given that increases in attention and cognitive control were selectively observed for strong and not weak MPEs, the models were restricted to strong MPEs. We therefore needed a trial-level measure of MPE magnitude to determine whether stronger MPEs in the strong condition elicit greater attention/arousal by engaging more cognitive control. As such, we decided to use mismatch RT as a proxy measure of MPE magnitude; we acknowledge in the text that this measure is imperfect. While a model with mismatch RT as the outcome variable is possible, the relative timing of the attention/arousal effects (which largely occur following responses) would render interpretation to be more challenging. Had stronger evidence of indirect effects emerged in Figs. 4b-c, we could have conducted model comparison with RT as an outcome. We acknowledge in the text that these analyses were exploratory and characterization of potential indirect effects will require more data and a more precise measure of MPE magnitude.

      Alternatively, examining trial-by-trial recognition memory of mismatches as the relevant outcome variable would also seem to capture the functional process of interest. In this regard, have the authors examined whether trial-by-trial RT on mismatches predicts subsequent recognition of these items? If this direct relationship holds, it could be a target for mediation analyses in itself.

      We agree with the reviewer that in theory, a mediation model predicting subsequent memory would be a desirable test of an integrated model of the mechanisms underlying MPE-driven learning. However, the mediation analyses conducted to address the functional relationships at the time of a prediction error (Fig. 4) are not well-powered to begin with; this limitation is raised in the Results and the Discussion. A mediation model predicting subsequent memory would be similarly underpowered; given that there is not strong evidence for indirect effects at the time of a strong MPE, and that only frontal theta – and not posterior alpha nor pupil – predicts subsequent memory, we think that such a mediation model is not well justified to include. Such a model should be more directly tested by well-powered designs in future studies.

      (4) Hippocampal theta in the Introduction

      The Introduction discusses hippocampal theta as well as frontal theta yet also makes clear that the former is not really well-detected or analyzed using scalp EEG. Consequently, a recommendation would be to remove this paragraph from the Introduction, since it can be misleading and a “red herring” for the reader, and instead only bring up this point in the Discussion section, as a pointer to the need for future research using methods that may be more sensitive to hippocampal interactions with PFC regions.

      We appreciate this point and moved discussion of the hippocampus from the Introduction to the Discussion.

    1. Author response:

      [Editors’ note: An Expression of Concern has been published for this article. The authors’ responses submitted during revision have been appended for further context]

      eLife Assessment

      This study provides a useful inventory of genes that are up- or down-regulated during the early metamorphic development of male and female larvae and proposes that the microRNA cluster miR-277/34 is involved in the development of sexual differences during early metamorphosis of Drosophila melanogaster, although its precise role remains unclear. The strength of evidence, based on a combination of diverse methods including mRNA and small RNA sequencing, in silico analyses, in vitro assays, and loss-of-function experiments, is incomplete as it lacks a general model and an examination of the potential effects of the miR-277/34 mutations on phenotypes such as morphology or developmental time. This work will be of interest to developmental biologists interested in sexual dimorphism and in the interplay between hormones and microRNAs during development.

      We thank the editor and reviewers for the positive and constructive comments and suggestions. Point-to-point responses are listed below.

      Reviewer #1:

      Summary:

      In this paper, Li and colleagues have found mircoRNAs that affect levels of metamorphosis-regulating genes that can also affect levels of sesquiterpenoids (juvenile hormone and related compounds) and ecdysteriods, which regulate the timing and stages of insects, respectively. They first compared the transcriptomes of Drosophila at the third larval instar and at the white pre-pupa stage. They found thousands of differences in gene transcript levels between males and females, and between the two different stages. Among those genes that were differentially regulated they saw that genes involved in insect hormone biosynthesis were disproportionately represented. Many of the differentially regulated genes were involved in the insect hormone biosynthesis pathway and ascorbate and alderete metabolism. MicroRNAs were also differentially expressed during metamorphosis and were separately identified. The authors then considered genes and whether the differentially expressed microRNAs might regulate transcripts known to be involved in sesquiterpenoid production. In silico analysis of microRNAs predicted a list of 17 microRNAs that can regulate transcripts of sesquiterpenoid biosynthesis genes. The authors then used an in vitro luciferase assay to validate the binding and downregulation of 10 of the microRNAs to genes involved with sesquiterpenoid production in S2 cells.

      Li and colleagues then focus on two genes they found were bound by microRNAs that have established roles in metamorphosis. The microRNAs miR-34 and miR-277 bind transcripts of two protein-coding genes that regulate metamorphosis Kr-h1, which encodes a transcription factor that is a JH-inducible transcription factor, and Allatostatin C Receptor 1, (AstC-R1), a G-protein coupled receptor that regulates the corpora allatum, the gland that produces sesquiterpenoids. Using a LAMP assay, one of the microRNAs, miR-277 was shown to bind to both AstC-R1 and Kr-h1 in in vivo whole-animal extracts. There is no mention of binding between either protein-coding transcript and the miR-34 microRNA. Temporal expression of all four transcripts shows that their abundance is anti-correlated; stages of high miR-34 or miR-277 expression correlate with low AstC-R1 or Kr-h1 expression. Homozygous deletions of both mircroRNAs result in 23% lethality, five days after adult eclosion. The authors also generated specific mutants in miR-34 or miR-277 and find differences in the expression of AstC-R1 and Kr-h1 and sex-specific differences in both sesquiterpenoids and ecdysteroids in the knock-out lines. If there were phenotypes associated with the specific knock-outs, those were not mentioned. Next, the authors examined the transcriptomes of the miR-3277 and miR-34 mutants and found several other GO-terms enriched among the differentially expressed genes. However, the sesquiterpenoid pathway and ascorbate and alderete metabolism are not listed.

      Strengths:

      This is an interesting manuscript that could make an important contribution to our understanding of the roles of micro RNAs at metamorphosis, and potentially of how sex-specific differences arise during metamorphosis. Strengths of the paper include the functional validation of microRNA binding, in vitro and in vivo-, as well as the characterization of sesquiterpenoid and ecdysteroid titers. The authors have also used CRISPR to generate specific knock-outs of miR-34 and miR-277. The transcriptomes will be a resource for future work to mine for differences in gene expression during metamorphosis.

      Weaknesses:

      (1) Spatial Expression of miR-34 and miR-277. If miR-34 and miR-277 regulate AstC-R1 and Kr-h1, then they must be expressed in the same cells. Although the authors show that the microRNAs do bind to the transcripts of AstC-R1 and Kr-h1 in S2 cells, and miR-277 binds AstC-R1 and Kr-h1 in vivo whole-animal homogenates, we do not know if the microRNAs are ever in the cells where AstC-R1 or Kr-h1 are expressed. AstC-R1 is only expressed in a few cells in the brain, so it is not at all certain that it is co-expressed with either microRNA. The creation of enhancer lines or in situ hybridization in Drosophila is straightforward and would sort this out.

      We thank the reviewer for the positive and constructive comments. We agree with the reviewer, and have pointed out the limitation in the main text as follows:

      Lines 307-309 - “Further exploration of the spatial expression between miR-277, miR-34, Kr-h1 and AstC could bring new insights to the regulatory effects they have during metamorphosis”.

      (2) Phenotypes. Although a double deletion was used and specific knock-outs of both miR-34 and miR-277 were generated, the analysis of the mutants is very superficial. For the homozygous deletion of both microRNAs miR-34 and miR-277, only a decrease in survivorship was observed a full six days after adult eclosion - after the end of metamorphosis. No phenotype for either miR-34KO or miR-277-KO was given. The authors cite the work of others who have found specific phenotypes after manipulation of sesquiterpenoids or ecdysteroids, like Riddiford and Ashburner, but do not use any of these many studies to help them characterize the phenotype. If the loss of miR-34 and miR-277 affects so many pathways (including MAPK signaling, TGF-beta signaling, FoxO signaling, and Wnt signaling), as well as global titers of metamorphic hormones, then there shouldn't there be something different in the development to discuss?

      We thank for reviewer for pointing out the phenotypes. We did not detect morphological or developmental abnormalities during larval-pupal transitions in the different knockout mutants, and have now included the previously established research on miR-34 in the main text, shown as follows:

      Lines 305-307 - “MiR-34 has been documented to maintain the neural proteostasis while suppressing age-associated decline (Liu et al. 2012; Kennerdell, Liu and Bonini 2018; Srinivasan, Tran and Bonini 2022).”

      (3) I think the reliance on GO term enrichment is getting in the way of biology. For instance, I would not describe Kr-h1 as a sesquiterpenoid biosynthesis pathway gene. Yet the authors say they were motivated to examine microRNA regulation of Kr-h1 because they saw differences in levels of the sesquiterpenoid biosynthesis pathway between WL3 and WPP, a period which also saw differences in expression of some microRNAs. I understand that Kr-h1 expression is regulated by JH, a sesquiterpenoid, but it is not directly involved with JH production, so relying on GO term enrichment has made the decision to focus on Kr-h1 feel arbitrary.

      We have stated out the rationale and rephrased that Kr-h1 as sesquiterpenoid responsive gene in relevant sentences in the Results, shown as follows:

      Lines 135-145 - “Utilising an established cell culture dual-luciferase reporter assay (Hui et al 2013); we have validated 7 microRNAs (miR-8, miR-277, miR-958, miR-1000, miR-1002, miR-2283, miR-2280) that can downregulate the expression of Drosophila genes involved in JH synthesis, responsive, or signalling genes to varying degrees, including allatostatin C (AstC), allatostatin C receptor 1 (AstC-R1), allatostatin C receptor 2 (AstC-R2), Krüppel homolog 1 (Kr-h1), Chd64, juvenile hormone binding protein (JHBP), juvenile hormone diol kinase (JHDK) and juvenile hormone esterase (JHE) (Figure 1C). Among these genes, Kr-h1 or Kruppel homolog 1, is a JH-dependent transcription factor (responsive gene), and have been found to be regulated by another microRNA in cockroaches (Lozano et al 2015); while AstC-R1 or allatostatin C receptor 1, is a G-protein coupled receptor for neuropeptide allatostatin C which regulates juvenile hormone synthesis (Stay and Tobe 2007).”

      (4) The transcriptomes of miR-34 and miR-277 should have revealed genes encoding members of the sesquiterpenoid biosynthesis pathway as well as AstC-R1 and Kr-h1, but neither was mentioned. The functional tests of miR-34 and miR-277 were performed because they were shown to affect the levels of expression of genes in the sesquiterpenoid biosynthesis pathway. Figure 2 shows a significant decrease in AstC-R1 and Kr-h1 transcripts after the loss of miR-34 and miR-277. However, the results do not mention either (Lines 250-264). Instead, there is a list of 10 different GO terms (like arginine and proline metabolism or fatty acid degradation) that were enriched in miR-34 and miR-277 transcriptomes. If any of those ten types have any relationship to Kr-h1, AstC-R1, or metamorphosis, that has not been explained.

      We have now explicitly stated that Kr-h1 is significantly downregulated in the miR-277-KO transcriptomes consistent with our qPCR validation, as well as the transcriptomic analyses were used to understand genome-wide changes, shown as follows:

      Lines 211-217 - “Among these differentially regulated genes, Kr-h1 was significantly downregulated in the miR-277-KO mutants (Supplementary Table S2), consistent with our qPCR validations (Figure 2B). On the other hand, AstC-R1 was not classified as differentially regulated based on the in silico analyses threshold of the whole-body RNA-seq data, and whether this was due to its restricted expression in a small subset of brain neurons would require further experiments to differentiate between different scenarios.”

      Lines 255-259 - “It implies that miR-277 could have conserved regulatory roles of sesquiterpenoid and related pathways, and also divergent roles between sexes during metamorphosis with signaling pathways associated with cell proliferation, wing development, nutritional support, and endocrine regulation (Pan et al 2018; Jiang and Edgar 2009; Gibbens et al 2011; Toyama et al 2014).”

      (5) Not enough care was taken in describing the stages. The methods describe wandering larvae (WL3) and white pre-pupa (WPP) for the transcriptomes, but in the text, different terms are used, like "larva", "pupa" and "L3 larvae instars" "early pupae" "late L3". Also, it seems like the small RNA libraries for sequencing were taken from "L3 larvae", but the stage of the L3 larvae was not mentioned. Staging is important, especially during metamorphosis, since differences in expression are expected to exist between different stages of L3, between early vs late wandering, and between WPP and early pupal stages.

      We thank the reviewer for highlighting the importance of staging clarity, and have now revised both the Results and Methods to ensure all stages are defined explicitly and used consistently throughout the manuscript. In our dataset, all references to “L3 larvae” or “larva” correspond specifically to wandering third-instar larvae (WL3) which that have exited the food, display 1/3 to 1/4 gut contents, and show protruding anterior spiracles. All references to “pupa”, “pre-pupa”, or “early pupae” refer to white prepupae (WPP), defined as immobile individuals with fully everted spiracles and no movement when gently probed.

      Recommendations:

      (1) Lines 171-173. The genotype of the deletion line is given, but what is the genotype of the flies that were used? Were the balancers and chromosomes with mutations included in the analysis? I cannot tell from the description.

      The miR-277-34-KO line was used and significant decrease in survivorship was observed in double knockout line. The information is now included as follows:

      Lines 158-164 - “In the homozygous loss of function of miR-277/34 cluster fly (w[*]; Df(3R)mir-277-34-KO, TI{w[+mW.hs]=TI}mir-277-34-KO/TM3, P{w[+mC]=GAL4-twi.G}2.3, P{UAS-2xEGFP}AH2.3, Sb[1] Ser[1]; Chen et al 2014), we found that the heterozygous knockout individuals displayed low to almost no lethality, while the survivorship for the double knockout flies fell significantly with 77% of the double knockout flies dying within five days after eclosion (Figure 2A).”

      (2) The introduction and discussion are too broad. I would expect some information about what is happening to ecdysone and juvenile hormone titers during metamorphosis. Additional detail should be given to the regulation of the corpora allatum, since the Ast-C1 gene and sesquiterpenoid levels were a major part of the results. I had hoped the discussion would help to synthesize the details within the results, particularly the differences between sexes. Instead, the discussion is very general, citing other papers that are related, but without tying the results within those papers to specific results in this paper.

      We thank the reviewer. The following information is now included in the main text:

      Lines 47-53 - “Multiple ecdysone titre peaks were observed during Drosophila development with each pulse corresponds to a developmental transition (Kannangara et al., 2023; Scanlan et al., 2023). For instance, there are one small and another big one triggering wandering in larvae and pupariation, respectively. For sesquiterpenoid juvenile hormone, its titre in corpora allatum changes in different developmental stages (Zhang et al., 2022) and generally decreases closer to the end of larval stages for pupariation (Dubrovsky 2005).”

      (3) I found the text to be unclear, and important details were missing. There are many different cases where titers or gene expression went up or down, in males or females, but it is difficult to understand if these were expected or not, or what to make of all the differences. I also do not have a clear idea of what the hypothesis is. I had thought that the microRNAs were promoting the degradation of AstC-R1 or Kr-h1, so their loss should result in higher levels of AstC-R1 or Kr-h1 transcripts. However, Figures 2B and C show that there are lower levels of AstC-R1 and Kr-h1 transcripts in the loss of either miR-34 or miR-277. How does this fit with what is known of the progression of metamorphosis? A model built from the results to this point could help to organize the text.

      The following information is now included in the main text, shown as follows:

      - Lines 172-177 - “We then compared the expression of Kr-h1 and AstC-R1 of miR-277-KO, miR-34-KO, and between KO mutants and wild type flies using quantitative real-time PCR. The expression level of Kr-h1 was found to be significantly downregulated in both sexes of WL3 and WPP miR-277-KO mutants, coherent to the RNA-seq results; whereas a reduction was only noted in the male WL3 for miR-34-KO mutants but not in RNA-seq (Figure 2B; Supplementary Table S2).”

      - Lines 178-186 - “On the other hand, expression level of AstC-R1 determined by real-time PCR was found to be upregulated during metamorphosis in wild-type (w1118) flies, but not for either miR-277-KO or miR-34-KO mutants (Figure 2C; Supplementary Figure 6). This is in agreement with the transcriptomic analyses where AstC-R1 was only up-regulated during male and female metamorphosis in the wild-type fly (Supplementary Table S2). In addition, we also found that the expression level of AstC-R1 in WPP of both miR-277-KO and mir-34-KO flies were significantly different to that of the w1118 flies (Figure 2C). Together, these data demonstrated that Kr-h1 and AstC-R are stage-specifically regulated by miR-277/34 in vivo.”

      Reviewer #2:

      Summary:

      This study proposes that the microRNA cluster miR-277/34 controls the generation of sexual dimorphism in Drosophila melanogaster during metamorphosis by acting on specific hormonal and developmental gene pathways.

      Strengths:

      Using a combination of mRNA and small RNA sequencing together with genome-wide in silico and in vitro analyses the authors identified a microRNA cluster that may be involved in metamorphosis and the generation of sexual dimorphism in Drosophila melanogaster.

      Weaknesses:

      Biological validation of the identified sexually dimorphic genes and a detailed understanding of how the microRNA cluster miR-277/34 might be involved in the regulation of sesquiterpenoids are needed.

      Major suggestions:

      (1) If AstC-R1 and Kr-h1 are targets of the miR-277/34 cluster and cause their downregulation, it is not clear why there would also be a decrease in the levels of these genes in the miR-277/34 mutants. This would suggest that the mechanism is not straightforward and that further epistatic experiments should be carried out in order to clarify this issue.

      We thank the reviewer for the positive and constructive comments. We agree that targets participate in endocrine feedback loops is dynamic, which could be the case for Kr-h1 and AstC-R1 during the larvae-pupae transition as they are components of the sesquiterpenoid hormone regulatory network. Epistatic analyses would be useful for future work and seem to be beyond the current scope of this study. The following information is now included in the main text:

      Lines 184-187 - “Together, these data demonstrated that Kr-h1 and AstC-R are stage-specifically regulated by miR-277/34 in vivo. Further epistatic experiments would be needed to understand the dynamics between and the hormone actions.”

      (2) The changes in the expression levels of AstC-R1 in pupae of miR-277-KO and mir-34-KO flies must be accompanied by photos of the respective larvae and pupae, as well as an analysis of the larvae-pupa transition on the mutants by gender.

      We thank the reviewer for this suggestion. We have now added reference images illustrating the WL3 and WPP stages for w1118 in the Appendix as suggested (Author response image 1). We have analysed the larvae-pupae transition in both sexes of miR-277-KO and miR-34-KO mutants, directly comparing them with stage-matched w1118 controls, and we did not observe any detectable differences in larval morphology, pupal morphology, anterior spiracle eversion, gut-purge status, or timing of pupariation between the mutants and controls.

      Author response image 1.

      (3) Biological validation of the identified sexually dimorphic genes in vivo will be necessary for the support of this work.

      We have now included additional quantitative RT-PCR validation of key insect hormone pathway genes in male and female WL3 and WPP stages of wild-type, miR-277-KO, and miR-34-KO flies (Figure 5). These additional analyses confirm sex-specific expression differences in both wild-type and mutant backgrounds, supporting dimorphic endocrine regulation. The main text are also revised and shown as follows:

      Lines 276-287 - “To understand how different hormones such as juvenile hormone (Belgacem and Martin, 2002) involved during metamorphosis in both sexes, we selected and tested a selection of candidates from both sesquiterpenoid and ecdysteroid hormone pathways, and found JHAMT, Spok, CG40486, and CG10962 showed differential expression during transition from WL3 to WPP in mutant and/or wild-type fly lines in the transcriptome analyses (Supplementary Figure 16). To further examine these RNA-seq patterns, we performed RT-PCR on nine candidate genes from WL3 to WPP in WT and mutant fly lines. In the larval-pupal transition comparison, CG40486 was consistent down-regulated in WT males and females in both RNA-seq and RT-qPCR datasets. In the mutant-vs-WT comparison, CG9360 showed concordant downregulation in miR-277-KO WPP females. Other tested genes showed more condition-specific patterns matching between the transcriptomic and RT-qPCR analyses. Further validation and mechanistic studies will be required to define how these hormone-pathway changes contribute to the larval–pupal transition.”

      Reviewer #3 (Public Review):

      Summary:

      The authors show convincingly the complexity of gene up- and down-regulation at the outset of metamorphosis and identify substantial differences between the two sexes, even at this early time in development. The complexity of microRNA expression and the difference between the sexes are also nicely laid out. The functional significance of these differences, though, is harder to establish. The authors have focused on the roles of two families of developmental hormones, the ecdysteroids, and the juvenile hormones. The emergence of sex-specific differentiation of organs during metamorphosis is clearly downstream of the action of ecdysteroids and/or JH, but there is no evidence that the presence or lack of these hormones has any effect on the sexual identity of organ systems - i.e., that manipulations of JH or ecdysteroid result in either the masculinization or feminization of individuals or their organs. The precedence for the linkage of these hormones to sex determination is the 2002, Belgacem & Martin study, which describes the effects of JH on fly locomotion. These authors show that the number of stop/start bouts is sexually dimorphic, and removal of JH in males shifts their frequency into the female range while giving treated males exogenous JH moves it back. While this is referred to as a "feminization" of male behavior, this quantitative shift in frequency is not as compelling as would be a qualitative shift -- for example, the removal of JH causing males to show egg-laying behavior (a result that has never been seen). Also, these effects are in a fully mature system, rather than at the early metamorphic time examined in the present paper. In driving and coordination metamorphosis, JH and ecdysteroids are intimately involved in sexual differentiation, but I know of no compelling evidence that they play a role in sex determination.

      We thank the reviewer for the positive and constructive comments. We agree that our findings advanced on the sexual differences in gene regulation during metamorphosis rather than establishing direct evidence of juvenile hormone (JH) or ecdysteroids in influencing insect sex determination. In addition to rephrasing at various parts of the main text (see below), we have also carried out additional experiments in obtaining and analysing transcriptomes of late larvae and early pupae of both sexes in the wild-type of another species (Drosophila virilis), which showed similar KEGG pathways enriched. The revised parts are shown as follows:

      Lines 289-303 – Results section

      “Metamorphosis between different sexes in D. melanogaster and D. virilis

      In D. melanogaster, the transition from WL3 to WPP shows increased carbohydrate/energy metabolism and ER protein processing, with decreased lipid metabolism, detoxification (cytochrome P450), and redox/cofactor pathways (folate, glutathione, retinol); while PM-LM exhibits broader negative enrichment in translational and RNA-processing machinery (ribosome, spliceosome, proteasome, RNA degradation, ubiquitin-mediated proteolysis) and in signaling modules (mTOR, MAPK, FoxO, Hippo), whereas PF-LF shifts are smaller and less coordinated by GSEA (Supplementary Figure S15). On the other hand in D. virilis, core features match that of D. melanogaster from WL3 to WPP, carbohydrate/energy metabolism and ER protein processing increase, while lipid, detoxification, and redox/cofactor pathways decrease. The sex bias is inverted relative to D. melanogaster as PM-LM shows limited up-regulation, whereas PF-LF displays broader, coordinated repression involving amino-acid metabolism (glycine/serine/threonine; cysteine/methionine), lysosome, ABC transporters, and longevity-related signaling, yielding the largest DEG set in females (Supplementary Figure S15). These data strongly suggested the sexual differences in gene regulation during metamorphosis in insects is not species-specific.”

      Lines 354-361 – Methods section

      “D. melanogaster w1118 and D. virilis were reared at 25 C, 45-50% relative humidity and 14:10 hour light-dark cycle. Sexes of wandering L3 larvae instar (WL3) were differentiated under the light dissecting microscope by the presence (male) or absence (female) of gonads (Supplementary Figure 1). Collections were restricted to larvae wandering out of food and ready for pupariation. WPP were defined as immobile puparia with everted spiracles and a uniform white cuticle that were no longer moving even with external stimuli. A total of three biological replicates (Whole-body of 1 individual was served as per biological replicate) per stage and sex were obtained for D. melanogaster and D. virilis.”

      While the summary of the effects or removal of specific microRNAs on the components of the biosynthetic pathway for the JHs and ecdysteroids (Figure 2E ,F) is quite compelling, I am concerned about the effects of the removal of mir-277 and mir-34 on the levels of both the JHs and 20E. My concern centers around the data from the control group (w[1118] animals in Figure 2D). These data are the first report of a marked sex difference in the titer of either JH or ecdysteroid at the start of metamorphosis in Drosophila. As expected, males show a 10-20 increase in levels of JH III, JHB3, and 20E between the L3 stage and the white puparium, but, surprisingly, the levels of these hormones in female L3 larvae are equal to or greater than that seen at pupariation! These data for females run counter to over 50 years of work on the effects of ecdysteroids in Drosophila!

      We thank the reviewer and agree that the endocrine profiles of WL3 females require careful interpretation, given the late-L3 to WPP transition represents a highly dynamic window in which ecdysteroid and sesquiterpenoid titres can fluctuate over short developmental intervals. The revised text is shown as follows:

      Lines 322-326 – “Given the WL3 to WPP transition represents a highly dynamic window in which ecdysteroid and sesquiterpenoid titres can fluctuate over short developmental intervals, future experiments on narrower early-/mid-/late-wandering timepoints will be required to understand the dynamics of the microRNAs and hormones.”

      As far as I can gather from the paper, the L3 data were obtained using wandering larvae. This stage lasts for about 12 hours and ends with pupariation. Larvae from this period need to be used with caution for hormone studies. Levels of both JH and ecdysteroid are low as larvae leave the food but rapidly rise to their peak levels at the white puparium stage 12 hours later. To deal with the rapidly changing hormonal landscape through this period, the researchers have used physiological markers to track this progression. Initially, it was the sage of "puffing" of the giant salivary gland chromosomes, but, for bulk collection of staged larvae, larvae are fed on food containing a blue dye, and progression is tracked by the loss of blue coloring from the gut. I could not find if the authors had any criteria for selecting larvae during the wandering period. Male and female larvae grow to different sizes. Might this difference in growth be biased when larvae were selected during their wandering phase?

      We thank the reviewer and agree that WL3 represents a hormonally dynamic 12-hour window. To minimise developmental heterogeneity, WL3 larvae were selected for larvae that had completely exited the food and climbing upwards of the fly vials. To ensure tight developmental synchrony, pupating individuals from the same batch were collected 4 hours later, allowing us to match WL3 and WPP animals from a single, developmentally coordinated cohort. This paired-batch collection tried to minimise variation arising from differences in timing of wandering onset. As for the differences between the body sizes of male and female larvae, we minimise size-dependent bias, hormone titres measurement were measured to ng hormone per gram of tissue in our study, which corrects for sex-specific differences in mass. The information is now included in the main text as follows:

      Lines 276-287 – “To understand how different hormones such as juvenile hormone (Belgacem and Martin, 2002) involved during metamorphosis in both sexes, we selected and tested a selection of candidates from both sesquiterpenoid and ecdysteroid hormone pathways, and found JHAMT, Spok, CG40486, and CG10962 showed differential expression during transition from WL3 to WPP in mutant and/or wild-type fly lines in the transcriptome analyses (Supplementary Figure 16). To further examine these RNA-seq patterns, we performed RT-PCR on nine candidate genes from WL3 to WPP in WT and mutant fly lines. In the larval-pupal transition comparison, CG40486 was consistent down-regulated in WT males and females in both RNA-seq and RT-qPCR datasets. In the mutant-vs-WT comparison, CG9360 showed concordant downregulation in miR-277-KO WPP females. Other tested genes showed more condition-specific patterns matching between the transcriptomic and RT-qPCR analyses. Further validation and mechanistic studies will be required to define how these hormone-pathway changes contribute to the larval–pupal transition”.

      The other hormone-related issue is the expression of Kr-h1 during larval stages and metamorphosis (Figure 1G). Kr-h1 is the main target of JH and Kr-h1 expression is often used as a proxy for the JH titer. The authors report that peak Kr-h1 expression occurs in the L3 (when the JH titer should be lowest!) and that it drops at wandering. This pattern is counter to that reported in the literature (e.g., FlyBase, ModEncode).

      We have now revised the main text as follows:

      Lines 204-207 – “It should be noticed that the analyses of this study was based on RNA taken from whole-body rather than individual tissue, and further experiments will be required to dissect the dynamics of Kr-h1 and different hormones both spatially and temporally.”

      Besides dealing with the issues above, it would be useful in the background to establish the difference between "sex determination" and "sexual differentiation". I was surprised that the authors could deal with this subject without ever mentioning the sex determination pathway - e.g., double sex, transformer, etc.

      In this study, one major focus was on the differences between sex during metamorphosis rather than the sex determination pathway. We have included the reviewer’s suggestion by adding the following information in the main text, shown as follows:

      Lines 73-75 - “In insects, various genes related to sex determination or showing sexual dimorphic features have been revealed, including doublesex and transformer (Shukla and Nagaraju, 2010; Deng et al, 2025).”

      Line 61: at the time that the authors are considering, -- the transition from larva to pupa - the main controller of ecdysone production in the prothoracicotropic hormone, not ecdysis triggering hormone.

      Thanks for the reviewer’s suggestions. The main text is now written as follows:

      Lines 44-47 - “In general, these three hormones work in a cooperative manner, where ecdysteroid 20-hydroxyecdysone controls the timing of ecdysis or molting, prothoracicotropic hormone and the insulin-like peptides act as regulators of ecdysteroid synthesis, and sesquiterpenoid hormones such as juvenile hormone (JH) regulates metamorphosis based on their titre levels.”

      Line 71: it would be useful to name the main microRNAs that have been implicated in regulating insect metamorphosis.

      The main text is now written as follows:

      Lines 60-63 - “Previous studies have identified a number of microRNAs contributing to the regulation of insect metamorphosis such as let-7, miR-125, and miR-2 family (e.g. Caygill and Johnston 2008; Sokol et al 2008; Lozano et al 2015).”

      For Figures 2E and F as well as 3C (and a number of supplementary figures), it would be useful to provide some quantitative representation of the level of activation or suppression (as done in Figure 3B) rather than just Red or Green

      The trend of expression change of genes in selected pathways and detailed quantitative information can now be found in the supplementary file.

    1. Author response:

      General Statements

      We thank the four reviewers for their careful reading of the manuscript and for their constructive and insightful comments. Below, we outline the revisions we have already started or plan to make shortly in response to the reviewers' specific comments.

      Description of the planned revisions

      Reviewer #1:

      In general, the manuscript is well structured and written, with carefully designed figures. The authors are also generally aware of the limitations of the work. The manuscript is interesting and valuable, but some interpretations should be moderated.

      Major Comments:

      (1) The data presented provide in general good support for majority of conclusions presented in the manuscript. However, less support is provided for the theories that: there is a universal "core expression signature" of dormancy; the mRNA/ribosome protein uncoupling reflects a specific mechanism of preparation for exiting dormancy; and the observed changes provide evidence for an epigenetic "memory" of dormancy. These elements are currently more interpretive than evidentiary. I would recommend softening the language in these places and clearly labeling them as hypothetical.

      We agree, of course, that the core expression signatures determined for yeast, killifish and human may not extend to all other dormant states (and we do not call it universal in the manuscript). Also, the mechanistic nature of the ‘memory’ of dormancy is not known, and we have merely speculated on the possibility of an epigenetic memory for discussion, based on the known causes of similar phenomena. Similarly, we discussed plausible processes underlying the mRNA/ribosome protein uncoupling. We will make it clearer in the revised manuscript that these are only hypotheses at this point.  

      (2) The authors propose that spores and post-dormancy cells retain a memory of time spent in dormancy or stress exposure. However, sporulation is also generally expected to reset or remove accumulated damage. Please clarify whether the observed long-term effects reflect classical "memory" of the cell, persistent regulatory state, or selection of cells with different fitness (carry-over effects). I would be careful in interpreting the effects as a form of memory associated mostly with epigenetic control - the statement seems stronger than what the data directly demonstrate

      Our experiments focus on spores (post-sporulation) and their offspring cells, so these findings have no bearing on any reset that may occur during earlier sporulation. It is extremely unlikely that the observed ‘memory’ effects reflect the selection of cells with different fitness, because we started with genetically identical cells, findings were repeated independent biological replicates, and our conditions (stress and prolonged time) maintained the viability of most cells. However, we certainly agree that our results do not establish a mechanism for the observed post-dormancy ‘memory’ effects. Again, we merely discussed the plausible possibility of an epigenetic memory and will provide more nuanced interpretations in the revised manuscript.

      (3) Validation of a small set of top hits by independent assays would substantially strengthen the conclusions. For example, targeted qPCR and/or biochemical assays for key genes (like ribosomal and autophagy) or pathways would help confirm the most important transcriptomic and proteomic trends. Without this, the suggestion of, for example, translational regulation remains possible but unproven

      For transcriptome and proteome studies using current, reliable methods, transcripts or proteins from specific genes are not typically validated, especially when studies focus on global patterns and functional enrichments rather than on any specific genes. General induction of autophagy-related genes at both the RNA and protein levels is unlikely to occur by chance, and autophagy genes have previously been shown to be induced under similar conditions, including in the transcriptomes of killifish diapause embryos (see Fig. S2H). However, we agree that validation of the unexpected regulation of ribosomal genes in diapause embryos would strengthen this conclusion. In spores, the effect is weaker and depends on the control sample used. We have begun qPCR and Western validation of ribosomal protein gene expression in killifish embryos to independently confirm the antagonistic changes in relative expression at the RNA and protein levels. We will incorporate these results in the revised manuscript.

      (4) Overall, the study appears reproducible, with detailed methods, biological replicates, and appropriate statistical analyses. However, reproducibility could be improved by more clearly describing the limitations of the comparisons (especially with the published datasets) and the data-processing parameters, particularly for correlation and functional enrichment analyses. Some comparative conclusions are based on data from different studies, under different conditions and often with different depths of coverage. It is not always clear to what extent interspecies comparisons are fully methodologically similar

      We used two strategies to minimise the limitations of comparing our RNA-seq data with a published RNA-seq dataset (human dormant cancer cells): first, we considered only genes that were detected in all datasets being compared, so that any differences in sequencing depth would not bias the comparison; second, we used relative expression values normalized to their respective controls instead of raw values, using identical cutoffs for all studies (fold-change >1.5x; FDR <0.05), to make the cross-study comparisons more consistent. We will further clarify this and its limitations in the Methods and Results. Notably, we observed significant functional enrichments shared across all three model systems, something one would not expect if the comparison were strongly affected by differences in the analyses. A strength of our study is that the RNA-seq datasets used to compare killifish and yeast were both generated in our laboratory under standardised conditions and processed through the same bioinformatics pipeline, thus enhancing comparability. 

      Minor Comments:

      (1) Because the Bar-seq assay measures barcode abundance only after germination and regrowth, the phenotype may reflect not only spore survival but also germination efficiency and subsequent growth. Please discuss how the authors controlled for selection during regrowth and whether new mutations, clonal selection, or differences in ploidy could contribute to the observed effects.

      We highlight in the manuscript that “Bar-seq quantification of deletion mutants was carried out after spore germination and regrowth. Therefore, the abundance of each barcode is a product of the combined influence of spore survival, germination efficiency and growth, which may affect stress- or lifespan-associated phenotypes for some mutants, a compromise necessary to prevent barcodes of dead spores from being sequenced.” To partially correct for this effect, we used conservative cutoffs and normalised all barcode abundances to the 2-week reference timepoint, so mutants that were already depleted early on due to poor germination or growth should not confound the longevity analysis. Similarly, the heat-shocked samples were compared to unstressed control samples, and any differences between the two samples should therefore reflect the effect of heat stress. All timepoints and pools were grown under consistent, uniform outgrowth conditions. We used two independent biological replicates and pooled samples, so any effects arising from extremely rare events, such as new mutations or diploidization, should be negligible. Moreover, our genome-wide screens focus on global functional enrichments rather than any specific mutants. We will describe this strategy in more detail in the Methods section.

      (2) Please clarify whether spores were analyzed as pooled spores or after tetrad dissection, and how the authors ensured that colonies originated from single haploid spores rather than mixed events. Since ploidy can affect growth and lifespan, please indicate whether ploidy was checked in the recovered colonies or whether the experimental design excludes diploid formation during germination/regrowth.

      As indicated in the scheme in Fig. 1A, meiosis was triggered by crossing a haploid h+ with a haploid h- colony to generate diploid cells that immediately sporulate, using a colonypicking robot. All cells that do not form haploid spores after this step are then killed by heat. This is the same principle as applied for genetic interaction screens using synthetic genetic arrays (SGA). Thus, the haploid spores in each colony resulted from a cross between cells of different mating types carrying an identical deletion mutant. For both the Bar-seq screen and expressionbased spore analyses, spores were analysed as pooled populations without tetrad dissection. Our results refer to the population rather than the single-cell level. Unlike budding yeast, fission yeast cells do not normally grow as diploids and will not mate in the medium used for germination and regrowth. Naturally occurring, vegetatively growing diploid cells in fission yeast are rare and unstable; they would be at an equal growth disadvantage during regrowth from all conditions tested, thus minimising the possibility of a systematic bias caused by diploidy. Accordingly, we did not directly check for ploidy. We will describe this experimental design in greater detail in the Methods.  

      (3) The cross-species GO enrichment analyses may be affected by differences in annotation quality and gene coverage, especially between yeast and killifish. Please clarify how gene duplication, paralogs and annotation redundancy were handled and whether the conclusions remain robust after accounting for GO term similarity or annotation bias.

      Response:  The handling of orthology, paralogs, and annotation differences between species is described in the Methods. Importantly, yeast and killifish genes, and their GO terms, were not directly compared but via their corresponding human orthologs and GO associations, as these mappings are most reliable and comprehensive. Orthology relationships between fission yeast and humans were obtained from a manually curated list in PomBase (Wood et al. 2019), compiled from various sources. In some cases, the consensus ortholog from the major ortholog predictors (Compara, Inparanoid, OrthoMCL) is used. Distant orthologs have also been identified by PSI-BLAST matches. Other ortholog predictions come from experimental data demonstrating functional correspondence or involving membership of corresponding complexes. These predictions are aligned and submitted to Pfam before inclusion. PomBase’s approach ensures that the breadth of coverage exceeds that of any individual prediction method and includes many ortholog calls that are not detected by any automated method. Killifish-to-human orthology was inferred from BLASTp-based mapping to the human UniProt reference proteome, with additional hidden orthologs identified using the spotted gar proteome (Kelmer Sacramento et al. 2020). Spotted gar is a fish whose lineage diverged from teleosts before their genome duplication, and it was therefore used as a bridge to identify hidden orthologs between teleosts and mammals. All paralogs were included to ensure comprehensive coverage, although some may have specialised roles. 

      Thus, all genes were mapped to their human orthologs and their GO associations, and genes commonly regulated were identified by filtering for significantly induced or repressed genes across all models, as indicated. This procedure circumvents the bias in GO term annotation between yeast and killifish. Naturally, given the relatively poor annotation of the killifish genome, such comparative analyses may miss some orthologs. Nevertheless, we observed significant functional enrichments shared across all three model systems, something one would not expect if the comparison were strongly affected by differences in annotation quality or gene coverage. We will highlight this information more clearly in the revised manuscript. 

      (4) Please discuss whether the age of the mother cells could influence spore quality, lifespan, or stress resilience. Did the authors control for mother-cell age? I would like to know about a possible impact on spore quality and subsequent lifespan.

      Spores were always produced from freshly grown cells derived from frozen stocks, thereby controlling for any effects of cell age on spore quality and lifespan. Moreover, unlike budding yeast, fission yeast cells grow by symmetrical division, producing two daughter cells of equal size, so the concepts of mother cells and replicative ageing do not apply.  

      (5) It may be useful to briefly note how dormancy in plants differs from the fungal and animal systems studied here or to clarify that the present conclusions are limited to the models analyzed in this manuscript.

      We agree that this is an interesting topic, e.g. plant seeds. However, given that dormancy is an understudied cell state, there is not enough solid information to make meaningful comparisons at this point. Moreover, any comparative review of what is known in plants is beyond the scope of our study. In the revised manuscript, we will clarify that our findings are naturally limited to the fungal and animal cells analysed in our study.  

      (6) Please briefly justify the choice of heat shock as the acute stress condition. It would also be helpful to comment on whether oxidative stress (for example, by incubation with H2O2) might reveal similar or distinct aspects of dormant-cell resilience.

      Heat shock is a well-established stressor for yeast that elicits a conserved stress response and, most critically, avoids the spore wall permeability problem that complicates the interpretation of trials with chemical stressors. We have actually tried to stress spores with H2O2 at different doses, treatment times, and cell densities; under all tested conditions, spores maintained high viability similar to untreated spores, possibly due to their strong catalase activity (spore suspensions foamed after adding H2O2). Therefore, oxidative stress is not a suitable stressor for the resilient spores. In the revised manuscript, we will show these data in a supplement to justify the use of heat shock as an acute stress condition. 

      Reviewer #2:

      This study is interesting because it provides valuable transcriptomic and proteomic datasets across a large number of conditions in both yeast spores and killifish embryos. Furthermore, these datasets reveal several interesting insights about dormancy, including shared gene expression changes in dormancy across diverse organisms, a trade-off between stress resilience and longevity in yeast spores, and memory of heat stress following exit from dormancy.  This interesting manuscript would be strengthened by additional characterization of the functional consequences of these gene expression changes.

      Major Comments: 

      (1) The finding that a set of gene expression changes in dormancy is shared between yeast spores and killifish diapause embryos is very interesting and raises the question of whether the genetic determinants of stress resilience or longevity in dormant states are also shared. For instance, do any genes identified in the genetic screen as critical for resilience to heat stress in yeast spores also show a similar phenotype in killifish diapause embryos?

      We used the genome-wide deletion library in fission yeast to systematically screen for genes required for spore resilience and longevity. A comparably large-scale functional interrogation is not possible for killifish diapause embryos. Generating deletion-mutant lines for even a single gene in killifish is quite a lengthy and costly effort and would not be realistic within the scope of this work. However, we agree that an exciting direction for future studies is to assess what conserved genes contribute to dormancy function across species.

      (2) The authors show that gene expression changes in dormancy (old vs. young spores and late vs. early diapause) are poorly correlated with aging in stationary-phase yeast cells (Figure 4E) and killifish brain (Figure 5E). The authors suggest that this poor correlation might reflect a lack of aging during dormancy. Interestingly, the authors also show that in both yeast and killifish models, both time and stress in dormancy result in gene expression changes following exit from dormancy. Are these post-dormancy differences correlated with aging in stationary-phase yeast cells and adult killifish? Additionally, could the authors compare these changes with age-related changes in different adult killifish organs?

      We conducted these analyses and did not observe any positive correlation between post-dormancy gene expression changes in yeast offspring from old spores and gene expression changes in stationary-phase ageing cells; if anything, the gene expression signatures showed a slight inverse correlation (R = -0.05; p = 9e-04). For killifish, postdormancy expression changes in embryos from late diapause showed no significant correlations with age-related expression changes in adult brain (R = −0.04, p = 0.84), liver (R = −0.03, p = 0.39), or skin (R = −0.06, p = 0.19). Changes in expression in killifish late diapause compared to early diapause showed no significant correlation with age-related changes in expression in adult killifish liver (R = −0.008, p = 0.53), but did show a weak correlation with old skin (R = 0.18 , p <2e−16), specifically repression of collagen and extracellular matrix genes. We will include the latter analyses in the revised manuscript as supplemental panels.

      (3) In Figures 1C, 4F, and 5F, the authors find significant correlations between two comparisons with a shared condition (e.g. 2-week unstressed spores in Figure 4F). Using the same samples in both comparisons can inflate the correlation between the two sets of fold-changes because the two comparisons are not made independently. The authors should ensure that the correlations found in these figures remain significant even when different samples are used for the shared condition in the two comparisons.

      To address this issue, we re-ran the correlation analyses shown in Figs 1C, 4F and 5F using independent replicates for the shared condition (split-replicate analyses). For example, in Fig 4F, replicate A of the 2-week unstressed spores was used for the old-versus-young comparison, while replicate B was used for the heat-shock-versus-control comparison. For Fig 1C, using independent batches, the correlations remained significant (Batch A vs B: R = −0.16, p = 4.e−16; Batch B vs A: R = −0.27, p <2e−16). For Fig 4F, using independent replicates of the unstressed spores, the correlations remained significant across all replicate pairs (Rep 1 vs Rep 2: R = 0.18, p <2e−16; Rep 2 vs Rep 3: R = 0.14, p = 3e−12; Rep 2 vs Rep 1: R = 0.23, p <2e−16). For Fig 5F, the correlations were also robust across independent pairs (Pair 1: R = 0.15, p = 4e−10; Pair 2: R = 0.13, p = 3e−08; Pair 3: R = 0.16, p = 2e−11). These results show that the correlations are not an artefact of shared samples.

      Minor Comments:

      (4) In Figure 1, it could be informative to present data from intermediate timepoints (i.e., 1, 2, and 5 months). Do mutants that affect spore longevity show a progressive enrichment or depletion over time in dormancy, as depicted in the schematic in Figure 1A? Are there differences in kinetics across the different mutants?

      We thank the reviewer for this suggestion. We will add line plots of the logCPM abundance of short-lived and long-lived mutants (relative to 2-week spore mutants) for all timepoints (2 weeks, 1, 2, 5 and 6 months) to Figure 1. The plots show that most short-lived mutants exhibit progressive depletion over time, while most long-lived mutants exhibit progressive enrichment.

      (5) The authors focus on shared gene expression changes in dormancy between yeast spores, killifish diapause embryos, and dormant cancer cells. Are any pathways enriched among yeast-, killifish-, or human-specific changes?

      We focused on pathways shared across species, but we have now also examined pathways enriched among genes that change specifically in each organism. Among the species-specific gene sets, only genes repressed in yeast spores were significantly enriched, with cytoplasmic translation being the most enriched process (p = 4e-11). The killifish- and human-specific gene sets were not significantly enriched for any functional terms. These results will be included as a supplementary figure.

      Reviewer #3:

      In this study, the authors use several genome-wide approaches to find commonalities and differences between distinct dormancy models, including S. pombe spores, killifish diapause embryos, and human dormant cancer cells. As G0 states are ubiquitous in nature, yet still understudied, this study provides not only a clear demonstration of an evolutionarily-conserved component in G0 regulation, but also a rich resource of genomics datasets, that will be especially of interest to S. pombe and killifish researchers.

      The main conclusions of the study are that: (1) there are commonalities in dormancy programs across eukaryotic evolution; (2) the uncoupling between transcriptome and translatome is more pronounced in non-dividing cells, particularly at ribosomal protein coding genes; and (3) dormant cells retain dynamic responses to stress, changing their cellular state and maintaining this difference.

      Overall, the study is clearly written, provides large data resources for future research in the dormancy field, and the conclusions are supported by the presented evidence (although point 3 would require further experimental clarification, see below).

      Major Comments:  

      A key consideration when comparing transcriptomes of cycling and dormant cells is the overall RNA quantity in the cells; however, it is not made clear in the manuscript whether this overall level was compared and/or if RNA-seq used spike-in quantification. However, this will directly affect some conclusions; for example there is a conceptual difference between a transcript upregulated in spores and a transcript that appears upregulated in spores but is in fact 'less repressed than average' (resulting in higher FC). While the overall transcript diversity as described will be not affected, this analysis can provide important context. For the highlighted example of ribosomal protein mRNAs, this scenario could be what resulted in an apparent mRNA increase but protein decrease (which would be interpreted as both mRNA stabilization and translation inhibition); if the total mRNA is much lower, then the mRNA levels may be similar (which would then be interpreted as no change in transcription nor mRNA stability, but highlight the importance of translation inhibition). This point was more clearly described in a previous seminal study by the authors

      (Marguerat et al 2012), and so should be made clearer here as well. What is the overall RNA level in cycling cells compared to quiescent cells, and compared to spores? Likewise, what is the overall reduction in total protein levels? Was the overall reduction comparable to the previous study? These overall levels should at least be quantified, which is a straightforward experiment. The current mention of this limitation (two sentences in the last paragraph of the conclusion) is not enough. 

      Accordingly, the term "induced" (in Fig 2 for example) may be misleading, and could be separated into truly "induced" genes and "relatively induced" genes, when normalized to absolute levels. Likewise, Fig S2A and S2I are misleading due to this effect (normalization will tend to show a similar number of up-regulated and down-regulated genes). These panels should be clarified by plotting next to the relative quantification (current panels) a comparison taking overall RNA level into account. This will very likely strongly increase the number of downregulated genes and decrease the number of upregulated genes, and the new lists can also be subjected to GO analysis. 

      The same issue would be important to discuss for the killifish experiment as well.

      We acknowledge that the overall quantities of transcripts and proteins in proliferating cells versus those in different dormant cells are important considerations. As described in the Results and Methods, our study presents relative expression changes between dormant and proliferating cells. We highlight this limitation in the Conclusions: “As is the case for most expression studies, our transcriptome and proteome data reflect relative expression levels between two conditions. It is likely that the absolute cellular numbers of most transcripts and proteins are reduced in dormant cells, as they are in quiescent S. pombe cells (Marguerat et al. 2012). Thus, genes induced in dormant cells relative to active cells might be repressed in absolute levels, but to a lesser extent than most other genes.” We also make it clear in the concluding sentences for different sections that our data refer to relative changes (e.g., “Accordingly, several transcripts and proteins were differentially expressed in offspring from 5month-old spores relative to offspring from 2-week-old spores, including 199 mRNAs, 223 proteins, and 33 long non-coding RNAs”). We will carefully review the manuscript, including the Abstract and figures, to further clarify this point, e.g., by using "relatively induced" or “higher relative abundance”. 

      We would like to note, however, that relative quantification, normalised to average expression, focusing on genes that become more or less enriched relative to average genes in the condition of interest compared to a control condition, is a widely accepted and biologically meaningful approach for identifying expression signatures that specify the condition of interest. This is also the principle for qPCR and western analyses, where housekeeping gene normalisation is common. If the absolute expression of all or most genes decreases in dormant cells (which is likely), it would not be meaningful to determine functional enrichments among these genes. Relative expression data help distinguish groups of genes that increase or decrease more than most other genes, reflecting cellular regulation and functional signatures.

      However, we fully agree that the overall quantities of transcripts and proteins in proliferating cells versus those in different dormant cells offer a complementary perspective. Therefore, we are quantifying the overall RNA and protein levels in yeast spores compared to proliferating cells as well as in killifish diapause embryos compared to actively developing embryos. If successful, these results will provide useful context for the relative expression data and will be included in the revised manuscript.  

      For spore offspring stress experiments, the estimated number of cell divisions after spore germination should be indicated. It appears over 20, which would confirm the authors' conclusion that an epigenetic state is induced and persists over multiple rounds of replication and underlie improved heat resistance, indeed hinting at transcriptional memory through chromatin modification. As the phenotype is tested at a population-level, it is unclear whether every spore is equally able to impart this phenotype, and for how long the stress resistance response persists. Moreover, it may be clearer to test heat resistance in log-phase cells, as in the current experimental setup cells are grown to stationary-phase before plating; however, stationary-phase cultures are more heterogenous and more heatresistant.

      We agree, and several of these issues are already addressed in the manuscript. First, regarding the number of cell divisions, the offspring cells were obtained by germinating spores in rich medium and allowing them to grow to mid-exponential phase for approximately 6 generations, as described in the Results (p. 24). Second, for the log-phase testing, we state in the Methods (p. 43) that cultures were adjusted to OD600 = 0.2 and grown to OD600 = 0.6 before stress treatment and plating. Thus, all assays were in fact already performed on log-phase cells.

      We will further emphasise these points in the revised manuscript.

      Yes, our experiments were conducted at the cell population level, and we therefore cannot distinguish whether there is uniform transmission of the transcriptional and phenotypic legacy of dormancy across all germinating spores or whether single cells show heterogeneity within the population in this respect. While this is an interesting question, it would be too technically challenging and time-consuming to pursue this project within the framework of the current study.

      Note also that using 3-fold serial dilutions (instead of more commonly used 10-fold) means that the differences shown in Fig 4M are mild. Plating duplicates (at log-phase) and imaging at several times of growth would be necessary to have a clearer view of the result.

      We fully agree that the serial dilution assay for stress resistance should be improved given the subtle differences. We are repeating the spot assay with 10-fold serial dilutions as suggested, imaging plates at multiple time points, and including sufficient repeats to strengthen the confidence in this result.

      Minor Comments:

      One point for clarification in the introduction is that there is a scale difference between cellular dormancy (at the level of a cell) and organismal dormancy such as diapause (in which the dormancy qualifies the whole organism; typically this will involve slower metabolism, but not necessarily the arrest of the cell cycle for every cell in the organism). As diapause can take different forms depending on organism, detailing this process for the turquoise killifish model may clarify the phenotypic commonalities between these models. Indeed, as pointed out by the authors, several mutants show opposite effects for stationary phase viability and for dormant spore viability, highlighting the diversity of G0 states.

      We agree that there may be a difference between cellular dormancy, in which individual cells arrest their cell cycle, and organismal dormancy, such as diapause, in which individual cells may differ in cell-cycle arrest. However, it has been shown in killifish that all cells throughout the diapause embryo exit the cell cycle and become quiescent (Dolfi et al. 2019), as may be expected given that these embryos can remain dormant for up to two years. We will highlight this aspect more clearly in the Introduction. 

      The title of the manuscript may gain from also mentioning some of the insights (instead of "Gene function and expression of X and Y", "Gene function and expression in X and Y shows Z").

      We agree and will change the title to “Gene function and expression profiling in yeast spores, killifish diapause embryos, and their offspring cells reveal common regulatory features of dormancy

      The Venn diagram in Fig 1D may not be the best way to represent the data; by definition, multiple overlaps here will be zero (between "long-lived spores" and "short-lived spores" and between "long-lived cells" and "short-lived cells"). A table or an upset plot may be useful there. Note that the gained space in Fig 1 may be used to provide examples of mutants in each GO category.

      We agree and will replace the Venn diagram in Figure 1D with an UpSet plot, which better represents the overlapping and non-overlapping categories. 

      Reviewer #4:

      Specific Comments:

      There is a dissonance between the apparent upregulation of autophagy genes during dormancy in both systems and the observation that loss of autophagy genes enhance dormancy. While the authors brush this off by noting "that genes regulated in a given cellular state often do not overlap with those functionally required for that state" (an argument that undermines their whole analysis), it raises the possibility that the process signatures they report are not, in fact, functionally-linked to dormancy and could be coincidental. What would make the expression analysis more convincing would be functional data showing that at least one of the upregulated genes in one of the systems is important for dormancy.

      We respectfully disagree with this assessment. Please note that this apparent paradox between autophagy gene regulation and spore phenotype is highlighted and discussed in the manuscript, and our data actually confirm the importance of autophagy in dormant spores when considered carefully. It is not correct to say that ‘loss of autophagy genes enhance dormancy’. Although autophagy mutants show increased lifespan, they also show decreased stress resiliency. Stress resilience is a key feature and purpose of dormancy, so the loss of autophagy function would clearly be a problem for dormant cells, consistent with the induction of autophagy genes in spores. The surprising trade-off between processes (including autophagy) that support spore longevity and those that support stress resilience is a key finding of our study.

      Regarding the request for functional data linking at least one upregulated gene to dormancy, we note that we have already provided this at a scale far beyond a single gene. In fact, we identified as many as 600 genes that are differentially expressed in spores and, when deleted, cause spore phenotypes (altered stress resilience and/or lifespan). Moreover, the processes significantly enriched among these 600 genes, including protein translation, ribosomes, TCA cycle, and autophagy, are the same processes most enriched among the differentially expressed genes. This significant process-level convergence between functional and expression data provides compelling evidence that our expression signatures are not coincidental but largely reflect roles in dormancy.

      It is not clear how the bar-coding experiment was controlled for mutants that make defective spores (eg poor spore walls) rather than being required for dormancy per se. As the authors note, several of the mutants with the strongest effects (shortening lifespan of the spores) have been previously identified in screens for sporulation or spore wall defects, consistent with those genes playing a specific role in proper spore assembly rather than a general function in dormancy.

      The experimental design was carefully set up to avoid the contribution of mutants that do not sporulate or fail to produce mature spores. After sporulation, samples were heatshocked at 43°C for 3 days and stored in water for at least 2 weeks prior to starting the longevity assay. These conditions will kill any remaining vegetative cells; hence, only spores that can withstand these treatments will be included in the barcode measurements. All abundance values were also normalised to the abundance of each mutant that regrew after two weeks of spore ageing, so any differences in abundance should be caused by our conditions of interest. Thus, mutants with sporulation defects or that fail to form viable spores would be substantially depleted before this normalisation point and would therefore not be included in the subsequent analysis; if they were included, they should not show different abundances across our postsporulation conditions. Nevertheless, we cannot rule out that some of the short-lived mutants reflect problems during sporulation rather than spore traits, as suggested by overlaps with the published sporulation screen. However, this overlap is limited to a very few genes (among 416 short-lived spore mutants), as described in the Results. 

      In this context, we also comment on a broader issue known in the ageing field. Short-lived mutants are less likely to function in ageing-related processes than long-lived mutants, as any perturbation that compromises cell integrity or general fitness – including poor spore wall assembly – will compromise survival regardless of its specific relevance to dormancy regulation. Thus, the long-lived mutants in our screen are more revealing of ageing-related processes. We will clarify and better describe these perspectives in the revised manuscript. 

      It would be helpful to make the data - or at least the lists of genes identified in the screen and the up and downregulated transcripts/proteins available as supplemental information.

      Please note that we provide extensive Supplemental Datasets S1 to S6 that include this very information in table form (genes identified in the Bar-seq screens, differentially expressed RNAs and proteins across the different conditions), along with additional useful data from our large-scale assays. 

      There are at least two different points of diapause in Killifish. It was not entirely clear which diapause was analyzed here. This should be clarified.

      We described the Diapause II stage in the Introduction as the most prominent dormant state and commonly studied state in N. furzeri. In the Results (p. 12), we stated, “To uncover conserved aspects of dormant states between yeast and vertebrates, we analyzed the transcript and protein signatures of N. furzeri diapause II embryos, henceforth called diapause embryos,….”. We also mentioned Diapause II in the Methods. 

      The data that offspring from older or heat-shocked spores are more stress resistant (Figure 4M) is not convincing. Serial dilution assays as shown are more qualitative than quantitative and an actual quantitative measure (eg. c.f.u.'s per cell plated) would be better and would allow statistical confidence to be calculated.

      Serial dilution assays are widely used and accepted to assess differences in stress resistance. The problem with CFUs is that they only determine the proportion of viable cells, while stress resistance also incorporates growth (e.g., stress-sensitive cells may survive the stress but grow more slowly in its presence). However, we agree that the current data in Fig. 4M are not convincing. We are repeating the spot assay with 10-fold serial dilutions, imaging plates at multiple time points, and including sufficient repeats to strengthen the confidence in this result. This is in response to a similar concern raised by Reviewer 3. We will also determine CFU counts, which would provide a more quantitative measure for statistical confidence, should the stress resistance be primarily reflected in cell viability. If necessary, for a more quantitative growth assay allowing statistical analysis, we may also analyse control and stressed cells growing in liquid cultures. 

      Description of the revisions that have already been incorporated in the transferred manuscript

      We have started conducting additional experiments and making text changes to the manuscript, as described in the specific points above. At this stage, we do not provide a partially revised manuscript, but we will provide a fully revised one when everything is ready. 

      Description of analyses that authors prefer not to carry out

      Reviewer 2:

      Comment 1: The finding that a set of gene expression changes in dormancy is shared between yeast spores and killifish diapause embryos is very interesting and raises the question of whether the genetic determinants of stress resilience or longevity in dormant states are also shared. For instance, do any genes identified in the genetic screen as critical for resilience to heat stress in yeast spores also show a similar phenotype in killifish diapause embryos?

      We used the genome-wide deletion library in fission yeast to systematically screen for genes required for spore resilience and longevity. A comparably large-scale functional interrogation is not possible for killifish diapause embryos. Generating deletion-mutant lines for even a single gene in killifish is quite a lengthy and costly effort and would not be realistic within the scope of a revision. However, we agree that an exciting direction for future studies is to assess what conserved genes contribute to dormancy function across species.

    1. Author response:

      The following is the authors’ response to the previous reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      The authors sought to determine how Rif1 contributes to DNA replication timing (RT), transcriptional regulation, and embryonic development using zebrafish. They generated a maternal-zygotic rif1 knockout line and examined developmental phenotypes, genome-wide replication timing profiles, RNA-seq, and nascent transcription (SLAM-seq) during early embryogenesis.

      Their major findings in this manuscript are

      (1) Rif1 is not essential for zebrafish viability, unlike its partially essential role in mice.

      (2) Rif1 deficiency causes defects in female sex determination, delayed epiboly, and reduced primitive erythropoiesis.

      (3) Genome-wide RT is altered by Rif1, but developmental stage has a much larger influence than Rif1 itself.

      (4) Rif1 is required for the proper maturation ("sharpening") of the RT program during development rather than for specific developmental RT switches.

      (5) Rif1 has a much stronger effect on transcription during zygotic genome activation (ZGA) than on replication timing at these early stages.

      (6) Loss of Rif1 leads to increased expression of early zygotic genes, indicating that Rif1 normally suppresses widespread transcription during ZGA.

      Overall, the work proposes that Rif1 independently regulates replication timing and transcription, with these two functions becoming most prominent at different developmental stages.

      The major strengths of the manuscript are as follows.

      (1) the study combines multiple genome-wide approaches including whole-genome RT profiling, RNA-seq, SLAM-seq in combination with gene KO and developmental analyses.

      (2) One of the strongest points is that the authors conducted the analyses at multiple developmental stages rather than a single point.

      (3) The most important conclusion is that the Rif1 regulates transcription during development in a manner largely independent of its RT function, which was further strengthened by the additional data provided in the revised manuscript.

      On the other hand, the weakness of the manuscript includes the followings.

      (1) Limited mechanistic insight. The questions such as where Rif1 binds on the chromatin (in relation to the transcriptional promoters/ enhancers and replication origins).

      (2) Which functional domains of RIf1 are involved in regulation of transcription and replication (Is PP1 recruitment required for transcription regulation?) are not addressed.

      (3) Since Rif1 is known to be involved in chromatin organization/ nuclear architecture regulation, the studies addressing this (Hi-C, compartment analyses, ATAC seq etc) would provide important mechanistic information.

      (4) Female sex determination phenotype is intriguing, but it remains largely descriptive, and its mechanisms are elusive at the moment.

      Overall, the results support the authors' conclusions and they have successfully provided answers to the authors' original questions on developmental roles of Rif1 in RT and transcription in vertebrate.

      Comments on revised version:

      The authors responded to my comments in a largely satisfactory manner. They have conducted additional analyses and concluded that Rif1 regulates transcription during ZGA largely independently of its classical RT function, which is an important finding.

      Although authors did not examine origin firing and replication fork rate in rif1 KO cells, which I suggested in my original review, this can be saved for their future studies.

      I think the revised manuscript has been improved and provides important basic information on the functions of the conserved Rif1 protein in RT and transcriptional regulation.

      I have no further recommendation for additional experiments or data analyses.

      We thank the reviewers for their public evaluations of the manuscript.

      Reviewer #2 (Public review):

      This study by Masser et al. analyzes global replication timing and gene expression in rif-1 null zebrafish. This work is an extension of their previous report of the normal replication timing pattern during wild-type zebrafish development. The major valuable finding here is that Rif1 is not essential for viability in zebrafish, and - counter to expectation from studies in cultured cells and other species - late replication does not strongly depend on Rif1. Instead, the data suggest that Rif1 subtly sharpens replication timing pattern during normal development rather than function generally to delay replication timing. In the absence of Rif1, the normal pattern establishment is somewhat delayed. The authors also document some changes in expression during development with more genes being repressed by Rif1 than activated at some early stages.

      The study and analysis are generally rigorous, and the conclusions are supported by convincing data. Given the strong link between replication timing and cell type/development, studying timing in a whole developing organism is important. The experimental approach is technically challenging, particularly the bioinformatic analysis. The scientific advance here is largely confined to documenting the timing of Rif1-affected transcription, the unanticipated effect of the rif1 deletion on replication timing and on sex determination, though the latter is not explored. The difference in timing of the transcription phenotypes and replication phenotypes suggests they may be very distinct Rif1 roles. The overall study a useful set of findings and detailed data for future work.

      Loss of Rif1 did not affect viability, but it did strongly influence sex determination, resulting in a lower population of females. This effect is the strongest organismal phenotype, but the study provides no mechanistic explanation for the loss of females from the data gathered here.

      Comments on revised version:

      We are generally satisfied with the revised version of this manuscript.

      We thank the reviewers for their public evaluations of the manuscript.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      Desingu et al. show that JEV infection reduces SIRT2 expression. Upon JEV infection, 10-day-old SIRT2 KO mice showed increased viral titer, more severe clinical outcomes, and reduced survival. Conversely, SIRT2 overexpression reduced viral titer, clinical outcomes, and improved survival. Transcriptional profiling shows dysregulation of NF-KB and expression of inflammatory cytokines. Pharmacological NF-KB inhibition reduced viral titer. The authors conclude that SIRT2 is a regulator of JEV infection.

      This paper is novel because sirtuins have been primarily studied for aging, metabolism, stem cells/regeneration. Their role in infection has not been explored until recently. Indeed, Barthez et al. showed that SIRT2 protects aged mice from SARS-CoV-2 infection (Barthez, Cell Reports 2025). Therefore, this is a timely and novel research topic. Mechanistically, the authors showed that SIRT2 suppresses the NF-KB pathway. Interestingly, SIRT2 has also been shown recently to suppress other major inflammatory pathways, such as cGAS-STING (Barthez, Cell Reports 2025) and the NLRP3 inflammasome (He, Cell Metabolism 2020; Luo, Cell Reports 2019). Together, these findings support the emerging concept that SIRT2 is a master regulator of inflammation.

      We thank the reviewer for his/her valuable time, clear summary, and critical comments on the work.

      Weaknesses:

      (1) Figures 2 and 3. Although SIRT2 KO mice showed increased viral titer, more severe clinical outcomes, and reduced survival upon JEV infection, the difference is modest because even WT mice exhibited very severe disease at this viral dose. The authors should perform the experiment using a sub-lethal viral dose for WT mice, to allow the assessment of increased clinical outcomes and reduced survival in KO mice.

      We thank the reviewer for the valuable recommendation. We conducted an experiment using a sub-lethal viral dose of 5 × 10^2 PFU in 14-day-old wild-type (WT) and SIRT2 knockout (KO) mice to evaluate clinical outcomes. Our findings showed a significant reduction in survival rates among the SIRT2-KO mice compared to the wild-type mice (Figure 2O).

      (2) Figure 5K-N, the authors examined the expression of inflammatory cytokines in WT and SIRT2 KO cells upon JEV infection, in line with the dysregulation of NF-kB. It has been shown recently that SIRT2 also regulates the cGAS-STING pathway (Barthez, Cell Reports 2025) and the NLRP3 inflammasome (He, Cell Metabolism 2020; Luo, Cell Reports 2019). Do you also observe increased IFNb, IL1b, and IL18 in SIRT2 KO cells upon JEV infection? This may indicate that SIRT2 regulates systemic inflammatory responses and represents a potent protection upon viral infection. This is particularly important because in Figure 7F, the authors showed that SIRT2 overexpression reduced viral load even when NF-KB is inhibited, suggesting that NF-KB is not the only mediator of SIRT2 to suppress viral infection.

      We agree with the suggestion made by the reviewers. We have quantified the transcript levels of IFNb, IL1b, and IL18 and found that the expression of these genes was increased in JEV-infected SIRT2-KO mice compared to wild-type mice (Figure S5D-S5F). Additionally, we acknowledge the reviewers' comments regarding the role of SIRT2 in regulating systemic inflammatory responses and its significant protective effect against viral infections. Furthermore, NF-κB is not the only mediator involved in SIRT2's suppression of viral infections; other molecular mechanisms may also contribute to this process.

      Reviewer #2 (Public review):

      The manuscript by Desingu et al., explores the role of SIRT2 in regulating Japanese Encephalitis Virus (JEV) replication and disease progression in rodent models. Using both an in vitro and an in vivo approach, the authors demonstrate that JEV infection leads to decreased SIRT2 expression, which they hypothesize is exploited by JEV for viral replication. To test this hypothesis, the authors utilize SIRT2 inhibition (via AGK2 or genetic knockout) and demonstrate that it leads to increased viral load and worsens clinical outcomes in JEV-infected mice. Conversely, SIRT2 overexpression via an AAV delivery system reduces viral replication and improves survival among infected mice. The study proposes a mechanism in which SIRT2 suppresses JEV-induced autophagy and inflammation by deacetylating NF-κB, thereby reducing Beclin-1 expression (an NF-κB-dependent gene) and autophagy, which the authors consider a pathway that JEV exploits for replication. Transcriptomic analysis further supports that SIRT2 deficiency leads to NF-κB-driven cytokine hyperactivation. Additionally, pharmacological inhibition of NF-κB using Bay 11 (an IKK inhibitor) results in reduced viral load and improved clinical pathology in WT and SIRT2 KO mice. Overall, the findings from Desingu et al. are generally supported by the data and suggest that targeting SIRT2 may serve as a promising therapeutic approach for JEV infection and potentially other RNA viruses that SIRT2 helps control. However, the paper does fall short in some areas. Please see below for our comments to help improve the paper.

      We thank the reviewer's valuable recommendation. We measured NF-kB acetylation in JEV-infected Neuro-2a cells treated with Ad-null or Ad-SIRT2. Our findings show that levels of NF-kB acetylation and JEV-NS5 were reduced in the SIRT2-overexpressing cells (Figure S6).

      We conducted an experiment using a sub-lethal viral dose of 5 × 10^2 PFU in 14-day-old wild-type (WT) and SIRT2 knockout (KO) mice to evaluate clinical outcomes. Our findings showed a significant reduction in survival rates among the SIRT2-KO mice compared to the wild-type mice (Figure 2O).

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      In Figures 5C-F, the text is very small.

      Thanks for raising this point. We have increased the text size in the revised Figures 5C-F

      Reviewer #2 (Recommendations for the authors):

      Major concerns:

      (1) Line 71: The introduction does not adequately cite existing work demonstrating the role of SIRT2 in viral infections, including other RNA viruses. It would be more effective to summarize the current literature (similar to lines 162-165) rather than stating that the role of SIRT2 in RNA virus infection is largely unknown.

      We thank the reviewer for the valuable suggestion to improve the manuscript substantially. We have cited existing work demonstrating the role of SIRT2 in viral infections, including other RNA viruses, in the introduction, as suggested.

      (2) Figure 1C: The image should be quantified to state that the observation is statistically significant.

      Thank you for the valuable suggestion. We have quantified the proteins SIRT2, LC3 I, LC3 II, p62, and Beclin in Mock- and JEV-infected Neuro-2a cells, as well as in mouse brain Western blots. These results, along with representative blots (Figure 6I-6J) and n-number-related blots, are presented graphically along with p-values in supplementary figures 7A-7B. Our analysis indicates that these proteins are expressed at statistically significant levels.

      (3) Figure 1I: What tissue is 1I? not stated in the manuscript text or the figure legend.

      Thank you for pointing that out. These samples are from mouse brains. We have included this information in both the text and the figure legend of the revised manuscript.

      (4) Figure 2A: How does Sirt2 expression in WT-infected cells compare to the levels observed in the KD? Are they at comparable levels?

      Thank you for highlighting an important point. We used control siRNA to compare SIRT2 knockdown in SIRT2-siRNA-treated cells in JEV infection. In Figure 2A, “control siRNA” was labelled as “control.” In the revised Figure 2A, we updated this to read “control siRNA.”

      (5) Figure 2L-N: Clinical outcome comparing WT and SIRT2KO mice, JEV-infected mice seems modest. Can statistical analysis be performed to determine whether the results are statistically significant?

      We agree with the suggestion. Clinical signs (Figure 2L) and paralysis (Figure 2M) onset were earlier in SIRT2-KO mice compared to WT mice, and the survival curve (Figure 2N) shows statistical significance. We conducted an experiment using a sub-lethal viral dose of 5 × 10^2 PFU in 14-day-old wild-type (WT) and SIRT2 knockout (KO) mice to evaluate clinical outcomes. Our findings showed a significant reduction in survival rates among the SIRT2-KO mice compared to the wild-type mice (Figure 2O).

      (6) Figure 3: AGK2 can also inhibit other Sirtuins. Thus, to test the contribution of other Sirtuins, the experiment could be repeated using wild-type and Sirt2 KO mice.

      We agree with the suggestion. We repeated the experiment using wild-type and SIRT2-KO mice and found that the differences in survival rates were statistically insignificant between JEV-infected wild-type mice treated with AGK2 and JEV-infected SIRT2-KO mice treated with AGK2 (Figure 3K).

      (7) Figure 5: A-B: Clearly label diagrams and explain what is being compared. G-I: Please annotate genes in the heat maps and volcano plots.

      Thank you for pointing out an important aspect. The figures include several genes that may not be easily visible at readable levels in the main figure. To address this, we have enlarged the figures and labelled them with the gene names in a clearer format, as shown in the supplementary Figures S2-S4. Additionally, we have updated the figure legend for Figure 5 to include this information.

      (8) Line 230-232: "Taken together, these findings reveal that JEV infection negatively regulates SIRT2 levels, resulting in a concomitant increase in acetylated NF-κB mediated virus replication". Data does not support this statement. The experiments presented do not demonstrate that acetylated NF-kB mediates viral replication. In fact, it would be good to measure NF-kB acetylation in AdSIRT2 JEV-infected cells compared to WT-infected cells, to verify that the acetylation of NF-kB is truly linked to SIRT2 expression levels.

      We thank the reviewer for his/her valuable recommendation. We measured NF-kB acetylation in JEV-infected Neuro-2a cells treated with Ad-null or Ad-SIRT2. Our findings show that levels of NF-kB acetylation and JEV-NS5 were reduced in the SIRT2-overexpressing cells (Figure S6).

      (9) Figure 6E: The Graph is hard to interpret. It is also missing a figure legend/key, and also a misplaced A in the image.

      Thank you for highlighting an important point. We have highlighted NF-κB and other colour representations in the signalling network graph (Figure 6E). We revised the figure legend for clarity and removed the misplaced "A" from the figure.

      (10) Line 260-261: "These results indicate that SIRT2 regulates JEV replication through the NF-κB-beclin-autophagy axis.". Data does not support this statement.

      We modified the statement as follows: “These results suggest that SIRT2 regulates JEV replication through the NF-κB-autophagy axis.

      (11) Line 270: Do the authors mean decrease? Bay 11 is an NF-κB inhibitor.

      We agree with the suggestion. This is a typographical error. We have replaced “increase” with “decrease” in the revised manuscript.

      (12) Figure 8: The phenotype seems modest. Have the authors considered that Sirt2 may regulate JEV via other acylation targets?

      We agree with the reviewers' suggestion. NF-κB is not the only mediator involved in SIRT2's suppression of viral infections; other molecular mechanisms may also contribute to this process.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      Characterization of a dissociable Mediator subunit implicated in cellular pathways, particularly lung alveolar function, and HIV latency is conceptually interesting.

      Strengths:

      The strengths of this study are:

      (1) Demonstration of MED16 dissociation from the core Mediator complex and formation of a subcomplex containing MED16, upstream-binding protein 1 (UBP1), and transcription factor cellular promoter 2 (TFCP2) by elegant biochemical fractionation and immunoblotting analysis.

      (2) Defining nine N-terminal WD-40 repeats (WDRs) of MED16 as a Mediator-incorporating module and the C-terminal ⍺β-domain (157 amino acids) important for interaction with the UBP1-TFCP2 heterodimeric complex.

      (3) Illustration of a weak hydrophobic interaction between MED16 and the Mediator core that could be disrupted by 1,6-hexanediol, but not by its 2,5-hexanediol isomer nor by high salt (500 mM NaCl) disruption.

      (4) Classification of UBP1-upregulated cellular genes typically containing binding sites flanking the transcription start site (TSS) in contrast to UBP1-downregulated genes often containing a TSS-overlapping UBP1-binding site

      (5) Presenting evidence for Mediator complex-dissociated free MED16-repressed HIV promoter activity through functional association with UBP1 and showing bromodomain-containing protein 4 (BRD4) inhibitor JQ1 that potentially disrupts BRD4-inhibited HIV-1 transcription elongation could lead to reversal of HIV-1 latency.

      Weaknesses:

      Nevertheless, foreseeable weaknesses include:

      (1) No clear demonstration of MED16-UBP1-TFCP2 indeed forming a trimeric core subcomplex in regulating cellular gene transcription and HIV-1 promoter inhibition

      We appreciate this insightful comment from the reviewer. The physical interaction between MED16 and the UBP1–TFCP2 heterodimer was uncovered serendipitously via biochemical fractionation. Specifically, UBP1 and TFCP2 were identified in gel-filtration fractions containing free MED16 that eluted separately from the intact core Mediator complex (Figures 1D–1F). This biochemical observation suggested to us a potential functional linkage between MED16 and these two transcription factors. Subsequently, our functional assays further clarified this regulatory relationship: UBP1 and TFCP2 do interact with MED16 that is required to be fully assembled into Mediator complexes to exert transcriptional control. Truncation of MED16’s N-terminal WD40-repeat (WDR) domain (MED16ΔWDR) eliminates MED16 integration into the Mediator complex. Notably, this MED16ΔWDR mutant still retains an intact C-terminal αβ-domain capable of binding UBP1 yet completely loses the capacity to support UBP1-dependent transcription. Collectively, these data demonstrate that UBP1–TFCP2 engage MED16 as a component of the complete Mediator complex to govern target gene expression in cells.

      We have updated the abstract and full manuscript to present this model more clearly and coherently throughout the text.

      (2) No validation of transcriptomic datasets and pathways identified.

      We thank the reviewer for this comment. Since our RNA-seq analysis identified SFTP family genes (SFTPA1, SFTPA2, SFTPB, SFTPD) as UBP1-MED16 co-regulated targets, and these are lung-specific surfactant protein genes, we have now performed qRT-PCR validation in the A549 human lung adenocarcinoma cell line. The results confirm that knockdown of MED16 largely attenuates the expression of these SFTP genes (see Author response image 1) and other UBP1 target genes identified in our RNA-seq dataset.

      Author response image 1.

      qRT-PCR validation of SFTP gene family expression (SFTPA1/A2/B/D) in A549 cells

      (3) Use of mostly artificial reporter gene constructs and non-HIV host cells (e.g., human 293T embryonic kidney cells, human HeLa cervical cancer cells, and mouse HT pancreatic cancer cells) for examining MED16/UBP1-regulated HIV transcription.

      To overcome the limitations of artificial reporter systems, we have managed to utilize multiple complementary approaches beyond reporter assays, including: (i) RNA-seq analysis of endogenous gene regulation, (ii) biochemical co-IP and gel filtration experiments, (iii) immobilized template transcription assays that directly measure PIC assembly and nascent RNA production, and (iv) validation in the J-Lat 10.6 CD4+ T cell line harboring an integrated latent HIV-1 provirus, where MED16 overexpression suppresses HIV-1 reactivation.

      Unfortunately, the direct infection experiments with replication-competent HIV-1 were not feasible as our institution does not have the biosafety level 3 (BSL-3) containment facilities.

      (4) Inconsistent use of 293T and HeLa cells in the characterization of dissociated MED16 interaction with UBP1 and TFCP2.

      For biochemical characterization in this study, HEK293T cells were primarily utilized for overexpression-based co-immunoprecipitation (Co-IP) and domain-mapping assays owing to their superior transfection efficiency. In contrast, HeLa cells were employed for gel-filtration chromatography and endogenous Co-IP, as fractionation of HeLa nuclear extracts represents a well-established workflow for purifying native protein complexes. Critically, the physical interaction between MED16 and the UBP1–TFCP2 heterodimer was consistently detected in both HEK293T whole-cell lysates and HeLa nuclear extracts across all assays.

      (5) In vitro transcription using immobilized DNA templates was not performed to a high standard, thus failing to convincingly show MED16/UBP1-inhibited HIV-1 transcription preinitiation complex formation.

      We appreciate the reviewer’s careful assessment of the immobilized template assay. While we recognize the technical challenges inherent in this approach, we want to emphasize that the proposed model—that MED16-UBP1 inhibits HIV-1 transcription at the level of PIC assembly—does not rest solely on this single experiment.

      Multiple independent lines of evidence converge on this model:

      (1) The MED16-UBP1 inhibition depends on the UBP1 binding site overlapping the TSS: a chimeric reporter with the UBP1 binding site placed at the TSS is inhibited by MED16, whereas placing it upstream does not show inhibition, demonstrating the UBP1 binding site-specific repression (Fig 6A-C).

      (2) MED16 overexpression inhibits HIV-1 reporter activity in a manner depending on interaction with UBP1. Deletion of the MED16 αβ-domain (MED16Δαβ), which abolishes MED16-UBP1 interaction, completely abrogates the inhibitory effect (Fig 5E-G).

      (3) The MED16-UBP1 inhibition of HIV is independent of TAR-mediated elongation (Fig S2B-C) and HDAC-mediated deacetylation (Fig S2A), consistent with an inhibition mechanism operating at the initiation stage rather than at the post-initiation steps.

      (4) Upon MED16 overexpression, the immobilized template assay shows reduced CDK8 binding and Pol II pSer5 signals, along with TFIIB retention, providing mechanistic evidence that is consistent with the aforementioned functional observations.

      Thus, the model is supported by convergent evidence from reporter assays, domain-mapping experiments, pharmacological inhibition, and in vitro biochemical reconstitution. In the revised manuscript, we have further clarified how these complementary approaches collectively support the PIC inhibition model.

      Reviewer #2 (Public review):

      Summary:

      The article from Zheng et al. proposes an interesting hypothesis that the Med16 subunit of Mediator detaches from the complex, associates with transcription factor UBP1, and this complex activates or represses specific sets of genes in human cells. Despite my excitement upon reading the abstract, I was concerned by the lack of rigor in the experimental design. The only statement in the abstract that has some experimental support is the finding that Med16 dissociates from the Mediator and forms a subcomplex, but the data shown remain incomplete.

      We would like to first address a core conceptual point that we believe underpins several of the reviewer’s concerns.

      We respectfully disagreed that the reviewer summarized our proposed model as a pathway where “Med16 detaches from the complex, associates with transcription factor UBP1, and this complex activates or represses specific sets of genes.” We acknowledge that phrasing in our original manuscript may have created this misleading interpretation, yet this is not the mechanistic model we intend to convey. We identified the MED16–UBP1–TFCP2 interaction serendipitously during biochemical fractionation: UBP1 and TFCP2 co-eluted with free MED16 in gel-filtration fractions that were fully separated from the intact core Mediator complex. While this biochemical result guided our subsequent functional investigation into MED16–UBP1–TFCP2 crosstalk, we never intend to propose that a standalone MED16–UBP1–TFCP2 subcomplex can drive transcriptional activation or repression independently of the intact Mediator complex.

      Most importantly, our functional experiments demonstrate that UBP1 and TFCP2 require MED16 as an integral part of the Mediator complex to regulate transcription as shown by domain mapping experiments. Specifically, MED16 uses its N-terminal WDR domain to integrate into the Mediator and its C-terminal αβ-domain to bind UBP1/TFCP2. Deletion of either WDR or αβ-domain is functionally inert in both cellular and HIV-1 reporter assays. Thus, the MED16-UBP1 interaction is functionally relevant because it links these transcription factors to the Mediator complex, not because it forms an autonomous regulatory complex. In another word, UBP1–TFCP2 target MED16 to recruit the whole Mediator complex for governing gene expression in cells.

      We have comprehensively revised the full manuscript to sharply distinguish our initial biochemical observation from the validated functional model. As all experimental approaches carry inherent limitations, we tried our best to validate every major conclusion using multiple orthogonal assays and to draw mechanistic interpretations when results from distinct experimental systems do converge. Our detailed replies to each specific concern from the reviewer are provided below.

      Strengths:

      The authors have preliminary evidence that a stable Med16 complex may exist and that it may regulate specific sets of genes.

      Weaknesses:

      The experiments are poorly designed and can only infer possible roles for Med16 or UBP1 at this point. Furthermore, the data are often of poor quality and lack replication and quantitation. In other cases, key data such as MS results aren't even shown. Instead, we are given a curated list of only about 6 proteins (Figure S1), a subset of which the authors chose to pursue with follow-up experiments. This is not the expected level of scientific process.

      As clarified in our Summary Response above, we thought this reviewer may have misinterpreted our data and model. Overall, our work demonstrates that MED16 acts as a molecular bridge, linking UBP1/TFCP2 to the Mediator complex, not that three proteins form a free-standing subcomplex, and we have extensively revised the manuscript to clarify this.

      Here we also want to address the specific concerns about data completeness and rigor. The full mass spectrometry datasets were not clearly presented in the original submission. We have now reanalyzed the IP-MS data using a more precise quantification approach. Rather than scoring proteins by simple presence or absence, we calculated a bait-preferential score for each protein by comparing its normalized abundance in the MED16 IP to that in the other three Mediator bait IPs (MED1, MED12, CDK8). This score reflects the degree to which a protein is preferentially enriched by MED16 relative to other Mediator subunits. The bait-specific candidates identified by this analysis are presented in Fig S1B, and the complete list of MED16-specific candidates is now included. In addition, the raw abundance values and peptide counts for all identified proteins have been compiled and uploaded as supplementary tables. A detailed description of the normalization and scoring procedure is provided in the Methods section

      Furthermore, we have added quantification analysis for key Western blot results throughout the revised figures.

      (1) The data supporting the Med16 dissociation and co-association with UBP1 are incomplete and not convincing at this stage. According to the Methods and text, the gel filtration column was run with "un-dialyzed HeLa cell nuclear extract" and eluted in 300mM KCl buffer. The extracts were generated with the Dignam/Roeder method according to the text. Undialyzed, that means the extract would be between 0.4 - 0.5M NaCl. Under these high salt conditions (not physiological), it's possible and even plausible that Mediator subunits could separate over time. This caveat is not mentioned or controlled for by the authors. Because a putative Med16 subcomplex is a foundational point of the article, this is concerning.

      The data are incomplete because a potential Med16 complex is not defined biochemically. The current state suggests a smaller Med16-containing complex that may also contain UBP1 and other factors, but its composition is not determined. This is important because if you're going to conclude a new and biologically relevant Med16 complex, which is a point of the article, then readers will expect you to do that.

      We appreciate the reviewer’s thorough feedback and address the two core concerns separately below.

      (1) Undialyzed nuclear extracts & high-salt conditions

      Published work confirms Mediator undergoes massive precipitation (~70% loss) upon dialysis to low-salt 100 mM KCl buffer (1), justifying our use of undialyzed HeLa nuclear extracts for biochemical assays. Prior study also demonstrated intact Mediator remains stable in up to 1 M KCl (1). Therefore, MED16 dissociation seen at 300 mM KCl arises from its unique biochemical property, rather than non-specific high-salt damage.

      (2) Biochemical interpretation of MED16-containing fractions

      We have revised ambiguous original wording to clarify our model: we do not intend to propose an autonomous MED16–UBP1–TFCP2 subcomplex functions independently in cells. Gel filtration only captures a biochemical state where MED16 co-elutes with UBP1/TFCP2 separate from core Mediator, which merely inspired our functional follow-up. Three lines of evidence prove UBP1/TFCP2 require fully assembled Mediator to function:

      (i) MED16’s N-terminal WDR domain mediates Mediator integration, while its C-terminal αβ-domain binds UBP1; both interactions can occur simultaneously (Fig 2B).

      (ii) MED16Δαβ incorporates into Mediator but loses UBP1 binding, showing no activity in UBP1-driven and HIV-1 reporter assays (Fig 3G, 5G).

      (iii) MED16ΔWDR retains UBP1 binding yet cannot assemble into Mediator, thus fails to repress HIV-1 transcription (Fig 5F).

      In vitro MED16 separation only reflects its extractable biochemical behavior, not a functional standalone complex. Collectively, our data establish UBP1/TFCP2 recruit the entire Mediator complex via MED16. All relevant manuscript sections have been rewritten to distinguish this preliminary biochemical observation from our validated functional model.

      Equally concerning are the IP-western results shown in Figure 1. In my opinion, these experiments do nothing to support the claims of the authors. The authors use hexanediols at 5% or 10% in an effort to disrupt the Mediator complex. Assuming this was weight/volume, that means ~400 to 800mM hexanediol solution, which is fairly high and can be expected to disrupt protein complexes, but the effects haven't been carefully assessed as far as I'm aware. The 2,5 HD (Figure 1B) experiments appear to simply contain greater protein loading, and this may contribute to the apparent differential results. In fact, in looking at the data, it seems that all MED subunits probed show the same trend as Med16. They are all reduced in the 1,6HD experiment relative to the 2,5 HD experiment. But it's hard to know, because replicates weren't completed and quantitation was not done. There aren't even loading controls. Other concerns about the IP-Western experiments are outlined in point 2.

      Treatment with 10% (w/v) 1,6-hexanediol (1,6-HD) is a well-established method to selectively disrupt weak hydrophobic interactions while maintaining stable protein assemblies. A comparable strategy was recently applied to dissect NEAT1-dependent paraspeckle formation driven by liquid–liquid phase separation (2). Notably, we included 2,5-hexanediol (2,5-HD) as a critical specificity control: as a structural isomer with distinct hydroxyl group positioning, 2,5-HD cannot efficiently disrupt weak hydrophobic contacts and failed to trigger MED16 dissociation (Figure 1B). The divergent outcomes observed side-by-side with equal sample input therefore serve as an internal control, validating that MED16 dissociation is a specific consequence of 1,6-HD treatment.

      We acknowledge mild signal reductions for several other Mediator subunits following 1,6-HD exposure under certain immunoprecipitation (IP) conditions (Figures 1A, 1B). Nevertheless, MED16 exhibits a uniquely pronounced dissociation by 1,6-HD that is consistent across three independent IPs using anti-CDK8, anti-MED1, and anti-MED12 antibodies, in both HEK293T whole-cell lysates and HeLa nuclear extracts. By contrast, the mild depletion of other Mediator subunits varies substantially depending on the antibody and cell extract used, whereas robust MED16 loss is universally observed in all experimental setups we tested.

      (2) At no point do the authors apply rigorous methods to test their hypothesis. Instead, methods are applied that have been largely discredited over time and can only serve as preliminary data for pilot studies, and cannot be used to draw definitive conclusions about protein function.

      We greatly appreciate the reviewer’s emphasis on methodological rigor. We fully concur that individual techniques including protein fractionation, IP-WB, transient transfection, shRNA knockdown, immobilized template and luciferase reporter assays each carry intrinsic limitations when deployed alone. To address this, we employed a panel of orthogonal experimental strategies throughout our work and only draw conclusions supported by convergent results across distinct assays. Our core mechanistic conclusion—that MED16 acts as a molecular bridge linking the UBP1–TFCP2 heterodimer to the intact Mediator complex to control transcription—is validated by multiple independent lines of evidence, rather than resting on a single experimental approach, as elaborated in detail below.

      (a) IP-westerns are fraught with caveats, especially the way they were performed here, in which the beads were washed at relatively low salt and then eluted by boiling the beads in loading buffer. This will "elute" bound proteins, but also proteins that non-specifically interact with or precipitate on the beads. And because Westerns are so sensitive, it is easy to generate positive results. It's just not a rigorous experiment.

      We acknowledge that IP-Western has inherent limitations regarding specificity. To minimize non-specific signals, we included IgG controls in our CDK8 IP experiments (available in raw data) and the boiling elution method has been extensively validated in our hands. More importantly, the interaction between MED16 and UBP1/TFCP2 is not solely supported by IP-Western.

      This interaction was initially observed through co-elution of MED16 with UBP1 and TFCP2 in gel filtration fractions (Fig 1D), confirmed by reciprocal co-IP with anti-MED16 and anti-TFCP2 antibodies in both HeLa NE and the resolved fractions (Fig 1E-F), and further corroborated by in vitro GST pull-down assays showing direct binding between MED16 αβ-domain and recombinant UBP1 (Fig 2C). IP-MS analysis with three biological replicates independently identified UBP1 and TFCP2 as MED16-associated proteins. Each of these methods has different sources of potential artifacts, yet they all converge on the same conclusion.

      (b) Many conclusions relied on transient transfection experiments, which are problematic because they require long timeframes, during which secondary/indirect effects from expression/overexpression will result. This is especially true if the proteins being artificially expressed/overexpressed are major transcription regulators, which is the case here. It is simply impossible to separate direct from indirect effects with these types of experiments. Another concern is that there was no effort to assess whether the induced protein levels were near physiological levels. Protein overexpression, especially if the protein is a known regulator of pol2 transcription (e.g., UBP1 or Med16), will create many unintended consequences.

      The reviewer raises a valid concern about indirect effects from overexpression. To address this, our key conclusions were validated by multiple loss-of-function approaches that do not rely on overexpression alone. Specifically, the conclusion that MED16 is required for UBP1 transcriptional activity is supported by:

      (i) shRNA-mediated MED16 knockdown (Fig 3C);

      (ii) CRISPR-mediated MED16 knockout in five independent frameshift clones with consistent phenotypes (Fig 3E-F);

      (iii) Using a domain-disruption approach, we demonstrated that a UBP1-binding-deficient MED16 mutant (Δαβ) fails to exert the dominant-negative effect on UBP1 activity, as seen with wild-type MED16 (Fig 3G and 6A). All these different methods point to the same conclusion. This makes it unlikely that the effects we see are simply artifacts of overexpression or indirect consequences.

      (c) Many conclusions were made based upon shRNA knockdown experiments, which are problematic because they require long timeframes (see above point), which makes it nearly impossible to identify effects that are direct vs. indirect/secondary/tertiary effects. Also, shRNA experiments will have off-target effects, which have been widely reported for well over a decade. An advantage of shRNA knockdowns is that they prevent genetic adaptation (a caveat with KO cell lines). A minimal test would be to show phenotypic rescue of the knockdown by expressing a knockdown-resistant Med16 (for example), but these types of experiments were not done.

      We agree that shRNA has potential off-target effects, and that is why we did not rely on shRNA as our sole loss-of-function approach. We have generated five independent CRISPR MED16 knockout clones, each with a distinct frameshift mutation, and all five clones showed consistent reduction in UBP1 reporter activity (Fig 3E-F). Furthermore, we performed RNA-seq on MED16 knockout cells in which wild-type MED16 was re-introduced. As presented in Author response image 2, re-expressing MED16 in KO cells can largely restore the expression of UBP1 target genes. These rescue data provide strong evidence that the transcriptional defects are specifically attributable to MED16 loss rather than off-target effects or clonal adaptation.

      Author response image 2.

      Gene profiling of MED16 KO and rescue effect

      (d) Many experiments used reporter assays, which involved artificial, non-native promoters. Reporters are good for pilot studies, but they aren't a rigorous test of direct regulatory roles for Med16 or other proteins. Reporters don't even measure transcription directly. In fact, no experiment in this study directly measures transcription. An RNA-seq experiment was done with overexpressed or Med16 knockdown cells, but these required long timeframes and RNA-seq measures steady-state mRNA, which doesn't test the potential direct effects of these proteins on nascent transcription.

      The two principal reporters used in this study are both based on native promoters. The UBP1 reporter is derived from the mouse α-globin gene promoter, a well-established natural target of UBP1/TFCP2 that contains two endogenous UBP1 binding sites. To enhance sensitivity, we expanded these to six copies, as the α-globin promoter has low basal activity in most cell lines. Critically, this expansion preserved the original promoter architecture, including the CCAAT box, TATA box, and TSS. The HIV-1 reporter is driven by the HIV-1 core promoter (-78 to +60), which contains all elements required for basal transcription and Tat-mediated activation. Thus, both reporters retain the native sequence context of the regulatory elements under study.

      These reporter assays served as initial screening and hypothesis-testing tools. The key functional insights from reporters were then validated in more physiological contexts:

      (i) The position-dependent effect of UBP1 binding (activation when upstream of TSS, repression when overlapping TSS) observed in chimeric reporters (Fig 6A-C) was independently confirmed by motif enrichment analysis of endogenous genes from RNA-seq data (Fig 6D-E).

      (ii) Our immobilized template transcription assays directly measure nascent RNA production from the HIV-1 promoter, showing that MED16 overexpression reduces transcriptional output (Fig 7C). Thus, while reporter assays alone would be insufficient, our conclusion on UBP1-MED16 function are further corroborated by both global genomic analysis and direct in vitro transcription measurements.

      (e) The MS experiments show promise, but the data were not shown, so it's hard to judge. The reader cannot compare/contrast the experiments, and we have no indication of the statistical confidence of the proteins identified. How many biological replicate MS experiments were performed?

      The IP-MS experiments were performed with three biological replicates for each of the four antibodies against MED1, MED12, CDK8, and MED16 respectively. The complete datasets are now provided in the revised manuscript (Supplementary Table 1).

      In addition, we have reanalyzed the data using a more quantitative approach. In the original submission, we classified proteins by a binary cutoff—detected or not detected in MED16 relative to other baits. In the revised analysis, we calculated a bait-preferential score for each protein by comparing its normalized abundance in the MED16 IP to its mean abundance across the other three Mediator baits. This score reflects how strongly a protein is enriched by MED16, rather than simply whether it meets an arbitrary detection threshold. A detailed description of this method is provided in the revised Methods section.

      Notably, using this quantitative method, UBP1 and TFCP2 can also be detected at lower levels in some replicates of the other Mediator baits. This is consistent with our functional model: UBP1 and TFCP2 associate with the whole Mediator complex through MED16. The MED16-biased enrichment pattern, now supported by the bait-preferential score, reinforces the conclusion that MED16 serves as the primary anchor for UBP1/TFCP2 to associate with the Mediator complex.

      (3) The data are over-interpreted, and alternative (and more plausible) hypotheses are ignored. Many examples of this, some of which are alluded to in the points above. For example, Med16 loss or overexpression will cause compensatory responses in cells. An expected result is that Mediator composition will be disrupted, since Med16 directly interacts with several other subunits. Also in yeast, the Robert, Gross, and Morse labs showed that loss of Med16/Sin4 causes loss of other tail module subunits, and this would be expected to cause major changes in the transcriptome. The authors also mention that yeast Med16/Sin4 "alters chromatin accessibility globally" and this would be expected to cause major changes in the transcriptome, leading to unintended consequences that will make data analysis and identification of direct Med16 effects impossible. The unintended consequences will be magnified with prolonged disruption of MED16 levels in cells (e.g., longer than 4h). These unintended consequences are hard to predict or define, and are likely to be widespread given the pivotal role of Mediator in gene expression. One unintended consequence appears to be loss of pol2 upon Med16 over-expression, as suggested by the western blot in Figure 8B. I point this out as just one example of the caveats/pitfalls associated with long-term knockdowns or over-expression.

      We thank the reviewer for raising this important point. Indeed, our new Co-IP and IP-MS data confirm that MED16 knockout leads to partial dissociation of MED23, MED24, and MED25 from the Mediator complex. We agree that this structural perturbation must be carefully considered when interpreting phenotypes from MED16 depletion experiments, and we acknowledge that long-term knockdown or knockout approaches are inherently susceptible to secondary effects and cellular adaptation.

      Author response image 3.

      MED16 knockout impacts on the Mediator complex

      However, our key conclusions are not based solely on long-term depletion experiments. Several lines of evidence, including experiments performed on short timescales without prolonged MED16 loss, converge on the same conclusion:

      First, the MED16 mutant lacking its C-terminal αβ-domain cleanly separates the two functions. This mutant retains the intact N-terminal WDR domain of MED16 and can integrate into the Mediator complex, preserving its structural role and preventing tail module dissociation. Yet it completely fails to exert the competitive inhibition (squelching) effect on the UBP1 reporter that is observed with wild-type MED16 overexpression (Fig 3G), and similarly fails to inhibit HIV-1 reporter activity (Fig 5G). The sole molecular defect of this mutant is its inability to bind UBP1 (Fig 2B). Critically, this overexpression experiment is performed in a wild-type background where the endogenous Mediator complex remains structurally intact. The only variable is whether the overexpressed MED16 can interact with UBP1. This provides strong evidence that the transcriptional effects are mediated specifically through the MED16-UBP1 interaction interface, independent of MED16's structural role in maintaining Mediator integrity.

      Second, the transcriptional changes we observe are not random but show specific functional coherence. If the transcriptomic changes in MED16 knockdown cells were merely secondary consequences of Mediator tail module disruption, we would expect broad, non-specific dysregulation. Instead, the UBP1-MED16 co-regulated genes are enriched for specific biological processes—angiogenesis—which largely align with the known biological functions of UBP1 (Fig 4D-E). This functional specificity is difficult to reconcile with the global, non-specific transcriptional disruption that would be expected from the total Mediator dysfunction.

      Finally, we wish to address the reviewer's observation regarding Pol II levels in Figure 8B. In preparing the revised manuscript, we carefully re-examined our original Western blot data and found that the reduction of Pol II upon MED16 overexpression was not consistently reproducible across independent experiments. We have therefore replaced new Pol II blot in Figure 8B. We note that this revision does not affect any of the conclusions drawn from Figure 8, which focus on the inhibitory effect of MED16 overexpression on HIV-1 latency reversal in J-Lat cells.

      We are grateful for the reviewer’s careful assessment, which encouraged us to refine our data presentation and enhance experimental rigor. The manuscript has been significantly improved as a result.

      Reviewer #3 (Public review):

      Weaknesses:

      (1) The decrease in 1,6-hexanediol-treated cells of MED16 is modest, variable, not quantified, and internally inconsistent. For example, in Figure 1A, 1,6-hexanediol treatment should not have an impact on the level of the protein being directly IP. For MED12 (and CDK8 and MED1 to a lesser extent), 1,6-hexanediol treatment alters the level of the target protein in the IP. Along these lines, Figure 1A shows a no 1,6H-D dependent decrease in MED1 or MED12 levels in the CDK8 IP, whereas Figure 1B does show a decrease. Figure 1A shows no 1,6H-D dependent decrease in CDK8 levels in the MED1 IP, whereas Figure 1B shows a dramatic decrease. MED24 levels in the MED12 IP increase upon 1,6H-D in Figure 1A, but decrease in Figure 1B. Internal inconsistencies of this nature persist in the other Figures.

      We thank the reviewer for this careful observation, and we here clarify the rationale behind our experimental design to resolve the apparent discrepancies between Figures 1A and 1B.

      We first performed co-immunoprecipitation (co-IP) assays using HEK293T whole-cell lysates with three distinct antibodies targeting CDK8, MED1, and MED12, respectively, to pull down intact Mediator complexes. This setup was designed to assess whether 1,6-hexanediol (1,6-HD) impairs Mediator complex integrity and, if so, whether this perturbation affects individual subunits unequally. Across all three independent IP replicates, we observed a uniform trend: most Mediator subunits displayed only mild signal attenuation, whereas MED16 exhibited a striking, dose-dependent reduction upon escalating 1,6-HD concentrations (Fig 1A). Quantitative densitometry of these immunoblot signals has now been incorporated into the revised Figures 1A and 1B to better visualize this difference. Thus, this initial result in Fig 1A indicated that MED16’s interaction with the core Mediator complex is uniquely vulnerable to 1,6-HD disruption, irrespective of which Mediator subunit was used for immunoprecipitation.

      To validate the reproducibility of this phenotype, we replicated the assay in an alternative biochemical system using HeLa nuclear extracts (NEs) (Fig 1B), with 2,5-hexanediol (2,5-HD) included as a critical negative control—this structural isomer cannot disrupt weak hydrophobic protein-protein contacts. Notably, the HeLa NE experiments in Fig 1B were carried out under elevated salt conditions (~300 mM NaCl), in contrast to the 150 mM NaCl buffer used for the HEK293T lysate assays in Figure 1A.

      We want to emphasize that despite these substantial technical disparities between the two experimental setups, both datasets converge on the identical core conclusion: MED16’s association with the core Mediator complex is selectively disrupted by 1,6-HD. This consistent trend is further strengthened by quantitative analysis of immunoblot band intensities from biological replicates, which we have added to the revised figures.

      Minor variability observed for other Mediator subunits between Fig 1A and 1B arises from intrinsic differences in cell type, extraction protocols, and buffer salt concentrations. For this reason, we did not draw mechanistic interpretations regarding the variable signal changes of other subunits across distinct experimental conditions; instead, our analysis focused on the robust, consistent loss of MED16 following 1,6-HD exposure.

      (2) Undermining the value of Figure 1E/F, UBP1 and TFCP2 may also associate with the small amount of MED16 in the 2MDa fractions. This is not tested, and therefore, the conclusion that they just associate with the dissociable form of MED16 is not supported.

      We thank the reviewer for this insightful observation. Indeed, UBP1 and TFCP2 can associate with MED16 in the context of the intact Mediator complex. Figure 1B directly supports this: under 2,5-HD conditions, where MED16 remains integrated into the Mediator, both UBP1 and TFCP2 are co-immunoprecipitated with the Mediator complex (via anti-MED1). This association is lost under 1,6-hexanediol conditions, where MED16 dissociates—suggesting that UBP1 and TFCP2 are tethered to the Mediator through MED16.

      The gel filtration experiment (Fig 1D) further reveals that a portion of MED16 resolves away from the core Mediator complex under these in vitro conditions, and Figure 1E-F shows that UBP1 and TFCP2 co-immunoprecipitated with MED16 in these lower molecular weight fractions. Taken together, these data indicate that UBP1 and TFCP2 can be found in association with MED16 in two biochemically distinguishable states: one integrated into the Mediator complex, and another that has dissociated from it under our experimental conditions. We did not state that UBP1 and TFCP2 associate exclusively with the dissociated form; rather, the dissociated fraction is where we initially identified this interaction, which then led us to investigate its functional significance. The whole manuscript has been extensively rewritten now, and hopefully the confusion has been clarified.

      Our functional data further demonstrate that the transcriptional activities of UBP1 and TFCP2 require the intact Mediator complex. MED16 bridges this interaction through its C-terminal αβ-domain, which binds UBP1/TFCP2, and its N-terminal WDR domain, which anchors MED16 into the Mediator. We have revised the manuscript to clearly distinguish the biochemical observation from the functional model, and we now explicitly state that UBP1 and TFCP2 associate with the Mediator complex through MED16.

      (3) Domain mapping studies in Figure 2 are overinterpreted. Since the interactions could be indirect, it is not accurate to conclude "Therefore, the N-terminal WDR domain of MED16 is crucial for its integration into the Mediator complex, while the C-terminal αβ-domain is essential for interacting with UBP1-TFCP2."

      We fully acknowledge that co-immunoprecipitation (co-IP) assays alone cannot discriminate direct physical binding from indirect protein associations mediated by intermediate partners. Nevertheless, our conclusion that MED16 directly interacts with UBP1 is supported by two orthogonal, independent experimental datasets.

      First, GST pull-down assays using purified recombinant proteins expressed in E. coli confirm direct binding (Figure 2C). This cell-free biochemical system removes all potential cellular bridging factors, unambiguously demonstrating a physical contact between the C-terminal αβ-domain of MED16 and UBP1.

      Second, our mutational functional analyses further rule out an indirect interaction model. Deletion of the unique 36-residue USP peptide in UBP1 completely abrogates MED16 binding (Figure 2F, comparison between ΔSAM and DBD truncations). Reciprocally, MED16 mutants lacking the C-terminal αβ-domain lose all capacity to associate with UBP1. Importantly, both truncation mutations yield identical functional defects in UBP1-driven and HIV-1 luciferase reporter assays (Figures 3G and 5G). If this complex assembly relied on an uncharacterized bridging protein, it would be statistically improbable for two distinct, structurally unrelated deletions (USP removal on the UBP1 side and αβ-domain truncation on the MED16 side) to independently disrupt the same indirect linkage and generate identical loss-of-function phenotypes.

      Collectively, the congruent results from cell-free in vitro biochemistry and targeted mutational functional assays provide robust evidence for a direct, specific physical interaction between MED16 and UBP1.

      (4) A close examination of Figure 2C undermines confidence in the association studies. The bait protein in lanes 5-8 should be equal. Also, there is significant binding of GST to UBP1 and TFCP2, in roughly the same patterns as they bind to GST-MED16 αβ. The absence of input samples makes the results even more difficult to interpret.

      We acknowledge the technical limitations the reviewer pointed out. Regarding the concern about unequal protein loading across lanes 5-8, we note that lanes 7 and 8 in fact contain more GST-M16αβ bait protein than lanes 5 and 6, yet TFCP2L1 and YY1 still show no appreciable binding above the GST-alone background. This loading asymmetry therefore strengthens the conclusion that these proteins do not directly interact with MED16. For UBP1 and TFCP2, we have now provided quantification of the Western blot signals, which confirms a clear difference in binding to GST-M16αβ versus GST alone. Furthermore, these GST pull-down experiments were performed under stringent conditions—300 mM NaCl and 0.5% Tween-20 in the wash buffer—and the UBP1 and TFCP2 interactions with GST-M16αβ persisted under these conditions (lane 5-8), whereas binding to GST alone was minimal (lane 1-4). These technical details support the specificity of the observed interactions.

      (5) The domain deletion mutants are utilized throughout the manuscript as evidence of the importance of the UBP1-MED16 interaction. However, in Figure 2F lanes 7 and 8, the delta-S mutant binds MED16 as well as full-length UBP1. This undermines much of the subsequent data and conclusions about specificity.

      We believe the reviewer may have a misunderstanding about the experimental design. The delta-S (ΔSAM) mutant deletes the SAM motif, which is required for UBP1-TFCP2 heterodimerization, but retains the UBP1-specific sequence (USP) that mediates MED16 binding. The observation that ΔSAM still binds MED16 at levels comparable to full-length UBP1 is therefore not a discrepancy—it is the expected result and confirms that USP is the region responsible for MED16 interaction. The DBD mutant, which further removes USP, completely loses MED16 binding. Together, these deletion constructs delineate two separable interaction surfaces on UBP1: USP for MED16 binding and the SAM motif for TFCP2 heterodimerization (see Figure 2 G). The functional analysis of these domains is reflected in Figure 3B: ΔSAM, which retains MED16 binding but loses TFCP2 dimerization, shows approximately half the transcriptional activity of full-length UBP1, suggesting that both interactions contribute to full UBP1 function. To avoid similar confusion, we have renamed ΔS to ΔSAM,UBP1-SP to USP in the revised manuscript.

      (6) Even if the delta-S mutant were defective for MED16 binding, the result in Figure 3B does not "confirm that MED16 is required for the transcriptional activity of UBP1,". Removal of that domain may have other effects.

      We wish to first clarify a factual point: the delta-S mutant (ΔSAM) is not defective for MED16 binding. ΔSAM deletes the SAM motif that is required for UBP1-TFCP2 heterodimerization, but retains the UBP1-specific sequence (USP) that mediates MED16 binding. As shown in Figure 2F, ΔSAM binds MED16 at levels comparable to full-length UBP1. The mutant that loses MED16 binding is DBD, which further deletes USP.

      The functional result in Figure 3B is therefore consistent with this biochemical mapping: ΔSAM retains MED16 binding but loses TFCP2 dimerization, and accordingly shows approximately half the transcriptional activity of full-length UBP1. This suggests that both the MED16 interaction (via USP) and the TFCP2 interaction (via the SAM motif) contribute to full UBP1 function.

      More importantly, the conclusion that MED16 is required for UBP1 transcriptional activity does not rest on domain mutant analysis alone. It is supported by independent loss-of-function approaches: shRNA-mediated MED16 knockdown (Fig 3C) and CRISPR-mediated MED16 knockout across five independent frameshift clones (Fig 3E-F), both of which consistently reduce UBP1 reporter activity. The domain deletion mutants complement these approaches by mapping the specific interaction interfaces.

      (7) As Mediator is critical for the activation of many genes, it is not accurate to assume that the impact of its deletion in Figure 3E/F demonstrates a direct requirement in UBP1-driven transcription. This could easily be an indirect effect.

      MED16 knockout data must be interpreted cautiously due to potential Mediator destabilization artifacts. However, our conclusion does not rely solely on loss-of-function data; transient competitive overexpression and domain-mapping assays bypass chronic MED16 depletion entirely. The MED16Δαβ mutant retains full Mediator integration but loses UBP1 binding. Unlike wild-type MED16, this mutant fails to change UBP1 or HIV-1 reporter activity in 36–48 h transient assays performed in wild-type cells with intact endogenous Mediator. Dose titration further confirms that only UBP1-interacting MED16 competes for UBP1 binding to repress target promoters (Fig 3G). Since these experiments involve no permanent MED16 ablation, the observed transcriptional effects cannot be attributed to indirect global Mediator dysfunction, verifying specific MED16–UBP1 regulation.

      (8) Without documenting the relative protein expression levels in Figure 3G/H, conclusions cannot be drawn about the titration experiments, nor the co-expression experiments. These findings are likely the result of squelching or some form of competition that is not directly related to the UBP1-mediated transcription. A great deal of validation would be required in order to support the model that these effects are a result of MED16 overexpression sequestering UBP1 away from holo-Mediator.

      We thank the reviewer for this insightful comment. In fact, the squelching interpretation that the reviewer proposes is fully consistent with our functional model and helps reinforce a key conclusion of our study.

      The reviewer correctly points out that overexpressed MED16 may compete with the endogenous Mediator complex for UBP1 binding, sequestering UBP1 away from the holo-Mediator and thereby inhibiting UBP1-driven transcription. This interpretation directly implies that UBP1 requires association with the intact Mediator complex—not merely free MED16—to activate transcription. This is precisely the model we advocate, and the squelching phenomenon observed in Figure 3G thus provides independent functional evidence for it.

      The specificity of this effect is confirmed by the MED16 Δαβ mutant: the Δαβ mutant integrates into the Mediator complex normally but cannot bind UBP1, and consequently fails to exert any competitive inhibition on the UBP1 reporter (Fig 3G). This demonstrates that the squelching effect is specifically dependent on the MED16-UBP1 interaction interface. We have now documented the relative protein expression levels for these experiments in the revised manuscript.

      (9) The lack of any documentation of expression levels for the various ectopic proteins in the majority of Figures, renders mechanistic claims meaningless (Figures 3, 4, 5, 6, 7, S2, S3). This is particularly relevant since the model presented for many of the results invokes concentration-dependent competition.

      In the revised manuscript, we have now included Western blot data documenting the expression levels of ectopic proteins for the key experiments. The expression level data confirm that the proteins were expressed at the expected levels across the different conditions.

      Recommendations for the authors:

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      Reviewer #1 (Recommendations for the authors):

      (1) The writing and presentation are generally good, except that some typos and mistakes in conceptual statements (e.g., lines 407-408 "WDR-deleted MED16, which cannot interact with UBP1") often confuse the readers.

      We thank the reviewer for the careful reading. We have tried out best to correct the typos and misstatements, including the error in line 407-408 where "WDR-deleted MED16, which cannot interact with UBP1" should refer to the αβ-domain deletion rather than the WDR deletion. The whole manuscript has been extensively rewritten for better clarity and preciseness.

      (2) Inconsistency in the citation format between numbering and author names should be avoided.

      The citation format has now been unified throughout the manuscript.

      (3) Two important scientific concepts based on the published literature should be mentioned:

      (a) "The position-dependent function of transcription factors (TFs) relative to the TSS" (lines 427-428) is a well-known fact in the transcription field that partly explains gene activation versus gene repression; and

      (b) the statement "JQ1 that is known to reverse HIV-1 latency by antagonizing BRD4's suppression of the Tat-P-TEFb/SEC (Super Elongation Complex) interaction" (lines 384-386) is only partially correct and is a property unique to the BRD4 long (BRD4-L) isoform.

      We thank the reviewer for this suggestion. We have now cited the relevant literature on the position-dependent function of transcription factors relative to the TSS, including the recent study by Duttke et al. (3), which systematically demonstrated that the effect of TF binding on transcription initiation is highly position-dependent. Our findings provide a clear example that UBP1 activates transcription when its binding motif is located upstream of the TSS but represses when the motif overlaps the TSS, which exemplifying this concept.

      We have corrected the statement to specify that JQ1 antagonizes the BRD4 long isoform (BRD4-L)-mediated suppression of Tat-P-TEFb/SEC, and have noted that the BRD4 short isoform (BRD4-S) may also contribute to HIV-1 promoter repression and JQ1-mediated latency reversal.

      (4) Another relevant concept is that BRD4 short (BRD4-S) isoform-inhibited HIV-1 promoter activity could be potentially alleviated by JQ1, leading to latency reversal. Besides the aforementioned points and those comments already provided in the Public Review, the involvement of TFCP2 and YY1 in MED16-UBP1 function has not been clearly established and will require more careful and detailed investigation.

      We thank the reviewer for these suggestions. Regarding BRD4-S, we have added a discussion of the BRD4 short isoform's role in HIV-1 promoter regulation and its potential contribution to JQ1-mediated latency reversal.

      Regarding the involvement of TFCP2 and YY1, we agree that their precise roles within the MED16-UBP1 regulatory axis have not been fully dissected in the current study. Our data indicate that TFCP2 can dimerize with UBP1 to enhance transcriptional activation (Fig 3H), and YY1 is present in the MED16-containing fractions (Fig 1E), consistent with its previously reported role in HIV-1 silencing. However, the molecular details of how TFCP2 and YY1 contribute to MED16-UBP1 function—and whether they act in the same or parallel pathways—remain to be determined. We have acknowledged this as a limitation and a direction for future investigation in the revised Discussion.

      Reviewer #2 (Recommendations for the authors):

      (1) The data from Figure 1F are hard to interpret, the blot quality is poor for Med23, 16

      We acknowledge that the blot quality for MED23 and MED16 in Figure 1F was suboptimal in the original submission. We have now provided better Western blot, which confirms the specific co-immunoprecipitation of MED16 and MED23 with TFCP2 in both HeLa nuclear extract and the gel filtration fractions. Importantly, the reciprocal co-IP (anti-MED16 IP blotted for TFCP2 and UBP1, Fig 1E) independently validates this interaction.

      (2) Figure 2: No MW markers on gels. Also, these types of experiments are ok for pilot studies, but they aren't rigorous. Only a few proteins were tested, and it's easy to get false positives with how the experiments were completed. Finally, the Mediator proteins were tested as single isolated proteins rather than in their native context. As isolated proteins, they likely have large exposed hydrophobic patches (normally bound to other subunits), and this can generate non-specific "sticky" interactions that can lead to false positive results.

      We have now included MW markers on the gel images in the revised Figure 2.

      The reviewer raises a valid general concern about domain mapping experiments. However, we wish to emphasize that the readout in Figure 2B and 2F is the binding of exogenously expressed truncated proteins to their endogenous interaction partners—MED1, TFCP2, MED16, and MED23—which are natively folded and assembled in their physiological environment. This is not a situation where two isolated proteins are mixed in a test tube. Furthermore, the deletion series themselves contain important internal controls against non-specific "stickiness": In Figure 2B, progressive deletion of the WDR domains leads to a gradual reduction in MED1 binding, consistent with the predicted structural role of the β-propeller (WDR domain). The truncation at the αβ-domain specifically abolishes TFCP2 binding but does not affect its association with Mediator complex as indicated by MED1. If the truncated proteins were non-specifically sticky due to exposed hydrophobic patches, one would expect uniform binding across all truncations or random binding patterns, which is not observed. And in Figure 2F, deletion of the 36-amino-acid USP abolishes its MED16 binding, while deletion of the SAM motif does not. This sequence-specific differential effect is inconsistent with non-specific hydrophobic interactions.

      The domain mapping experiments in Figure 2 were not designed as an unbiased screen but as hypothesis-driven tests guided by the IP-MS results identifying UBP1/TFCP2 as MED16 interactors, sequence and structural analysis predicting the roles of the WDR and αβ-domains. The conclusions from these experiments are corroborated by subsequent functional assays: the USP-deleted mutant and the MED16 Δαβ mutant show corresponding functional defects in both UBP1 reporter and HIV-1 reporter assays (Fig 3G, Fig 5G), providing strong support that the mapped interaction interfaces are functionally relevant.

      (3) Figure 3: UBP1 reporter is artificial, 6X UBP1 sites upstream of a TATA box.

      We appreciate this comment and wish to clarify a misunderstanding. The UBP1 reporter used in Figure 3 is not an artificial construct assembled from random elements. Its backbone is derived from the mouse α-globin gene promoter, a well-established natural target of UBP1/TFCP2, which contains two endogenous UBP1/TFCP2 binding sites. In order to increase the reporter's sensitivity to UBP1/TFCP2, we expanded the original two sites to six. Critically, this expansion did not alter the native architecture of the promoter—the relative positions of the transcription factor binding sites, the CCAAT box, the TATA box, and the TSS remain unchanged from the original α-globin promoter. This reporter therefore retains the physiological spacing and topological organization of a genuine UBP1 target promoter, and its low basal activity and high inducibility by UBP1 make it a well-suited tool for modeling UBP1 transcriptional activity. We have further clarified this description in the revised manuscript.

      (4) Figure 3D: Med16 KD not compelling, perhaps 50% knockdown? Hard to tell because no replicates and no quantitation.

      We acknowledge that the shRNA-mediated MED16 knockdown in Figure 3D was partial and that the original presentation lacked replicate quantification. We initially tested three independent shRNAs targeting MED16, of which only one achieved appreciable knockdown. Recognizing this limitation, we turned to a more definitive loss-of-function approach: CRISPR-Cas9-mediated MED16 knockout. Five independent frameshift KO clones were generated in mouse HT cells, each verified by sequencing and Western blotting (Fig 3F), and all five clones consistently showed reduced UBP1 reporter activity compared with wild-type cells (Fig 3E). The consistency between the shRNA knockdown and CRISPR KO reinforce the conclusion that MED16 is required for UBP1 transcriptional activity.

      (5) Figure 3E: Med16 KO will be a different cell line because of genetic adaptation. That is, an RNA-seq experiment is expected to result in many gene expression changes compared to the parental line. This could contribute to differences, or differences could result from altered Mediator composition to compensate for Med16 loss, but this wasn't addressed by the authors. A rapid degron method would be much more rigorous.

      We thank the reviewer for raising this important concern. We agree that prolonged MED16 loss can elicit cellular adaptation and compensatory changes in Mediator composition, as our own new data on tail module dissociation confirm. This makes it challenging to disentangle direct and indirect effects using constitutive KO models alone.

      However, two independent lines of evidence support a direct role for MED16 in UBP1-mediated transcription that cannot be explained by adaptive responses:

      First, acute shRNA-mediated knockdown produces the same phenotypic trend. shRNA operates on a shorter timescale (days) without prolonged selection for compensatory mutations, yet it also reduces UBP1 reporter activity (Fig 3C). The convergence of acute and chronic loss-of-function approaches suggests the phenotype is driven by MED16 loss itself rather than by the secondary adaptations that accumulate over time in KO cells.

      Second, and most critically, the MED16Δαβ mutant experiment completely bypasses the issues of genetic adaptation and Mediator structural disruption (Fig 3G). This experiment is performed in wild-type cells with an intact endogenous Mediator complex, without any MED16 depletion and without any long-term selection. The MED16Δαβ mutant retains full ability to integrate into the Mediator complex (its WDR domain is intact) but cannot bind UBP1. Overexpression of wild-type MED16 competitively inhibits the UBP1 reporter due to the squelching effect, whereas overexpression of MED16Δαβ at comparable levels does not (Fig 3G). The sole molecular difference is that MED16Δαβ doesn`t contain the UBP1-binding interface. Because this experiment involves no MED16 loss and no adaptive period, the result directly demonstrates that MED16-UBP1 interaction is required for UBP1 transcriptional activity, entirely independent of concerns about clonal adaptation.

      We appreciate the reviewer's suggestion of a rapid auxin-inducible degron approach. While acute depletion strategies offer clear advantages in minimizing cellular adaptation, they are not without limitations. First, degron-based depletion rarely achieves 100% elimination of the target protein, and residual protein may confound interpretation. Second, and particularly relevant to our system, degron-mediated degradation may preferentially target free, unassembled subunits while sparing proteins already stably integrated into large macromolecular complexes such as the Mediator—potentially creating a lag or even complete resistance to degradation for the pool of MED16 that is assembled into the complex. Given these considerations, we believe our convergent strategy—combining shRNA knockdown, CRISPR-mediated knockout in multiple independent clones, and the Δαβ mutant that bypasses structural perturbation—provides a robust and complementary set of evidence that does not rely on any single depletion method.

      (6) The title for Figure 3 is "Med16 is required for UBP1 activation of gene transcription", but that's not conclusively shown by these experiments.

      We agree that the original title of Figure 3 may overstate. We have revised the title to " MED16 acts through the Mediator complex to support UBP1-mediated transcriptional activation ", which may better reflect the data. As discussed in our responses above, this conclusion is supported by converging evidence from shRNA knockdown (Fig 3C), CRISPR-mediated KO across multiple clones (Fig 3E-F), and the specific loss of function observed with the MED16Δαβ mutant (Fig 3G).

      (7) Figure 5: Med16 protein levels were never measured, nor were other transfected proteins. Reporter assay data are correlative only; no evidence for direct effects, and only 2 other MED subunits are probed. Again, this is a starting point, but nothing to use for concrete conclusions about Med16.

      We have now provided Western blot data documenting MED16 and other transfected protein levels for the experiments in Figure 5, confirming that the proteins were expressed at the expected levels. We agree that plasmid-based reporter assays alone cannot establish direct transcriptional mechanisms. The HIV-1 reporter experiments in Figure 5 serve as an initial functional readout, and their conclusions are corroborated by more direct approaches: (i) the position-dependent specificity demonstrated by chimeric reporter assays (Fig 6A-C); (ii) the independence of the effect from TAR-mediated elongation and HDAC activity (Fig S2), ruling out alternative mechanisms; and (iii) the immobilized template transcription assays, which directly measure nascent RNA production and PIC assembly on the HIV-1 promoter (Fig 7). The reporter data should be viewed as one component of a larger body of convergent evidence rather than as standalone proof.

      MED23 and MED24 were chosen as the most relevant controls because they, along with MED16, form the core of the tail module submodule that creates the transcription factor interaction platform. They are structurally adjacent to MED16 within the same submodule. The fact that neither MED23 nor MED24 overexpression affects HIV-1 reporter activity (Fig 5C), whereas MED16 overexpression does so in a UBP1-binding-dependent manner (Fig 5C, 5E), demonstrates that the inhibitory effect is specific to MED16 and not a generic consequence of overexpressing a Mediator tail subunit.

      (8) Figure 6: similar concerns to Figure 5. The promoters are artificial, derived from a chicken beta-actin promoter with artificially inserted UBP1 binding sequences.

      We acknowledge that the chimeric promoters in Figure 6 are indeed deliberately designed. To address this specific question: Does the binding position of the UBP1 relative to the TSS dictate whether UBP1-MED16 activates or represses transcription?

      To isolate position as the sole variable, we needed a backbone promoter that (i) is stably and robustly active in the cell lines used, (ii) does not itself contain endogenous UBP1 binding sites that would confound the interpretation, and (iii) allows precise placement of the UBP1 binding motif either upstream of or overlapping the TSS. The chicken β-actin promoter meets all three criteria and is a widely used tool in molecular biology for such controlled promoter engineering experiments. Notably, its high GC content around the promoter region is also a feature shared with the HIV-1 core promoter, making it a particularly relevant backbone for the HIV-1 TSS chimeric constructs.

      The key controls for this experiment are internal: in the same backbone, placing the UBP1 binding site at the TSS results in MED16-UBP1-dependent repression, whereas placing it upstream does not (Fig 6A vs 6B). Furthermore, this position-dependent effect requires the MED16-UBP1 interaction interface, as the MED16 Δαβ mutant and the UBP1 DBD mutant both fail to produce the inhibitory effect (Fig 6A). The differential outcome between the two constructs—which differ only in the placement of the UBP1 binding site—cannot be attributed to the artificial nature of the backbone, because the backbone is identical in both cases.

      (9) Figure 6D: Not rigorous, no statistical analysis, cannot determine whether the modest changes are biologically relevant/meaningful. Also, data were obtained through indirect measurements and long timeframes, so any direct effects from possible UBP1 binding are probably lost.

      The differentially expressed genes in Figure 6D were selected using DESeq2 with a significance threshold of p < 0.05. The top 50 upregulated and top 50 downregulated transcripts were then used for UBP1 motif enrichment analysis around their promoters. We have clarified these selection criteria in the revised figure legend.

      Regarding the concern that indirect measurements over long timeframes, we now have additional evidence that UBP1 binding effects are preserved in our RNA-seq data. Motif analysis of UBP1-upregulated genes using HOMER identified the CP2 family binding motif (CNRG-N6-CNRG) as the most significantly enriched motif. This indicates that UBP1-binding-dependent transcriptional effects are not lost in our dataset.

      Author response image 4.

      Motif enrichment result of the UBP1 up-regulated genes

      Furthermore, when these UBP1-upregulated and UBP1-downregulated genes are analyzed separately for motif position relative to the TSS, a clear pattern emerges: UBP1-upregulated genes show motif enrichment flanking the TSS, whereas UBP1-downregulated genes show enrichment overlapping the TSS (Fig 6D). If the transcriptional changes were non-specific secondary consequences of prolonged UBP1 overexpression, one would not expect this position-specific distribution. Finally, this positional specificity is corroborated by the chimeric reporter experiments (Fig 6A-C), where moving the UBP1 binding site across the TSS in an otherwise identical promoter directly switches the regulatory outcome. The concordance among the de novo motif discovery, the genome-wide positional analysis, and the functional reporter assays supports the biological relevance of the motif enrichment pattern.

      (10) The title for Figure 6 is "UBP1 binding site determines the UBP1-Med16 inhibition in HIV-1 transcription" but the data do not convincingly show this.

      We appreciate this suggestion. We have revised the title to "The position of the UBP1 binding site relative to the TSS dictates whether MED16-UBP1 activates or represses transcription.". For clarification, Figure 6 not only demonstrates that the UBP1 binding position dictates MED16-UBP1-mediated inhibition in the HIV-1 context, but also revealed that this positional effect could be generalized to endogenous genes: UBP1 motifs flanking the TSS are associated with activation, while motifs overlapping with the TSS are associated with repression.

      (11) Figure 7: The data and the experiment do not support the claim in the title that "MED16-UBP1 complex prohibited PIC formation of HIV-1 transcription". I cannot convince myself that there are meaningful differences between the results shown in 7B, but it's hard to judge because there are no replicates and no quantitation.

      We have revised the title from "MED16-UBP1 complex prohibited PIC formation of HIV-1 transcription" to "MED16 interferes with HIV-1 PIC assembly at the TSS via its interaction with UBP1." We have also provided quantification of the Western blot signals from replicate experiments in Figure 7B, which confirms statistically significant differences in CDK8 binding, Pol II pSer5 signals, and TFIIB retention between conditions. We note that the key observations in Figure 7B were consistently observed across multiple pilot experiments prior to the final dataset presented in the manuscript. Thus, the reported differences are reproducible and not based on a single experiment.

      (12) The immobilized template experiments had only -78 upstream and +60 downstream of the TSS. By my understanding, much more upstream DNA is needed to allow a PIC to assemble, because the 5'-end bead attachment will block. I think this was outlined in an article by the Carey lab, but I'm not sure. A point here is that it would be reassuring for the authors to show that PIC assembly was occurring and that transcription was responsive to a transcription factor, similar to what the Carey lab has done with immobilized templates. See, for example, Figure 1 in Lin & Carey Curr Protocol Mol Biol 2012 Ch12 unit 12.14.

      We thank the reviewer for raising this technical consideration. We respectfully offer a different perspective based on current structural data on the human PIC.

      A recent cryo-EM study of the human Mediator-bound preinitiation complex (4) demonstrated that the PIC spans approximately 50 bp upstream and downstream of the TSS. The DNA templates used for structural determination in that study were generally within 105 bp upstream and 63 bp downstream of the TSS. Our HIV-1 template (-78 to +60, i.e., 78 bp upstream and 60 bp downstream of the TSS) falls within this well-characterized range and provides sufficient space for PIC assembly.

      Regarding the choice of the -78 boundary: the HIV-1 core promoter is defined as -78 to +60, and the region from -78 to -105 encompasses the HIV-1 enhancer, which contains additional regulatory elements including NF-κB and NFAT binding sites. We deliberately excluded these enhancer elements to avoid confounding regulatory inputs and to focus specifically on the UBP1 binding site at the TSS, which is the central focus of our model. The robust luciferase mRNA production observed in wild-type nuclear extract (Fig 7C) provides direct functional evidence that PIC assembly and transcription initiation proceed efficiently on this template under our conditions.

      Author response image 5.

      Promoter templates used for human PIC assembly (Chen et al., Science 372, eaba8490, 2021): templates within −105 to +65 bp of the TSS support PIC formation

      (13) Related to the above concern, the qPCR analysis from the extract experiments may be misleading because of contaminating nucleic acids in the extract. More control experiments are needed, such as no NTP controls.

      We thought this concern has been addressed by our experimental design.

      First, the PIC step in our experimental design (Fig 7B, "PIC") is the no-NTP control: nuclear extract is incubated with the immobilized template without NTPs. After washing, the proteins bound at this step are analyzed by Western blot, and importantly, there is no transcription occurred at this step. Transcription is then initiated by adding NTPs (Fig 7B, "Trx."), and the supernatant from this step is collected for qPCR analysis of transcription.

      Second, it is unlikely that the contaminating nucleic acids from the nuclear extract could confound our qPCR results, because the qPCR analysis specifically detects Luciferase mRNA transcribed from the immobilized HIV-1-Luciferase template, which is absent from eukaryotic genomes; and the endogenous genomic DNA or RNA cannot generate a false-positive signal.

      Lastly, after transcription, the immobilized templates are retained on the streptavidin beads and removed, while only the supernatant containing newly synthesized RNA is collected for qPCR. Any residual template DNA or extract-derived nucleic acids bound to the beads are therefore excluded from the qPCR sample.

      (14) Some references are made with the format of (author name, year), but others use numbers.

      The citation format has been unified throughout the manuscript.

      (15) On line 111-115, it is stated that 2,5 HD somehow "does not interfere with weak hydrophobic interaction due to different positions of hydroxyls" with no reference. Both 1,6 HD and 2,5 HD are hydrophobic molecules, and they will disrupt protein structure. The authors make a point about the differential results with 1,6 HD vs. 2,5 HD, but it's not compelling and not justified.

      We have now provided the reference to support this statement. The specificity of the 1,6-HD effect is further clarified as follows.

      1,6-HD and 2,5-HD are structural isomers sharing the same chemical formula and molecular weight. The key difference lies in the positions of their hydroxyl groups (See Author response image 6). The position of the two hydroxyl groups changes both the molecule’s shape and how it interacts with water and hydrophobic surfaces.

      In 1,6-HD, the two -OH groups sit at the ends of the chain, giving a more symmetric, flexible molecule, while in 2,5-hexanediol the -OH groups are closer to the middle, which changes polarity distribution and local geometry (5, 6). The distinctive structures matter because hydroxyl groups strongly hydrogen-bond with water. When they are terminal and well separated in 1,6-HD, the molecule can present a more balanced hydrophilic “cap” at both ends while keeping a relatively long hydrophobic center, which helps 1,6-HD partition into and disturb weakly interacting hydrophobic regions in condensates or hydrophobic interfaces (Author response image 6). By contrast, moving the hydroxyls inward in 2,5-HD does not help with disrupting the hydrophobic interfaces (Author response image 6). That is why 2,5-HD is often used as a comparison compound: it has the similar chemical formula, but the different hydroxyl pattern usually makes it a weaker or at least differently acting perturbant.

      Author response image 6.

      Differential disruption of hydrophobic interfaces by 1,6-HD vs 2,5-HD

      (16) On lines 117-120, the authors claim that Med16 is "integrated into the Mediator complex through weak hydrophobic interaction but not ionic interaction" based upon a few IP results. They then state (lines 130-131) that "the interaction between Mediator and Med16 is an unstable hydrophobic interaction." These statements make no sense based on any data shown, and they ignore the fact that Med16 purifies with Mediator from many different purification protocols. It's safe to say that its interaction with Mediator results from strong, extensive hydrophobic interfaces, which is further supported by actual structural data. The authors should check their reasoning here because they are over-interpreting their results, and this will be misleading to readers.

      We thank the reviewer for this important suggestion. The reviewer is right that our original phrasing—particularly "unstable hydrophobic interaction"—was imprecise and inconsistent with the established structural data. As the reviewer notes, MED16 co-purifies with the Mediator complex through multiple purification protocols, and recent cryo-EM structures (4) reveal that MED16 engages in extensive hydrophobic interfaces with neighboring tail module subunits, particularly MED24 and MED25. We fully agree that this is a strong, hydrophobic interaction in the physiological context.

      Our 1,6-hexanediol experiments demonstrated that the MED16-Mediator interface does have a hydrophobic character, which renders the sensitivity to 1,6-HD disruption. This does not mean the interaction is weak. We have now carefully described the relevant statements in the revised manuscript.

      Reviewer #3 (Recommendations for the authors):

      (1) It is not accurate to claim that "198 (genes) were repressed by shMED16 knockdown (Fig 4B and 4C)". These genes were simply not activated by UBP1 in the knockdown cells.

      We thank the reviewer for this careful distinction. We have revised the text to state that the UBP1-activated genes were “profoundly downregulated upon MED16 depletion” rather than “repressed by shMED16 knockdown”. The biological point remains unchanged: MED16 is required for UBP1 to activate this set of target genes.

      (2) Like the majority of experiments presented, the RNA-seq presented in Figure 4 may reflect indirect effects of MED16 loss. As such, the results do not support the claim that "This result demonstrated that UBP1 and MED16 collaborate to regulate transcription".

      We acknowledge that RNA-seq data from MED16 knockdown cells alone cannot distinguish direct from indirect effects. However, we did not rely on the RNA-seq data alone to support a collaborative role for UBP1 and MED16.

      The key evidence comes from experiments comparing wild-type MED16 with the MED16Δαβ mutant. MED16Δαβ integrates into the Mediator complex normally but cannot bind UBP1 (Fig 2B). When overexpressed in wild-type cells, wild-type MED16 inhibits the UBP1-driven reporter activity through a squelching effect. In contrast, MED16Δαβ has no effect on the UBP1 reporter assay (Fig 3G), and the same is true for the HIV-1 reporter assays (Fig 5G). Thus, MED16 must both integrate into the Mediator complex and directly bind UBP1 to support UBP1-mediated transcription.

      In addition, the genes identified as UBP1-MED16 co-regulated by RNA-seq are enriched for specific biological processes—angiogenesis (Fig 4D-E)—that align with the known physiological functions of UBP1. Such functional coherence would be unexpected if the transcriptional changes were merely non-specific secondary consequences of Mediator disruption.

      Thus, while we agree that RNA-seq alone has limitations, the convergent evidence from the MED16Δαβ mutant and the functional specificity of the co-regulated gene set supports a collaborative role for UBP1 and MED16 in transcriptional regulation.

      (3) The data in Figure 4 are not presented with controls documenting the relative expression levels of MED16 and UBP1. For example, it would be important to understand the level of UBP1 overexpression achieved, relative to endogenous UBP1 levels in HeLa cells.

      We agree with the reviewer that documenting expression levels is important. Author response image 7 are the CPM values for UBP1 from our RNA-seq data, confirming robust overexpression in the UBP1-overexpression condition compared with the control. The MED16 protein levels in the knockdown cells can be found in Fig 3D, as the same MED16-knockdown HeLa cell line was used for the RNA-seq experiment.

      Author response image 7.

      UBP1 expression level derived from RNA-seq

      Regarding the physiological relevance of UBP1 overexpression, several observations support that the transcriptional effects we observe are specific rather than artifacts of overexpression: (i) the UBP1-activated genes are enriched for pathways known to be regulated by UBP1—angiogenesis (Fig 4D-E)—rather than showing random, non-specific activation; (ii) the activation of these genes is attenuated upon MED16 knockdown, demonstrating dependence on the MED16-UBP1 interaction; and (iii) in reporter assays, the MED16 mutant lacking its C-terminal αβ-domain fails to competitively inhibit UBP1 driven reporter transcription even when UBP1 is similarly overexpressed (Fig 3G), indicating that the competitive inhibition of the UBP1 reporter depends specifically on the MED16-UBP1 interaction interface, rather than on the amount of UBP1 protein overexpressed.

      (4) The enhancer-promoter architecture of the luciferase construct used in Figure 3 is not sufficiently described. Are the elements far enough apart that Mediator-dependent looping is required for transcription, for example?

      We appreciate the reviewer's question. The UBP1 reporter construct used in Figure 3 is derived from the mouse α-globin gene promoter, a well-established natural target of UBP1/TFCP2(7, 8). The native α-globin promoter contains two endogenous UBP1/TFCP2 binding sites; to increase the reporter's sensitivity to UBP1, we expanded these to six tandem copies. Critically, this expansion preserved the native architecture of the promoter—the relative positions of the UBP1 binding sites, the CCAAT box, the TATA box, and the TSS were not altered. The entire reporter construct spans only 198 bp in total length. At this scale, all regulatory elements reside within a compact proximal promoter region, with no element separated by a distance that would require DNA looping for functional communication. The reporter therefore measures UBP1-dependent transcriptional activation from the proximal promoter, consistent with the canonical role of Mediator in facilitating PIC assembly rather than mediating long-range enhancer-promoter interactions. We have added a detailed description of the construct architecture to the Methods section.

      (5) The identification of matches to the UBP1 consensus sequence in a promoter does not prove that this is how UBP1 overexpression is impacting their transcription. "highly matched UBP1 motifs were identified in their promoters (Fig. 4F), leading to their activation when UBP1 was overexpressed."

      We agree with the reviewer that the presence of a UBP1 consensus motif in a promoter does not by itself prove direct regulation. We have revised the original statement: the activation of these genes by UBP1 overexpression is now described as "associated with" the presence of UBP1 motifs in their promoters.

      We acknowledge that the ideal experiment to demonstrate direct UBP1 occupancy would be ChIP-seq. However, ChIP-grade antibodies against UBP1 are not commercially available, and no UBP1 ChIP-seq datasets exist in public databases. We attempted to carry out the ChIP-seq ourselves but were unable to obtain sufficiently good-quality data.

      In the absence of ChIP data, three lines of evidence indicate that the identified UBP1 motifs are functionally relevant. First, motif analysis of UBP1-upregulated genes using HOMER identified the CP2 family binding motif (CNRG-N6-CNRG) as the most significantly enriched motif. This demonstrates that UBP1-binding-dependent transcriptional could be preserved in our RNA-seq data. Second, when we examine the positional distribution of these motifs, a clear pattern emerges: UBP1 motifs flank the TSS in activated genes, but overlap the TSS in repressed genes (Fig 6D). Indirect effects would not produce this position-specific pattern. Third, our chimeric reporter experiments (Fig 6A-C) directly test this position effect: moving the UBP1 binding site upstream of the TSS leads to activation, while moving it to overlap the TSS leads to repression. Together, these three independent approaches support the conclusion that UBP1 regulates these genes through the motifs we identified. See Author response image 4.

      (6) Lines 266 and 277 are redundant.

      We have carefully reviewed lines 266 and 277. Line 266 is the topic sentence (caption) of the section ("MED16 collaborates with UBP1 to inhibit HIV-1 transcription"), which introduces the overall conclusion, while line 277 describes the specific experimental result ("MED16 inhibited HIV-luciferase activity in a dose-dependent manner"). These serve distinct rhetorical functions. We have ensured that no other redundant phrasing exists elsewhere in the section.

      (7) The mere correlation of binding site position with activation status does not prove "that UBP1 may act as either a transcriptional activator or repressor, depending on distance of its binding site to TSS."

      We appreciate the reviewer's concern regarding the distinction between correlation and causation. The genome-wide analysis (Fig 6D) reveals an association between UBP1 motif position and transcriptional outcome, which prompts us to postulate that the UBP1 binding position could dictate the transcriptional activity level. The causal evidence comes from the chimeric reporter experiments (Fig 6A-C), in which we directly manipulated the position of the UBP1 binding site relative to the TSS in an otherwise identical promoter background. Placing the UBP1 binding site at the TSS resulted in MED16-UBP1-dependent repression, whereas placing it upstream of the TSS did not. This controlled experiment demonstrates that changing only the position of the UBP1 binding site is sufficient to switch the regulatory outcome, thereby establishing a causal relationship between binding site position and transcriptional effect. We have revised the text to clearly distinguish the correlational genome-wide analysis from the causal reporter experiments.

      (8) In Figure 7, MED16 overexpression results in less CDK8 binding. This undermines the claim that MED16 overexpression lowers transcription by binding to UBP1, and suggests an indirect effect.

      We appreciate the reviewer's careful observation. The reduction in CDK8 binding upon MED16 overexpression is consistent with our model: MED16, through UBP1 occupying the TSS, interferes with PIC assembly, of which CDK8 is a component. Importantly, the input levels of CDK8 and other Mediator subunits remained unchanged across the three conditions (Fig 7B), indicating that the reduced CDK8 signal in the PIC is not due to altered protein expression.

      In support of the specificity of the transcriptional effect, MED16Δαβ—which integrates into the Mediator complex but cannot bind UBP1 (Fig 2B)—fails to competitively inhibit either the UBP1 reporter (Fig 3G) or the HIV-1 reporter (Fig 5G), confirming that the transcriptional outcome depends on the MED16-UBP1 interaction.

      (9) Figure 8F is not referenced in the text or legend.

      Figure 8F has now been referenced in the Results and Discussion section.

      Reference:

      (1) Wang G, Cantin GT, Stevens JL, Berk AJ. Characterization of mediator complexes from HeLa cell nuclear extract. Mol Cell Biol. 2001;21(14):4604-13.

      (2) Yamazaki T, Souquere S, Chujo T, Kobelke S, Chong YS, Fox AH, et al. Functional Domains of NEAT1 Architectural lncRNA Induce Paraspeckle Assembly through Phase Separation. Molecular Cell. 2018;70(6):1038-+.

      (3) Duttke SH, Guzman C, Chang M, Delos Santos NP, McDonald BR, Xie J, et al. Position-dependent function of human sequence-specific transcription factors. Nature. 2024;631(8022):891-8.

      (4) Chen X, Yin X, Li J, Wu Z, Qi Y, Wang X, et al. Structures of the human Mediator and Mediator-bound preinitiation complex. Science. 2021;372(6546).

      (5) Zheng T, Wake N, Weng SL, Perdikari TM, Murthy AC, Mittal J, et al. Molecular insights into the effect of 1,6-hexanediol on FUS phase separation. EMBO J. 2025;44(10):2725-40.

      (6) Romero CM, Páez MS, Miranda JA, Hernández DJ, Oviedo LE. Effect of temperature on the surface tension of diluted aqueous solutions of 1,2-hexanediol, 1,5-hexanediol, 1,6-hexanediol and 2,5-hexanediol. Fluid Phase Equilibr. 2007;258(1):67-72.

      (7) Lim LC, Swendeman SL, Sheffery M. Molecular cloning of the alpha-globin transcription factor CP2. Mol Cell Biol. 1992;12(2):828-35.

      (8) Chae JH, Kim CG. CP2 binding to the promoter is essential for the enhanced transcription of globin genes in erythroid cells. Mol Cells. 2003;15(1):40-7.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Reviewer #1 (Public review):

      Summary:

      The authors have achieved an excellent, thorough anatomical characterization of all spinal projecting neurons in the larval zebrafish. The comprehensive nature of their labeling approach and their quantification will make this work an instant reference benchmark for a wide number of zebrafish researchers. In addition, the scholarly approach in comparisons with other work in and outside of fish makes the manuscript valuable to researchers outside the field who would like to know how to translate between zebrafish and mouse terminologies.

      Strengths:

      The figures are clear and easy to follow. The literature review is impressive. The authors are careful to note the few limitations of their approach (eg the absence of Mauthner cell labeling and associated large neuron weak label). The manuscript does the whole field a major service.

      Weaknesses:

      No weaknesses were identified by this reviewer.

      We deeply thank reviewer #1 for recognizing the importance of our work.

      Reviewer #2 (Public review):

      Summary:

      The vertebrate spinal cord receives inputs from many supraspinal regions. The authors used optical backfilling to trace neurons in the zebrafish larval brain sending axons to the spinal cord. With two-photon microscopy, they managed to render a comprehensive 3D map of these neurons and drew homologs with mammalian brain structures.

      Strengths:

      The main strength lies in the precise 3D mapping. The fact that most of the previously reported neuron groups have been confirmed by their approach is a solid endorsement of their methodology. This study provides a comprehensive alternative anatomical reference framework for studying individual groups of supraspinal neurons with projections to the zebrafish spinal cord.

      Weaknesses:

      The whole approach could be enhanced by counter-staining their preparation to profile brain structures, including many nuclei more precisely.

      Also, the backfilling approach does not reveal the full trajectories of axons, which is already available to some degree by ZExplorer Atlas.

      We thank Reviewer #2 for the attention given to important details. As you will read below, our approach needed to be implemented on live larval zebrafish for the PA GFP to fluoresce only when photactivated. Although counterstains on fixed samples could have been done, it would have been difficult to trace it back in a fixed (and deformed) sample where all neurons appear GFP-positive. We wrote this publication so it can serve the field best before the release of full brain connectome in 2027. Further molecular and histological characterization will be the topic of a subsequent study. Below we will individually address the issues stated by the reviewer.

      Reviewer #2 (Recommendations for the authors):

      (1) The power of 800 nm laser: 1 mW in Figure 1a, 10 mW stated in the method text.

      Thanks for catching this, this is now corrected to 1 mW in the revised manuscript.

      (2) Figure 2c: laterality density (e.g., 90:40 by neuron numbers) is already quite clear. The laterality index is less informative if not causing confusion. Take POA as an example; shouldn't the value be close to 1, rather than -0.8 based on your formula?

      The laterality density plot shows the anatomical spatial distribution of spinal descending neurons relative to the midline, whereas the laterality index is a scalar summary of the relative neuron counts on each side, independent of spatial position. For POA, we observed after pooling across animals 26 ipsilateral versus 1 contralateral neurons, which gives an LI close to -0.8 (after bootstrapping), indicating strong ipsilateral dominance. The density plot additionally shows that these neurons cluster close to the midline. We view the two measures as complementary: one quantifies laterality, the other reflects its spatial organization.

      (3) Line 286, check grammar.

      Corrected to "Using the ZExplorer atlas (Du et al., 2025), which contains thousands of single-neuron tracings in the larval zebrafish brain, we searched for telencephalic neurons projecting to the spinal cord."

      (4) Add discussion on comparison between your approach, conventional backfill tracing method, singlecell tracing by dye or GFP, and, more importantly, ZExplorer Atlas.

      We believe this comparison is sufficiently addressed in the Introduction and Discussion.

      (5) Line 346, add "in bi" after "scale bar".

      Corrected, thank you for spotting this.

      (6) Figure 4, change label ICN to INC in c and d.

      We apologize for this confusion, all of them are now corrected in the revised manuscript.

      (7) Line 389, change to "ventral (top) to dorsal (bottom)". Try to use the same order for all figures, i.e., dorsal images on top and ventral ones at the bottom.

      Corrected for the specific line and now all figures follow the same convention.

      (8) Figure 7b, add stack location diagrams.

      Added. Thank you very much for suggesting an improvement to the figure readability.

      (9) Figure 7c and other figure panels, suggest changing the word "medial" to "middle" since medial/lateral is usually used to describe sagittal locations.

      Good point: now corrected as suggested.

      (10) Why was DAPI counter-staining not carried out? This would help the authors to better draw outlines for different nuclei. It also provides important data on the proportion of SPNs within each nucleus.

      We agree with the reviewer that determining the proportion of SPNs within each nucleus is an important question; however, properly addressing this requires an independent, cytoarchitecture-based definition of nucleus boundaries, a substantial project that we consider outside the scope of the present study.

      DAPI labels cell nuclei generally but carries limited information relevant to classical neuroanatomical delineation of nuclei. Methods such as Nissl staining are better suited to this purpose, as they reveal the cytoarchitectonic characteristics of neurons. As mentioned in the Introduction and Discussion, we instead based our nuclei definitions on the strong evolutionary conservation of spinal-projecting neuron distributions, which we used as a proxy for delineating the different nuclei.

      (11) The photoactivation is restricted to the rostral spinal cord. Therefore, how far the axons project throughout the spinal cord cannot be assessed with the current photo-activation method.

      We agree with the reviewer: because photoactivation was restricted to the rostral spinal cord, our current data cannot resolve how far individual axons project caudally. However, all evolutionary comparisons in this study were performed across vertebrates using similarly rostrally-labeled SPNs, ensuring consistency in our cross-species analysis. We therefore do not believe that this limitation undermines our initial characterization of the SPN populations.

      We agree, however, that extending photoactivation to multiple spinal levels will be valuable for future work characterizing and refining the nuclei proposed in this work. Some of this effort is carried for vsx2+ neurons only by Jia et al., under revision in Nature Communications.

      (12) Line 544, if it is the spinal trigeminal tract, why does there appear to be some feint soma staining?

      We apologize for the confusion. We always meant to say trigeminal nucleus and not its tract. Text and figure legend are now corrected.

      Reviewer #3 (Public review):

      In this study, the authors aim to provide the most comprehensive and detailed topographic map to date of spinal projection neurons in the larval zebrafish brain. They achieve this by retrogradely photoactivating, in the rostral spinal cord, a photoconvertible GFP expressed pan-neuronally, and by constructing a template larval zebrafish brain atlas to regionalize the location of all labeled somata across the brain. The labeling strategy, together with the chosen animal model, provides strong support for the completeness of the dataset. The generation of a standardized anatomical atlas establishes a rigorous framework for analysis. Molecular and anatomical evidence suggesting evolutionary conservation of selected regions of interest appears solid.

      Overall, the authors successfully achieve their aim. By generating this atlas of spinal projection neurons, they provide not only an anatomical framework of the regions involved, but also an important reference for improving the orientation and regionalization of the zebrafish brain, which has historically been difficult to define. This work may serve as a valuable resource for future evolutionary, developmental, and comparative studies of spinally projecting neuronal populations implicated in diverse functions.

      We deeply thank Reviewer #3 for recognizing the impact of our work and benefit for the community at large, which has always been our intention.

    1. Author response:

      Reviewer #1 (Public review):

      Summary:

      The study by Fernandes et al used multiple types of experiments to study the increased metastatic activity conferred by p95-HER2 and presented evidence that biased downstream signaling was engaged by p95-HER2. Further studies demonstrated crucial phosphorylation sites and downstream transcription targets. Overall, this study will contribute to increased understanding of HER2 biology and breast cancer metastasis.

      Strengths:

      Multiple types of experiments to assess the increased invasion property by p95-HER2. Solid evidence was provided that p95-HER2 elicits a different transcription program, enhancing EMT. Convincing results were achieved in knockdown studies on crucial genes such as MRTFA and TGFB1I1.

      We thank the reviewer for this positive feedback on our manuscript.

      Weaknesses:

      To enhance the quality of this study, several points need to be addressed.

      (1) First, as the background to this study, the authors stated in the introduction that different isoforms of HER2 lead to different invasive properties. Is this conclusion based on clinical observation or animal models? This needs to be specified to help readers grasp the importance of the paper.

      We thank the reviewer for bringing this to our attention; we will add additional language to emphasize and explain prior findings referenced in the introduction establishing HER2 isoforms’ different invasive properties. The increased invasiveness of both d16 and p95 isoforms of HER2 has been established both in animal models and in clinical studies (1-6). We summarize these studies below:

      (1) Expression of the delta16 splice variant isoform has been shown in human cell lines to be more oncogenic than the WT HER2 isoform (7), and associated with different transcriptional profile including increased expression of cancer metastasis and cancer stem cell-related genes (4). Clinically, patients with d16HER2-positive breast cancer have higher rates of lymph node metastases than those with d16HER2-negative breast cancer (8). Castagnoli et al (9) provides an overview of preclinical and clinical data on d16 in HER2+ cancers.

      (2) The p95 isoform of HER2 is associated with increased metastasis (2) and worse outcomes (1, 10) in HER2+ breast cancer patients. Preclinical models show that p95-HER2 (also known as 611-CTF) activates a transcriptional program that promotes invasion and metastasis (3), part of the basis for our interest in HER2 isoform biology.

      Moreover, our group has previously detailed different tumor growth and dissemination characteristics of WT, d16, and p95 HER2 isoforms in our HER2 Crainbow mouse model which expresses all 3 of these isoforms in the mammary epithelium (5).

      Both d16 and p95 tumors in Her2Crainbow mice have the ability to progress to overt metastasis, unlike WT HER2 in this model (6). During early stages of malignant transformation prior to palpable tumor formation, p95 cells disseminated to the lung were 5x more numerous than d16 cells in the lung (despite more proliferation of d16 cells in the mammary gland at that timepoint). This is the foundation on which we built this current work, to study what could promote these different proliferation, dissemination, and metastasis behaviors in different HER2 isoforms.

      (2) Second, this study is mostly performed on three cell lines generated from three tumor models, WT, d16, and p95. Were multiple cell lines generated from the same tumor model (e.g., p95), and how similar are these cell lines if they are from the same tumor model?

      Our lab has generated a number of tumor cell lines derived from individual tumors developed in different HER2 Crainbow mice. We hypothesize, based on preliminary data in these cell lines as well as our previously reported data examining phenotypes of WT, d16, and p95 tumors (5, 6), that different clones will share core features such as invasive properties. In order to strengthen the generalizability of our conclusions, we intend to perform transwell assays, matrix degradation assays, and western blots to examine expression of Mrtfa and Tgfb1i1 in additional HER2 Crainbow-derived cell lines to validate if our findings hold true across cell lines derived from different tumors.

      (3) Third, Figure 2 presented data from a very interesting experiment. However, the overall conclusion of this experiment is hard to grasp from the text.

      We thank the reviewer for this comment. We will revise the text accompanying Figure 2 to provide further detail on the interpretation of the PCA plots and clarify the overall conclusions by adding the following text:

      Vectors indicate variable loadings, where vector direction corresponds to increasing values of the variable and vector length reflects the magnitude of the variable’s contribution to the displayed principal components. For example, HCR-WT populations cluster toward lower values of PC1 and higher values PC2, notably in the direction of higher self-correlation indicating an association with greater spatial clustering. HCR-16 and HCR-95 cells cluster similarly and are driven by their similarity in speed, MSD, persistence, and individual behavior (low self-correlation and high proportions of cells with zero neighbors), whereas HCR-WT is distinct for its collective cell behavior (high self-correlation) (Figure 2E). This separation indicates potentially distinct kinematic and spatial organization compared to HCR-16 and HCR-95 cells.

      Reviewer #2 (Public review):

      Summary:

      This is a significant study with implications for signal transduction, breast cancer, and metastasis research. The study uses cell lines from the innovative HER2BOW model mouse to compare and contrast properties of mouse mammary tumors induced by wt HER2, dex16 HER2, and p95 HER2. The linkage between p95 Y1139 and TGFB1I1, as well as MRTFA, is very interesting. The study involves mechanistic approaches to distinguish signaling from dex16 HER2 and p95 HER2 that will be well received by the field.

      Strengths:

      The study describes the development of novel cell lines for mouse mammary tumors induced by different forms of HER2. In vitro analysis includes a wide variety of assays, including high-resolution fluorescent imaging and tracing of cell movement/ECM degradation, and single-cell RNA-seq analysis. Several approaches are used to confirm p95 HER2 pY1139-induced signaling through nuclear MRTFA and TGFB1I1. shRNA and CRISPR/Cas9 were used to confirm signaling through this pathway.

      We thank the reviewer for these positive comments.

      Weaknesses:

      The authors have only described one cell line for each HER2 form, a weakness which they acknowledge. The fact that these lines mimic characteristics that were described in their previous work on tumors induced by wt HER2 vs. dex16 HER2 vs. p95 HER2 is, however, supportive of their conclusions. In addition, the specific connection between p95 and nuclear MRTFA is confirmed in HEK cells. The manuscript could be improved with some discussion on how p95 p-Y1139 is likely to signal (what binds to this site?)

      We thank the reviewer for this assessment, and we agree that adding additional cell lines derived from different HER2 Crainbow mouse tumors would strengthen the conclusions drawn in this manuscript. As mentioned in response to Reviewer #1, we intend to perform transwell assays, matrix degradation assays, and western blots to examine expression of Mrtfa and Tgfb1i1 in additional HER2 Crainbow-derived cell lines to validate if our findings hold true across cell lines derived from different tumors.

      With regards to p95 p-Y1139 signaling, previous work by Dankort et al. (11, 12) established that tyrosine autophosphorylation site Y1144 on rat neu (equivalent to Y1139 in human HER2) promoted lung metastasis in animal models, and that this site was necessary and sufficient for direct binding of Grb2.

      We intend to clarify and discuss links between Y1139 on p95 HER2 and the nuclear translocation of MRTFA.

      Reviewer #3 (Public review):

      Summary:

      The study aims to explain why different HER2 isoforms produce distinct cancer-cell phenotypes, with a particular focus on the poorly understood mechanisms by which p95-HER2 promotes the invasive and metastatic behaviors of HER2-positive breast cancer. The authors propose that functional selectivity at the HER2 receptor level, particularly signaling through Y1139, preferentially engages an MRTFA-TGFB1I1 transcriptional/cytoskeletal program, thereby shifting p95-HER2-expressing cells toward individual motility, matrix degradation, invasion, and metastasis rather than simply proliferation.

      Strengths:

      A major strength is the multi-level experimental strategy. Rather than relying on a single invasion assay, the authors integrate phenotypic profiling, single-cell RNA-seq, imaging of MRTFA nuclear localization, protein validation, cytoskeletal analysis, matrix-degradation assays, transwell invasion, 3D spheroid/organoid assays, and orthotopic transplantation. This provides relatively coherent evidence that p95-HER2 cells occupy a distinct biological state characterized by individual motility and invasion, accompanied by a myogenic/contractile transcriptional program and increased MRTFA nuclear localization. Another strong aspect is the attempt to connect the downstream phenotype to a specific HER2 phosphorylation site. The authors identify Y1139 as a candidate determinant of the "go" phenotype and show that mutation of Y1139 to phenylalanine eliminates MRTFA translocation as well as the associated motility and invasion phenotypes

      We thank the reviewer for these positive comments on our manuscript.

      Weaknesses:

      The main limitation is that the evidence for the proposed signaling mechanism is stronger for functional dependence than for direct molecular mechanism. The data establish that Y1139, MRTFA, and TGFB1I1 are required for the p95-HER2 invasive phenotype, but they do not appear to fully establish how phosphorylation at Y1139 mechanistically couples p95-HER2 to MRTFA activation. In particular, a direct biochemical link between Y1139 and the machinery controlling actin polymerization/MRTFA nuclear translocation would make the proposed pathway substantially more convincing.

      We thank the reviewer for these insightful comments. We agree that establishing a mechanistic link between p95 Y1139 and MRTFA nuclear translocation would strengthen the conclusions in this study. As such, we intend to perform Rho activation assays and western blotting for proteins in HER2 signaling cascades to explore the signaling link between p95 Y1139 and MRTFA. Additionally, we plan to treat cells with RhoA/ROCK inhibitors to explore our hypothesis that Y1139 acts through RhoA activation to ultimately alter MRTFA translocation.

      A second limitation is the model system used in the study. Much of the mechanistic work relies on three particular engineered HER2 isoform-expressing cell lines, while the in vivo experiments use NOD/SCID mice. This is useful for testing tumor-cell intrinsic invasion and metastasis, but it limits conclusions about the generality of the functional regulation across different cell contexts, and also limits the understanding of how the pathway operates in the intact immune microenvironment. This is especially relevant because the manuscript itself places p95-HER2 in the broader context of immune evasion and notes that MRTFA can regulate PD-L1; however, the current models cannot adequately establish whether the proposed pathway contributes to immune-mediated metastatic progression in vivo.

      We also acknowledge the limitations of relying on mostly in vitro assays and in vivo experiments in an immunodeficient environment, and will more explicitly address this in our discussion. The interplay between p95-HER2 and the immune system is being explored in a parallel project that will be published separately in the future; the focus of the current manuscript is the cell-intrinsic signaling mechanisms that contribute to p95 invasiveness. Points about immune evasion that were brought up in the introduction will be moved to the discussion section, to make it clear that the current study does not address the immunocompetent environment but that we wish to further investigate the results we report in this manuscript in that context as well.

      Finally, the distinction between "go" and "grow" signaling is conceptually attractive, but the extent to which it represents a general property of HER2-positive human breast cancers remains less certain. The study provides strong experimental evidence for functional selectivity in the models examined, but additional validation in independent patient-derived models and clinically relevant tumors would be needed before generalizing this mechanism across HER2-positive disease.

      With respect to validating findings in human samples, we intend to utilize human HER2+ breast cancer cell lines and/or patient-derived xenografts to investigate the extent to which our described mechanism is relevant in human HER2+ breast cancer.

      References:

      (1) Sáez R, Molina MA, Ramsey EE, Rojo F, Keenan EJ, Albanell J, et al. p95HER-2 Predicts Worse Outcome in Patients with HER-2-Positive Breast Cancer. Clinical Cancer Research. 2006;12:424–31.

      (2) Molina MA, Saez R, Ramsey EE, Garcia-Barchino MJ, Rojo F, Evans AJ, et al. NH(2)-terminal truncated HER-2 protein but not full-length receptor is associated with nodal metastasis in human breast cancer. Clin Cancer Res. 2002;8:347–53.

      (3) Pedersen K, Angelini PD, Laos S, Bach-Faig A, Cunningham MP, Ferrer-Ramon C, et al. A naturally occurring HER2 carboxy-terminal fragment promotes mammary tumor growth and metastasis. Mol Cell Biol. 2009;29:3319–31.

      (4) Turpin J, Ling C, Crosby EJ, Hartman ZC, Simond AM, Chodosh LA, et al. The ErbB2DeltaEx16 splice variant is a major oncogenic driver in breast cancer that promotes a pro-metastatic tumor microenvironment. Oncogene. 2016;35:6053–64.

      (5) Ginzel JD, Acharya CR, Lubkov V, Mori H, Boone PG, Rochelle LK, et al. HER2 Isoforms Uniquely Program Intratumor Heterogeneity and Predetermine Breast Cancer Trajectories During the Occult Tumorigenic Phase. Mol Cancer Res. 2021; 19(10):1699–1711.

      (6) Ginzel JD, Chapman H, Sills JE, Allen EJ, Barak LS, Cardiff RD, et al. Nonlinear progression during the occult transition establishes cancer lethality. Dis Model Mech. 2025;18:dmm052113.

      (7) Kwong KY, Hung M-C. A novel splice variant of HER2 with increased transformation activity. Molecular Carcinogenesis. 1998;23:62–8.

      (8) Mitra D, Brumlik M, Okamgba S, Zhu Y, Duplessis T, Parvani J, et al. An oncogenic isoform of HER2 associated with locally disseminated breast cancer and trastuzumab resistance. Mol Cancer Ther. 2009;8(8):2152-62.

      (9) Castagnoli L, Ladomery M, Tagliabue E, Pupa SM. The d16HER2 Splice Variant: A Friend or Foe of HER2-Positive Cancers? Cancers (Basel). 2019;11.

      (10) Sperinde J, Jin X, Banerjee J, Penuel E, Saha A, Diedrich G, et al. Quantitation of p95HER2 in paraffin sections by using a p95-specific antibody and correlation with outcome in a cohort of trastuzumab-treated breast cancer patients. Clin Cancer Res. 2010;16:4226–35.

      (11) Dankort DL, Wang Z, Blackmore V, Moran MF, Muller WJ. Distinct tyrosine autophosphorylation sites negatively and positively modulate neu-mediated transformation. Mol Cell Biol. 1997;17:5410–25.

      (12) Dankort D, Maslikowski B, Warner N, Kanno N, Kim H, Wang Z, et al. Grb2 and Shc adapter proteins play distinct roles in Neu (ErbB-2)-induced mammary tumorigenesis: implications for human breast cancer. Mol Cell Biol. 2001;21:1540–51.

    1. Author response:

      We thank the reviewers for their constructive feedback.

      Reviewer 1:

      (1) We will provide an estimate of total neuron numbers.

      (2) We will explore the possibility to extend cell type classification by unsupervised clustering of connectivity but it may not be possible to obtained a meaningful clustering based on the available connectivity data. The main issue is that connectivity information is available only for subsets of neurons. The underlying reason is that synapses were annotated manually and a complete manual annotation of the entire dataset would be an excessive task. In principle, this problem could be solved by automation but networks for automated annotation of synapses in other brain areas do not produce reliable results in the olfactory bulb, most likely because many neurites are both pre-and postsynaptic (further remarks below).

      (3) We are happy to supply the missing tables and to provide a glossary/table summarizing the features of the different neuron types.

      (4) Thank you; we will consider the suggestion to optimize Fig. 20.

      Reviewer 2:

      We agree that more a more comprehensive analysis of synaptic connectivity would be desired. The underlying problem, however, is that scaling synapse annotation requires automation but networks used for synapse annotation in other brain areas failed to produce reliable results in the olfactory bulb. The underlying reason is most likely that neurites of many olfactory bulb neurons are both pre- and postsynaptic; their ultrastructure is therefore different from classical axons or dendrites, e.g., vesicles are frequently found in close proximity on both sides. We therefore annotated synapses manually, which is the reason why synapse annotation was restricted to subsets of neurons. We will explain this situation in the revisions. Moreover, we will explore further approaches for automated cell type classification using both morphological and synaptic features.

      We shall be happy to include a glossary of cell types.

      We are also happy to expand the discussion of ultrastructural observations. Concerning primary cilia, we do not have a strong hypothesis concerning their function, neither based on our observations nor based on the literature.

      Reviewer 3:

      Following the reviewer’s suggestion we will be happy to include a more in-depth discussion of why our analysis is based primarily on human annotations and observations rather than more automated classification.

      As suggested by the reviewer we are planning to include additional figures and/or tables to show the relations between neuron types and layers, and to provide more summary information about cell types.

      We will also explain in more detail how neurons were chosen for connectivity analysis, with a specific focus on the assessment of connectivity fractions.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Our revision includes:

      (1) The generated data from long-read whole-genome sequencing of 1000 Genomes Project samples, including FASTQ files, SV calls, and the imputation panel, are now openly available via ENA and OpnMe. The imputed structural variant data have been submitted to UK Biobank for release through the UK Biobank Research Analysis Platform, subject to UK Biobank release procedures. SV-WAS summary statistics have been made available via OpnMe.

      (2) Clarification of analyses and methods, addition of two new Supplementary Figures, and correction of minor issues throughout the manuscript.

      (3) A significantly expanded Discussion to address the reviewers’ comments and better contextualise our methods and results.

      eLife Assessment

      This fundamental work significantly enhances our understanding of how structural variants influence human phenotypes. The conclusion is convincingly supported by rigorous analyses of long-read sequencing data. If the raw data are made publicly available, these high-quality datasets and findings will further advance our knowledge of genetic variation in the human population.

      We thank the editors for this positive assessment of our work. The raw long-read sequencing data (FASTQ files) can now be accessed through the European Nucleotide Archive (ENA) under accession number PRJEB89727, as part of a larger collection of 1019 sequenced probands from the 1000 Genomes Project (https://www.ebi.ac.uk/ena/browser/view/PRJEB89727). The generated imputation panel and the structural variant calls, based on the 888 probands used in the present manuscript, remain freely available for download at https://opnme.com/genomiclens. We have now added the summary statistics of 32 SV-wide association studies to the same resource. In addition, we have submitted the imputed SV genotypes for UK Biobank participants to the UK Biobank; once processed by UK Biobank, these genotypes will be released via the UK Biobank Research Analysis Platform (RAP).

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      The authors sequenced 888 individuals from the 1000 Genomes Project using the Oxford Nanopore long-read sequencing method to achieve highly sensitive, genome-wide detection of structural variants (SVs) at the population level. They conducted solid benchmarking of SV calling and systematically characterized the identified SVs. While short-read sequencing methods, including those used in the 1000 Genomes Project, have been widely applied, they exhibit high accuracy in detecting single nucleotide variants (SNVs) and small insertions and deletions but have limited sensitivity for SV detection. This study significantly enhances SV detection capabilities, establishing it as a valuable resource for human genetic research. Furthermore, the authors constructed an SV imputation panel using the generated data and imputed SVs in 488,130 individuals from the UK Biobank. They then conducted a proof-of-principle genome-wide association study (GWAS) analysis based on the imputed SVs and selected traits within the UK Biobank. Their findings demonstrate that incorporating SV-GWAS analysis provides additional insights beyond conventional GWAS frameworks focusing on SNVs, particularly in improving fine mapping.

      The authors constructed a high-sensitivity reference panel of genome-wide SVs at the population level, addressing a critical gap in the field of human genetics. This resource is expected to significantly advance research in human genetics. They demonstrated the imputation of SVs in individuals from the UK Biobank using this panel and conducted a proof-of-concept SV-based GWAS. Their findings highlight a novel and effective strategy for integrating SVs into GWAS, which will facilitate the analysis of human genetic data from the UK Biobank and other datasets. Their conclusions are supported by comprehensive analyses.

      We thank the reviewer for highlighting the value of our SV imputation reference panel.

      Weaknesses:

      (1) Although the authors employ state-of-the-art analytical approaches for the identification of SVs, the overall accuracy remains suboptimal, as indicated by an F1 score of 74.0%, particularly in tandem repeat regions. To enhance accuracy, it would be beneficial to explore alternative SV detection methods or develop novel approaches. Given the value of the reference panel and the fact that improved SV accuracy would lead to more precise SV imputation and GWAS results, investing effort in methodological refinement is highly encouraged.

      Accurate SV calling remains an active area of research and is beyond the scope of the present study. Tandem repeat regions are particularly challenging for standardised SV detection. We believe that achieving a benchmark for NA12878 of F1 = 74% on a genome-wide level and, notably, F1 = 91% when excluding longer tandem repeats, represents strong performance. This result is especially convincing when considering that our benchmarking compared the SV calls to data generated using a different sequencing technology and processed using different bioinformatics pipelines.

      (2) From the Methods section, it appears that the authors employed Beagle for both imputation and the UK Biobank imputation.

      (a) It would be better to explicitly clarify this in the Results section and provide a detailed description of the corresponding procedures and parameters in the Methods section for both analyses, as this represents a key aspect of the study.

      We thank the reviewer for these suggestions. Accordingly, we added the clarification to the Methods section that the leave-one-out imputation used exactly the same pipeline and settings as the UK Biobank imputation (page 14, section “Leave-one-out imputation performance”):

      “We excluded one individual from the panel and imputed SVs for this individual using the panel of the remaining 887 samples, applying exactly the same pipeline and settings as those later used for SV imputation into UK Biobank (see below).”

      (b) Additionally, Beagle is not specifically designed for SV imputation, the imputation quality of SVs is generally lower than that of SNVs. Exploring strategies to improve SV imputation, such as developing a novel method with reference panel data, may enhance performance.

      As stated in our manuscript (page 4), we believe that, in our study, the imputation quality of SVs is lower than of that of SNVs primarily because of a) the greater difficulty of SV calling compared to SNV genotype calling and b) the heterogeneity in SV representation across samples. Once SVs are encoded as bi-allelic markers in the reference panel, they can be imputed using the same LD/haplotype-based framework as any other variants. Accordingly, improving SV imputation is likely to benefit most from more accurate upstream SV calling and genotyping (e.g., through more robust multi-sample calling and harmonised variant representations) and not so much from improved or SV-specific imputation methods. While improved imputation is an important research direction, it is beyond the scope of the present manuscript.

      (c) It is also important to assess how this reduced imputation quality may influence GWAS results. For instance, it would be useful to examine whether associated SVs exhibit higher imputation quality and whether SVs with lower quality are less likely to achieve significant association signals. In addition, the lower imputation quality observed for INV, DUP, and BND variants (Figure 3) may be due to their greater lengths (Figure 2). It is better to investigate the relationship between SV length and imputation quality.

      We agree that imputation quality can influence GWAS results. For example, for the FEV1/FVC phenotype, SVs with INFO > 0.9 are almost twice as likely to reach genome-wide significance (p < 5e-8) compared with SVs with 0.7 < INFO < 0.9 (odds ratio 1.95; Fisher’s exact test p-value 2.5e-5). This is consistent with the intuitive notion (applicable to any variants, not only to SVs) that greater uncertainty in the imputed genotypes dilutes association signals and therefore reduces power. For a detailed discussion of the relationship between allele frequency, imputation accuracy, and GWAS association results, see Zhang et al., Human Molecular Genetics 31(1):146–155 (2022), https://doi.org/10.1093/hmg/ddab203

      We have now investigated the relationship between SV length and imputation quality (the new Supplementary Figure 6). The results suggest that the observed association between imputation quality and SV size is primarily driven by the SV-size–dependent minor allele frequency in the imputation panel.

      (3) All examples presented in the manuscript focus on SVs that overlap with genes. It may also be valuable to investigate SVs that do not overlap with genes but intersect with enhancer regions. SVs can contribute to disease by altering regulatory elements, such as enhancers, which play a crucial role in gene expression. Including such analyses would further demonstrate the utility of SV-GWAS and provide deeper insights into the functional impact of SVs.

      We agree with the reviewer that examining SVs intersecting with enhancer regions could be an interesting direction for future studies, as it would provide additional insights into regulatory mechanisms and disease associations. However, in the present proof-of-principle study, we prefer focusing on SVs overlapping with genes and have now highlighted this in additional detail in the revised manuscript (Discussion, page 7):

      “In the present proof-of-principle study, we focused on SVs overlapping with the coding sequence of genes. In future applications of our SV imputation panel, more refined gene mapping approaches could be employed, e.g., including SVs overlapping enhancer regions or epigenetic marks. Such an enhanced mapping would increase the number of identified associated genes and thus provide additional insights into regulatory mechanisms and disease biology.”

      (4) The data availability link currently provides only a VCF file ("sniffles2_joint_sv_calls.vcf.gz") containing the identified SVs.

      (a) It would be beneficial for the authors to make all raw sequencing data (FASTQ files) and key processed datasets (such as alignment results and merged SV and SNV files) available. Providing these resources would enable other researchers to develop improved SV detection and imputation methods or conduct further genetic analyses.

      Thank you for emphasising the importance of data sharing, which we agree with.

      The Data Availability section of the manuscript already includes a link to https://opnme.com/genomiclens, where we made both the SV calls and the full and reduced SV imputation panel files freely available. We have now added SV summary statistics from 32 SVwide association studies to the same resource. Based on the reviewer’s request, we now also reference the ENA repository project PRJEB89727 (https://www.ebi.ac.uk/ena/browser/view/PRJEB89727), where the raw FASTQ files are available for download, in the manuscript.

      We have appended the Data Availability statement on page 22 of the revised manuscript as follows:

      “Raw SV calls, the long-read sequencing-based SV imputation panel, and the SV summary statistics from 32 SV-wide association studies are available through the OpnMe initiative of Boehringer Ingelheim GmbH (https://opnme.com/genomiclens). The raw long-read sequencing data (FASTQ files) for the 1000 Genomes Project samples included in this study are accessible via the European Nucleotide Archive under accession number PRJEB89727 (https://www.ebi.ac.uk/ena/browser/view/PRJEB89727). The dataset analysed here constitutes a subset of this broader collection.”

      (b) Furthermore, establishing a dedicated website for data access, along with a genome browser for SV visualization, could significantly enhance the impact and accessibility of the study. Additionally, all code, particularly the SV imputation pipeline accompanied by a detailed tutorial, should be deposited in a public repository such as GitHub. This would support researchers in imputing SVs and conducting SV-GWAS on their own datasets.

      The Methods section provides a full and detailed description of the imputation pipeline and parameters in the section “Preprocessing and imputation of SVs into UK Biobank” on page 14 of the revised manuscript. Our data processing simply consisted of running standard bioinformatics tools with the parameters exactly as described in the manuscript.

      Reviewer #1 (Recommendations for the authors):

      (1) In the Results section, Figure 3b is mentioned before 3a, and it is better to switch them in the Figure.

      Thank you for highlighting this fact. We acknowledge that typically the sequence of sections matches exactly between text and figures. However, in this specific case, we would prefer to deviate from the norm: In our opinion, Figure 3 is easier to interpret in its current sequence. At the same time, the text flows more logically in its current sequence, describing 3b before 3a. We would therefore prefer to stick to the current order, even if it means that Fig. 3b is described before 3a in the text.

      (2) Page 10, "Figure 1e" -> "Figure 2e".

      Thank you, we corrected this issue.

      (3) Page 14, "Leave-one out" -> "Leave-one-out".

      Thank you, we corrected this mistake.

      (4) It is better not to use abbreviations in the subheadings, especially "UKB" (page 3).

      Thank you, we changed the acronym ‘UKB’ to ‘UK Biobank’ in all subheadings.

      Reviewer #2 (Public review):

      Summary:

      The authors aimed to develop a novel and efficient method for SV detection, utilizing data from the 1000 Genomes Project (1KGP) for modeling and calibration. This method was subsequently validated using UK population data and applied to identify structural variants associated with specific disease phenotypes.

      Strengths:

      Third-generation single-molecule sequencing data offers several advantages over traditional high-throughput sequencing methods, particularly due to its long-read lengths, which provide valuable insights into significant forms of genomic variation. The authors have developed an efficient method for detecting structural variations and optimizing the utilization of genomic data. We hope that this method will continue to be refined, enabling researchers to more effectively leverage long-read data, high-throughput data, or even a synergistic combination of both.

      Weaknesses:

      Although this research contributes to our ability to more effectively utilize long-length and high-throughput data, there are some key issues that need to be addressed in terms of analyzing the specific results as well as writing the article.

      Reviewer #2 (Recommendations for the authors):

      (1) How to discuss the lower detection rate of structural variations (SVs) in East Asian populations, it is worth considering whether the authors' training dataset, which may have been based on raw data with insufficient representation of East Asian individuals, could have introduced a bias favoring other populations. This potential bias might arise from the relatively limited data available for Asian ancestry. Alternatively, the observed differences could also be influenced by the role of natural selection, which may have shaped the genomic landscape of East Asian populations in distinct ways. Further investigation is needed to clarify these possibilities.

      Thank you for raising this important point. Although an interesting research direction, a detailed investigation of the factors affecting SV detection rates is beyond the scope of the present study. However, we do not think that the lower detection rate in East Asians is due to an underrepresentation of Asian ancestry in our dataset. To explain this to all readers, we have added the following explanation to page 7 of the Discussion:

      “In this context, we observed that the number of SVs detected per individual differed between superpopulations. We identified the highest average number of SVs in individuals of African descent and a slightly lower average in East Asians, compared to the other superpopulations. While we included a higher number of African ancestry individuals, the number of East Asian individuals included in our reference panel was comparable to the number of individuals from other, non-African ancestries. In fact, it was even larger than the number of European ancestry individuals (AFR n=241, SAS n=171; EAS n=168; EUR n=164; AMR n=144). Therefore, we do not expect a major bias from underrepresentation of any superpopulation in the training dataset. It is well established that African ancestry is more diverse than is the case for other superpopulations [32, 33] and previous studies indicate that East Asian populations tend to exhibit slightly lower genetic diversity compared to European populations [34], which is consistent with the lower observed SV counts per genome.”

      (2) The authors did not present the results of the detection of CNV.

      Copy number variations (CNVs) are considered a subclass of structural variants. In our analysis, we detected deletions and duplications, which represent the most common forms of CNVs. However, we did not specifically investigate high copy-number SVs, as these are often larger than what can be reliably detected using long-read sequencing. Large-scale CNVs are typically identified in biobank studies through analysis of intensity data from genotyping microarrays using tools like PennCNV, and there is extensive literature supporting the use of this microarray approach in UK Biobank and other genotyped cohorts, see for example Aguirre et al.: Phenomewide Burden of Copy-Number Variation in the UK Biobank. Am J Hum Genet. 2019, Aug 1;105(2):373-383. doi:10.1016/j.ajhg.2019.07.001.

      (3) Multiple testing correction is essential for ensuring the validity of large-scale structural variation (SV) association analyses. It is strongly recommended that the statistical methods and correction strategies employed, such as Bonferroni correction or false discovery rate (FDR) control, be explicitly detailed to enhance the transparency and reliability of the findings.

      For genome-wide SV association analyses, we applied the commonly used genome-wide significance threshold of 5e-8, which is standard in genome-wide studies. Given that these were exploratory proof-of-principle analyses illustrating use cases for SV analyses, we decided not to correct on top of that for multiple testing for the number of traits (32) tested. For the pQTL analyses, we further adjusted this threshold using a Bonferroni-type correction based on the number of proteins tested (1,463), to account for the increased number of multiple comparisons.

      We have now added a more detailed description of this multiple testing procedure to the Methods subsection “SV-wide association studies in UK Biobank” on page 16 of the revised manuscript:

      “In the exploratory SV-WAS, we used the standard threshold for genome-wide significance of p < 5×10<sup>-8</sup>. For the pQTL analyses, we applied Bonferroni correction for multiple testing on top of that genome-wide threshold, correcting for the number of tested protein levels (n=1463): p < 5×10<sup>-8</sup>/ 1463 = 3.4×10<sup>-11</sup>.”

      (4) The study primarily relied on data from the 1000 Genomes Project (1KGP) and the UK Biobank; however, the UK Biobank cohort is predominantly composed of individuals of European ancestry, which may restrict the generalizability of the research findings to other populations.

      Our reference panel was constructed to cover multiple ancestries, enabling imputation for diverse populations. Thus, our imputation panel can be applied to biobanks around the world and is freely available for this purpose. As a proof of principle, we have demonstrated the feasibility and performance of SV imputation in UK Biobank as an example of a broadly accessible cohort. We are looking forward to biobanks from diverse ancestries downloading our imputation panel and applying it to their populations.

      (5) Although the study employed long-read sequencing technology, the validation of structural variation (SV) detection accuracy predominantly relied on internal data, such as 'leave-one-out' validation. To further strengthen the reliability of the SV detection methods, it is recommended to incorporate additional external independent datasets for validation.

      The leave-one-out procedure in our study was used to validate the imputation performance, not the accuracy of SV detection. To assess SV calling accuracy, we performed extensive benchmarking against external SV call datasets derived from PacBio long-read sequencing and Illumina short-read sequencing. These details are provided under the subheading ‘Structural variant calling and benchmarking’ in the Results section on page 2 of the manuscript.

      (6) Some of the SVs mentioned in the study overlap with disease association loci in the GWAS Catalog, but functional annotation and exploration of the biological mechanisms of these SVs are more limited. It is suggested that LD can be added to analyse whether there are SNP that are highly linked to them to further explore their functions.

      We thank the reviewer for this suggestion. We have actually conducted an analysis addressing exactly this question: We performed conditional association analyses of the SV signals with nearby short variants (SNPs and InDels) at the SV locus. Such a conditional analysis addresses whether the observed SV association is influenced by LD-correlated SNPs or not. The results of this analysis are reported in Supplementary Tables 16 and 17. These tables include both the conditional analysis results and the LD between each SV and the variant at the locus with the second-highest evidence for an association.

      Researchers interested in exploring the biological significance of the SV-WAS results in more detail can now download the full SV-WAS summary statistics from https://opnme.com/genomiclens.

      (7) The discussion section could be further expanded to explore the role of SV in complex diseases and its potential application in precision medicine. For example, it could discuss how SV information can be integrated into existing GWAS frameworks to enhance the accuracy of disease risk prediction.

      Thank you for the suggestion, we have now added the following sentences to the discussion (page 7/8):

      “Structural variants can influence complex disease biology through either the disruption of coding sequence or an altered regulation of gene expression. Such effects may not be well captured by short variants alone. Incorporating SVs into GWAS and follow-up analyses would thus provide more accurate disease risk prediction, uncover underlying pathomechanisms by highlighting actionable pathways and targets, and support precision medicine by providing biomarkers for patient stratification.”

      (8) The geographic labeling of certain samples in Figure 2 appears to contain inaccuracies. For instance, the CDX sample, which represents the Dai population from Xishuangbanna in China's Yunnan Province, is currently mislabeled as originating from China's Inner Mongolia. This discrepancy should be corrected to ensure the accuracy of the data representation.

      We apologise for the misunderstanding. The geographic map in Figure 2a serves as an illustrative mapping of the samples to countries. It is intended to provide readers with an overview of population coverage, rather than to indicate the precise geographic origins of individual populations. The populations CDX, CHB, and CHS are displayed within the outline of China in alphabetical order, without any intention to indicate their exact geographic origin. We changed the respective figure caption to make this clear (page 19 of the revised manuscript):

      “Map of the 888 samples from the 1000 Genomes project, mapping the samples to countries and not indicating detailed geographical origins of populations.”

      Reviewer #3 (Public review):

      This study successfully identified genetic loci associated with various traits by generating large-scale long-read sequencing data from a diverse set of samples. This study is significant because it not only produces large-scale long-read genome sequencing data but also demonstrates its application in actual genetics research. Given its potential utility in various fields, this study is expected to make a valuable contribution to the academic community and to this journal. However, there are several critical aspects that could be improved. Below are specific comments for consideration.

      Strengths:

      Producing high-quality, large-scale variant datasets and imputation datasets

      Weaknesses:

      (1) Data availability

      Currently, it appears that only the Genomic Lens SV Panel is available on the webpage described in the Data Availability section. It is unclear whether the authors intend to release the raw sequencing data. Since the study utilized samples from the 1000 Genomes Project, there should be no restriction on making the data publicly accessible. Given this, would the authors consider making the raw sequencing reads publicly available? If so, NCBI SRA or EBI ENA would be the most appropriate repositories for data deposition. I strongly encourage the authors to consider public data release. Additionally, accessing the Genomic Lens SV Panel data does not seem straightforward. The manuscript should provide a more detailed description of how researchers can access and utilize these data. In my opinion, the best approach would be to upload the variant data (VCF files) to a public database such as the European Variation Archive (EVA) hosted by EBI.

      I strongly request that the authors publicly deposit the variant data. At a minimum:

      (a) The joint genotype data for all 888 samples from the 1000 Genomes Project must be publicly available.

      Thank you for emphasising the importance of data sharing, which we agree with.

      The Data Availability section of the manuscript already includes a link to https://opnme.com/genomiclens, where we make both the SV calls and the full and reduced SV imputation panels (provided as multi-sample VCF files) freely available. Based on the reviewer’s request, we now also reference the ENA repository project PRJEB89727 (https://www.ebi.ac.uk/ena/browser/view/PRJEB89727), where the raw FASTQ files are available for download.

      We have appended the Data Availability statement on page 22 of the revised manuscript as follows:

      “Raw SV calls, the long-read sequencing-based SV imputation panel, and the SV summary statistics from 32 SV-wide association studies are available through the OpnMe initiative of Boehringer Ingelheim GmbH (https://opnme.com/genomiclens). The raw long-read sequencing data (FASTQ files) for the 1000 Genomes Project samples included in this study are accessible via the European Nucleotide Archive under accession number PRJEB89727 (https://www.ebi.ac.uk/ena/browser/view/PRJEB89727). The dataset analysed here constitutes a subset of this broader collection.”

      (b) For the UK Biobank samples, at least allele frequency data should be disclosed.

      Supplementary Table 5 includes the allele frequencies of the SVs imputed into UK Biobank.

      (c) Since eLife has a well-established data-sharing policy, compliance with these guidelines is essential for publication in this journal.

      By sharing the FASTQ files, the SV calls, the SV imputation panels, the SV summary statistics, and (once processed by UK Biobank) the genotypes of SVs imputed into UK Biobank, we are providing all SV data generated in our study.

      (2) Long-read sequencing data quality

      While the manuscript presents N50 read length and mean or median read base quality for each sample in a table, it would be highly beneficial to visualize these data in figures as well. A violin plot or similar visualization summarizing these distributions would significantly improve data presentation.

      Notably, the base quality of ONT long-read sequencing data appears lower than expected. This may be attributed to the use of pore version 9.4.1, but the unexpectedly low base quality still warrants attention. It would be helpful to include a small figure within Figure 2 to illustrate this point. A visual representation of read length distribution and base quality distribution would strengthen the manuscript.

      We thank the reviewer for this suggestion. We have now included two violin plots (the new Supplementary Figure 1) to the revised manuscript, summarising a) the N50 read length per sequencing run and b) the median read quality per sequencing run. These plots provide a clearer visualisation of the underlying distributions. We do not consider the ONT base quality to be low. Importantly, structural variant detection is generally robust to modest variations of per-base quality. Therefore, we do not expect the observed base quality levels to significantly affect SV calling in this study.

      (3) Variant detection precision, recall, and F1 score

      This study focuses on insertions and deletions (indels) {greater than or equal to}50 bp, but it remains unclear how well variants <50 bp are detected. I am particularly interested in the precision, recall, and F1 score for variants between 5-49 bp.

      While ONT base quality is relatively low, single-base variants are challenging to analyze, but variants {greater than or equal to}5 bp should still be detectable as their read accuracy is still approximately 90%, making analysis feasible. Given that Sniffles supports the detection of variants as small as 1 bp, I strongly encourage the authors to conduct an additional analysis.

      A simple two-category classification (e.g., 5-49 bp and {greater than or equal to}50 bp) should suffice. Additionally, a comparative analysis with HiFi and short-read sequencing data would be highly valuable. If possible, I strongly recommend that all detected variants {greater than or equal to}5 bp be made publicly available as VCF files.

      Because short InDels are available from high-coverage Illumina sequencing data generated for the same individuals (i.e., the data referred to as the NYGC dataset in our manuscript), we decided against calling such short variants from our lower coverage Oxford Nanopore data and thus concentrated our efforts on reliably calling longer variants covering at least 50 bp, consistent with the conventional definition of structural variants.

      (4) Assembly-based methods

      Given the low read accuracy and low sequencing depth in this dataset, it is understandable that genome assembly is challenging. However, the latest high-quality human genome datasets-such as those produced by the Human Pangenome Reference Consortium (HPRC)demonstrate that assembly-based approaches provide significant advantages, particularly for resolving complex and long structural variants.

      Since HPRC data also utilize 1000 Genomes Project samples, it would be highly informative to compare the accuracy of ONT sequencing in this study with HPRC's assembly-based genome data. The recent publication on 47 HPRC samples provides a valuable reference for such a comparison. Given its relevance, the authors should consider providing a comparative analysis with HPRC data.

      The aim of the present study was to generate an SV reference panel that enables SV imputation for large biobanks. Detailed assessments of ONT sequencing quality in general and comparisons to other sequencing efforts and technologies are out of scope for the present manuscript. We invite the scientific community to use the FASTQ files provided at ENA for conducting such detailed assessments in follow-up studies.

    1. Author response:

      Reviewer #1 (Public review):

      Summary:

      The authors introduce a foraging task designed to test whether movement and harvesting durations are governed by a common objective combining reward, effort, and time or by separate objectives. Participants generate wrist torque to move a cursor to a rewarding patch and then hold it within the patch while reward accumulates at a diminishing rate. The task allows reach and harvest effort, as well as delays before or between the two phases, to be manipulated separately.

      Reach effort strongly affected reach duration but had little effect on harvest duration, whereas a delay imposed after reaching altered harvest duration without affecting the completed reach. Manipulation of harvest effort did not affect either duration. The authors also found consistency across individuals within each type of duration but no reliable association between reach and harvest durations. The separate model fit the behavioral results better than the common-utility model, particularly for the post-reach delay condition. The findings therefore support partly dissociable, but coupled optimization of harvest and movement in this task, while not excluding common optimization in other contexts.

      Strengths:

      The task provides a controlled way to manipulate the effort and delays associated with reaching and harvesting while measuring both durations. The control experiments alter the timing of delays, allowing the experimenter to test whether their effects depend on when they occur. These manipulations produce clear behavioral dissociations, particularly the selective effect of a post-reach delay on harvest duration. The delay and effort manipulations were verified, and most participants reported noticing the changes in effort and time.

      The separate model extends a previous cost-of-time framework to a foraging task involving movement and reward harvesting. Its assumptions have a clear relationship to the experimental design: applied delays and actions enter the time offset for each separate cost function. This provides an intuitive account of why a delay occurring after the reach can affect harvesting without affecting the completed movement. The separate model also provides a better fit than the common utility model in both modeled experiments.

      The individual-level behavioral analyses are also useful. Reach durations are correlated across reach conditions, and harvest durations are correlated across harvest conditions, indicating stable individual differences within each measure. The lack of a corresponding relationship between reach and harvest durations raises an important question about whether the two forms of vigor necessarily reflect a common individual tendency in their task.

      We thank the reviewer for acknowledging the relevance of our study.

      Weaknesses:

      The block design and familiarization made the changes in effort and delay learnable, and most participants reported awareness of these manipulations. The observed dissociation may reflect adaptation to this task structure. This does not weaken the behavioral result, but it limits how directly the findings can be generalized to tasks in which changes in reward, effort, or time are less explicit.

      The results show that, in a controlled environment, the common-utility model did not account for certain behaviors observed in our participants. In variable environments, because the previous history of reward and effort affect the current trial (Yoon et al., 2018; Sukumar et al., 2024), the behavioral regulation could be less stable and apparent. Here, we provided a favorable environment to assess the common-utility model, with stable manipulations of time and effort in a block-wise design allowing clear estimation of the capture rate by the participants. We agree with the reviewer that it is not necessarily generalizable to other types of environments involving uncertainty for instance. However, demonstrating that movement and decision vigor can be dissociated in a specific task is good evidence to suggest that it is not always co-regulated, and should therefore be flexible. This potential adaptation resulting from the development of explicit knowledge is a problem present in most studies of this type, where conditions are introduced in a blocked manner (Saleri Lunazzi et al., 2021; Sukumar et al., 2024). We will discuss this point in more detail in the revised version of the manuscript.

      The main modeling limitation is that both models are fitted to ten group-level median observations in each experiment, rather than to individuals' behavior. The separate model has seven fitted parameters compared with three in the common model. Although the reported AIC penalizes additional parameters, the analysis includes no participant-level fitting, resampling, or cross-validation.

      We acknowledge that fitting the models to participants’ individual behavior could provide better insight into the ability of the evaluated models to accurately capture the effects of time and effort on behavior. We will perform these analyses during the review.

      Reviewer #2 (Public review):

      Summary:

      The manuscript by Conessa and colleagues tests whether movement time and decision time are co-regulated in humans using a novel harvesting paradigm and computational modelling of the behavioral data. The data contradict the common utility model and are better supported by an alternative model where the costs of the harvesting and movement phases are optimized separately - rather than jointly.

      Strengths:

      The major strength of the study is the development of the novel paradigm where the forces applied during the distinct phases of the task (reaching and harvesting) can be perfectly controlled and measured.

      This elegant manipulation allows precise estimation of subjective effort costs, and later can be used to better understand how these costs shape behavior.

      The novel separate-cost model is also an interesting development.

      We thank the reviewer for acknowledging the strengths of our study and for the constructive suggestions. Below, we provide preliminary responses with some planned adjustments.

      Weaknesses:

      In my opinion, the manuscript suffers from too many weaknesses to solidly support the general conclusions:

      (1) The manuscript oversells the significance of the results;

      (2) The novel model appears to be built ad hoc based on the results, and its ingredients are poorly motivated

      (3) There are important methodological shortcomings. I develop all of these points below. The paper also lacks clarity, particularly when presenting the key concepts of the novel model.

      The model relies on a large part of the literature that assumes a cost of time affecting movement and decision-making. For instance, the urgency-gating model associate a time-growing signal with the pace of decisions (Cisek et al., 2009; Thura, 2020; Saleri Lunazzi et al., 2021); and a cost of time underlying human reaching vigor has been identified in previous studies (Shadmehr et al., 2010a; Choi et al., 2014; Berret et al., 2018; Berret and Baud-Bovy, 2022; Verdel et al., 2023). Our model is simply grounded on those studies. We will detail further the rationale behind the separate-cost model and address as much as possible the points highlighted by the reviewer.

      Importantly, I also recommend that the authors follow open science policy and publish their data and code on a public repository.

      The authors agree with the reviewer. Data are available in Supplementary Data and code used will be published on a public repository.

      (1) Significance

      As mentioned above, the question of the co-regulation of the vigor of different behaviors is a very interesting topic, but I believe the significance of the results is overstated, for different reasons:

      a) This is a harvesting task, which means that decisions are specifically about the duration of the reward period. In other words, more time directly provides more (immediate) reward, whereas in other types of tasks more time allows gathering and processing more information, and so reaching a more informed decision, which is a more indirect way of securing better outcomes - see e.g. Drugowitsch, Moreno-Bote et al. JNeurosci 2012 for optimizing decision time in this most common setting. This major difference is not discussed in the manuscript, and it is not clear whether the results found here would hold for the most common type of decisions. This is also different from the time to initiate a response, as explored by Morvan et al. in their cited preprint.

      One feature of the present study, consistent with previous work (Yoon et al., 2018; Sukumar et al., 2024), is the use of a harvesting task to study the decision-making process (Hayden, 2018). The context of optimal foraging provides an interesting approach to study decision-making, as it is directly linked to ecological contexts. Remaining in a food patch does indeed result in an immediate increase in reward, but staying there too long risks reducing the capture rate, which, according to the utility model, represents the actual value that matters. The subject has to gather information about the current state of the patch and the global capture rate of the environment to decide how long he should harvest. Here, the aim of the article was not to generalize the results to all types of decisions, but to test the utility model in a very specific and controlled environment to better dissociate the effects of time and effort. In our task, movement and decision vigor is not co-regulated, which can be seen as a counterexample of a systematic co-regulation. However, there are a lot of possible tasks combining movement and decision-making in different forms.  As such, we argue that behavior may benefit from a certain degree of flexibility that allows for the separation of movement and decision-making vigor when relevant to a given task. Depending on the context, optimal behavior may require moving quickly while deciding quickly, moving quickly while deciding slowly, or other combinations (see Thura et al., 2025 for a review). In this respect, the separate-cost model allows flexible regulation (coupled or not), hence capturing which regulation is optimal, as long as the objective costs (defined by the task) and the participant’s subjective costs (specific to the participant) are appropriately combined. The common-utility model is comparatively more constrained because movement and decision costs are intrinsically integrated.  We agree that this distinction warrants further discussion and will clarify it, together with the resulting limits on generalization, in the revised manuscript.

      b) The title of the study mentions "flexible" co-regulation, but it's hard to see direct evidence for flexibility in the results. This flexibility is extrapolated in the Discussion, but in order to make such a statement, it is necessary to show that the co-regulation differs between different conditions, as predicted from the model.

      The term flexible is used to highlight that the rigid co-regulation predicted by the common-utility model does not apply to all manipulations of effort and time in this controlled design, nor to all types of decision-making (harvest vs reaction time). Decisions in the form of harvest durations do not seem to co-vary with reach durations, contrary to decisions performed during reaction times. Accordingly, and based on recent evidences (see Thura et al. 2025 for a review), this co-regulation appears to be flexible, depending on the actual optimal behavior required by the task and the type of decisions involved. In our paper, we found a co-regulation between reaction times and movement times but an independence of harvest times and movement times. Together with existing results from the literature, we conclude about the flexibility of co-regulation. However, we acknowledge that the (co-)regulations have not been directly compared in our paper. We plan to further assess this point.

      c) The lack of impact of the harvesting effort on harvest time is very surprising, and the null value of the sensitivity to effort (d=0) in the model is intellectually uncomfortable. As some value of effort, it SHOULD matter. I am not very satisfied with the explanation provided in the Discussion ("possible hypothesis would be that the perceived effort of harvest was outweighed by the reward value"): this trade-off should be precisely dealt with by the model.

      We agree with the reviewer and the lack of an effect of harvest effort on its duration was surprising to us too. However, the null value of sensitivity to harvest effort should not be interpreted as the effort does not influence the harvest or the decision in general. This effort is indeed likely not significant enough to necessitate a change in behavior. The free weighting parameters capture the relative sensitivity of the costs involved. Although effort was noticeable for the participants and of the same magnitude as variations in movement effort, it is likely they did not find it disruptive enough to adjust their behavioral strategy, demonstrating that it was not a critical factor in these conditions. We note that both the cost of time and the harvesting cost of effort increase with time, which suggests that in this timescale and this level of effort, the cost of time may have had a greater influence on behavior. Yet, our model could have captured effort-related variations of harvest duration if there were observed experimentally. To observe such effects, we should have increased harvesting effort but it might have led to behavioral changes due to muscular fatigue or maximal isometric torque limitations (which are not considered in the current modeling) rather than to the optimization of subjective utility. We will clarify what this sensitivity of harvest effort represents, and examine alternative constraints on the free parameters.

      (2) Separate-Cost Model

      The separate-cost model is poorly motivated and not clearly presented, in particular the indirect coupling between the two phases.

      a) Some key components are motivated by the constraint to obtain a well-behaved optimization problem ('we need to find a cost that increases with time' ) rather than based on cognitive principles. Some other key components seem to have been placed there just to fit the data better, but their plausibility is not even discussed. Notably:

      i) The fact that the offset o_h includes the reaching delay is key to the coupling between t_h and t_r, but is not properly motivated. Why should this offset include all preceding intervals within the trial (leading to double counting of the cost of the reaching phase, in both G_r and G_d)? In this cyclic paradigm where participants aim at maximizing cumulative reward, it is not even clear that they parse behavior into different trials starting as they need to reach for a new target.

      Precisely, as the reviewer pointed out, this offset is key to the coupling of t<sub>h</sub> and t<sub>r</sub>, and it actually constitutes an original extension to previous `cost of time` models. Including t<sub>r</sub> in the offset o<sub>h</sub> allows the separate-cost model to co-regulation to some extent, without leading to double-counting the reach cost. It must be noted that G<sub>r</sub> and G<sub>h</sub> are distinct time cost functions, and the value of G<sub>h</sub> at t<sub>r</sub> can be different from that of G<sub>h</sub> at </>t<sub>r</sub>. The offset allows reach duration to influence harvest duration because it shifts its cost of time. Recent evidence show that subjects rely only to a limited extent on their past experience when assessing the quality of their environment (Sukumar et al., 2024). Hence, our hypothesis is that only recent delays could influence the cost of time, in the form of an offset that creates a bias affecting the vigor. For this reason, we chose to define it as the cumulative time elapsed from the start of each trial. Due to the cyclic nature, the models are then applied to the average behavior within a condition, allowing us to reduce variability. We plan to make the rationale clearer in the revised manuscript.

      ii) Why is there a free parameter d for the cost of harvest effort? If time and motor costs are converted into the same currency, and that conversion holds for all types of phases, then I believe we should have d=1. This free parameter seems to have been introduced a posteriori to accommodate the lack of effect of harvest effort on harvest time, but is not motivated.

      The number of free weighting parameters is defined by the minimization of a linear combination of cost functions. The reaching phase comprises only two costs in this model, leading to the possibility to have only one free weighting parameter that capture the relative sensitivity to time and effort. However, regarding the harvest phase, as there are three different costs, it was necessary to have at least two free weighting parameters to account for relative sensitivity and convert all costs in the same currency. Alternatively, we could indeed have applied a free parameter to the reward and set d = 1. However, the purpose of the study was to assess the contribution of time and effort changes, and ultimately participants’ sensitivity to changes in these factors. As such, it appeared appropriate to evaluate the sensitivity of the harvest effort captured by the models, rather than the reward (which is not manipulated). It was also to keep some consistency with the common utility model, which includes a free weighting parameter for the costs of effort and time (and none for the reward function) as well. We will add more details regarding the motivation behind the separate-cost model and the use/choice of these free parameters. We agree that the rationale for this parameterization was not sufficiently described in the manuscript and will clarify it in the revised version. We will also examine alternative constraints on the free parameters.

      b) The two models differ in two fundamental aspects: whether optimization is run separately on the different phases of the trial, or jointly; and how the different costs and rewards are assembled in the to-be-optimized metric. Which aspect is more important to capture behavior is not assessed.

      We thank the reviewer for raising this interesting point. It is difficult to determine which aspect is most important: the separate versus joint optimization, or how the costs are assembled (additive vs multiplicative). However, the two are closely linked. It is the switch from a multiplicative association of the cost (common-utility model) to an additive one (separate-cost) that makes the separate optimization possible. For example, it is not possible to achieve an optimal movement duration using the costs interaction from the common-utility model, since there would simply be a discounting of the cost of effort by the cost of time . It would be necessary to add another element justifying why the movement should not be infinitely slow, which would therefore require changing the costs or adapting them to capture a logical behavior. This is what led to the design of the separate-cost model, by switching to an additive model allowing an optimal duration to emerge for each phase. We will further examine this issue in the revision, in particular by testing whether the separate-cost model can also account for observed behaviors under a joint optimization of reaching and harvesting durations.

      c) The presentation of the "Separate-cost model" is very obscure. For example, the notion of a `cost of reward` is rather odd, and consequently the formula for R(t_h) appears arbitrary. I understand that this is the difference between the maximum reward that can be collected within a trial and the actual reward that is collected, but it is not even presented as such. The effort cost of harvesting seems to be discarded in the model presentation but does appear in equation 14.

      The terminology `cost of reward` is admittedly odd but is used because it is the counterpart of the harvest function used in the common-utility f<sub>h</sub>(t<sub>h</sub>). Instead of using it in a form subject to maximization, we use it in a form subject to minimization. The purpose of this function is to maintain a certain consistency between the models and the various types of costs implied; as such it was crucial to incorporate a function capturing the harvested reward in the separate-cost model. We will detail further this point in the revised version, as we agree that our previous explanation was insufficient. The effort cost of harvesting was not presented again in the separate-cost model section since it was already identified (as was the effort cost of reaching) in the common-utility section and referenced to the corresponding equation.

      (3) Methodological Weaknesses

      I believe that there are numerous methodological weaknesses that really limit the inferences that can be drawn from the experimental and modelling results.

      a) Sample sizes are small, especially for control experiments, and it is not clear how they have been selected. This is especially problematic because the only manipulation that shows no significant effect on behavior (harvest duration) is only tested with the smallest sample size (n=10), severely limiting the significance of this negative result.

      We acknowledge that some of the sample sizes are small. Importantly, the main goal of the study was to determine the effect of time and effort manipulations on the behavioral vigor. The first main experiment had already provided us with lot of insights to reach this objective, but to go further and explore our subsequent hypotheses, we decided to examine the role of the delay position and another type of effort cost. The change in harvesting effort is not the only manipulation that showed no effect on behavior. In the main experiment, we observed that changes in effort required for reaching does not affect the harvest duration, even though this is predicted by the common-utility model. In the same experiment, we also observed that changes in delays do not affect the reach duration, even though this is also predicted by common-utility model. Nevertheless, we will discuss the limit of the control experiments further in the revised version.

      b) The rationale for the different manipulations in different experiments is not clear. Notably, why were modulations of the harvest effort not included in the main experiment? Because not a single participant sees a modulation of both reach and harvest efforts, we cannot evaluate whether the model can capture both effects at the same time (i.e., with the same parameter values). The number of data points used for fitting directly depends on the number of conditions performed by the participant, and is very low compared to the number of parameters to be fitted. For example, the model used very different shapes for the costs of time (Figure 8) for different sets of conditions, but this cost of time should be fixed, so it's not clear whether a single cost of time function can accommodate all manipulations.

      We agree that the rationale for the different manipulations across experiments was not sufficiently explained. Traditionally, optimal foraging has not been studied in conjunction with movement vigor (Yoon et al., 2018), but a recent framework accounts for both decision-making and motor control (Shadmehr et al., 2016). In the main experiment, we chose to manipulate reaching effort because our primary aim was to test whether variations in the cost involved in motor control influence (i.e., co-regulate) the decision-making process. The manipulations of effort and time in the main experiment were a good basis for evaluating the common-utility model in a controlled environment. Showing that reaching effort would affect harvest duration would have already been great evidence to illustrate a form of co-regulation. Moreover, we had no certainty that the participants would exhibit stable behavior, and adding twice as many conditions risked introducing further biases related to fatigue and attentional focus. We decided to run control experiments upon seeing the results of this initial experiment, when other questions arose regarding the effect of the delay position and of the type of effort. We acknowledge that performing all manipulation in one large experiment would indeed have significantly increased the significance of the models’ predictions. Nonetheless, we made sure that the number of parameters fitted were taken into account by using the AIC to evaluate models’ performance. Regarding the assumption that the shape of the cost of time should be fixed: adding a waiting period changes (slightly) the task, and it is conceivable that a different task should be represented by a different cost of time. Reaching and harvesting are too distinct tasks, and the subjective cost of elapsed time may therefore differ depending on whether participants are moving or remaining stationary. Different cost of times have been proposed for both arm-reaching movements and saccades (Shadmehr et al., 2010b; Berret et al., 2018), in particular because these movements occur over very different timescales. This suggests that how the passage of time is valued may depend on the task at hand. Altogether, this led us to consider letting the cost of time have different shapes for each phase and each experiment (although fixed within the sigmoidal family of function). We will clarify the rationale for the different manipulations and the use of different cost of time for each phase in the revised manuscript.

      c) Best practice in behavioral modelling is to model single-subject data, as fitting the model jointly to all subjects completely obliterates subject heterogeneity. Fitting on single-subject data would also allow investigating whether the models reproduce the consistency of harvest durations and reach durations across conditions, and most importantly the absence of correlation across subjects between reach and harvest duration. At the moment, we're left wondering what the implications of these analyses for the original question are.

      We agree that fitting these models to the individual behavior of the participants would be interesting to assess the models’ ability to capture participants’ variability. We will explore this during the revision.

      d) What is the rationale for comparing reach duration in one condition to harvest duration in another condition?

      If behavioral vigor (either of movement or decision) is a trait-like characteristic supported by shared processes, some degree of consistency between movement and decision vigor is expected. For instance, participants who tend to move faster might also tend to decide faster, if their vigor relates to traits like impulsivity for instance (Choi et al., 2014; Berret et al., 2018; Labaune et al., 2020). As such, we decided to perform all correlations to provide a comprehensive overview of inter-individual consistency of vigor in a foraging-like task.

      e) The study does not take into account the likely impact of delays on muscular fatigue and perceived effort: the effort associated with maintaining the cursor on target during harvest might be perceived as less effortful after a longer break, partially explaining the impact of delay on harvest duration.

      The idea that delays may influence muscular fatigue and perceived effort is intriguing. However, we believe that if perceived effort was the reason leading to changes in harvest duration, changes would also have been elicited by manipulation of harvest effort. This point will be discussed further during the revision.

      f) I am confused by the reference to indirect effects in the separate-cost model (L692-7, Table 2). To fit this model, was the experimental value or theoretical value of the reach duration t_d used to determine the optimal harvest value (from Equation 14)? In both cases, the reach duration DOES increase with reach effort, so we should expect an impact on the harvest duration. This is indeed seen in Figure 7A. So why does Table 2 suggest that reach effort should not impact harvest duration in this model?

      We agree that this point was not sufficiently clear. The purpose of Table 2 was to present the specific effect of each modulation. Thus, the prediction that reach effort does not affect harvest duration in the separate-cost model refers specifically to a change in reach effort at a fixed reach duration. An example with our experimental design would be to display a virtual movement of fixed duration during which participants have to produce a torque (isometric contraction) superior to a certain threshold that could vary between conditions. The inter-dependence of reach and harvest are based on duration changes; manipulation of the magnitude of effort exerted during movement at fixed duration would therefore not affect harvest duration. Table 2 was intended to distinguish these direct and indirect effects rather than to predict that reach effort should have no effect on harvest duration in our experiment. To fit the model to the data, the experimental value of the reach duration was used. However, since Table 2 shows only the directions of the variations, an arbitrary fixed value for reach duration (of the same magnitude) was used to determine the direct effect represented. We will clarify this distinction and the purpose of Table 2 in the revised manuscript.

      g) Could the effect of pre-reach delay on reach time be alternatively explained simply by longer reaction times as reported in Figure S2, e.g., a longer period to reactivate the muscles after a longer break? In other words, as far as I understood, here reaction times are subsumed in the motor time, against the tradition of splitting them into two independent (non-overlapping) behavioral metrics.

      This is an interesting point raised by the reviewer and will be discussed further in the revision. Here, we assume that a shorter reaction times are associated with a less steep cost-of-time function. According to drift-diffusion models, it brings the decision-related neural activity more slowly toward the commitment threshold, thereby delaying movement initiation. Since the cost of time is less steep, the movement duration will also be increased, thus implying this co-regulation between movement and reaction time.

      Here, reaction time was not separated, since the protocol is not appropriately designed to its study, particularly in the main experiment. The detection of reaction time is highly conservative (see text of Time-Related supplementary analyses) and it is not entirely clear whether we can properly refer to a reaction time in the main experiment, since the two phases follow one another without any delay. Hence to avoid any uncertainty, we chose not to separate these presumed reaction times from motor times.

      h) The EMG-time integral in the harvest phase should be largely proportional to the harvest duration, given that the applied torque is constrained to remain on target. Is this the case? If so, then how to interpret the significant effect of reach effort on this value, given that the main analyses did not identify an effect of reach effort on harvest duration?

      We thank the reviewer for pointing this interesting effect. It is possible that a greater muscle activation during the reaching phase was carried over to the harvest phase (due to increased co-contraction for instance), leading to an increase in the EMG-time integral in the harvest despite manipulation of reach effort. We will explore this during the revision. In particular, we will examine how the EMG signals recorded during the reaching relate to those recorded during the harvesting, as well as the relationship between the EMG signals and the torque exerted by the participants.

      References

      Berret B, Baud-Bovy G (2022) Evidence for a cost of time in the invigoration of isometric reaching movements. J Neurophysiol 127:689–701.

      Berret B, Castanier C, Bastide S, Deroche T (2018) Vigour of self-paced reaching movement: cost of time and individual traits. Sci Rep 8:10655.

      Choi JES, Vaswani PA, Shadmehr R (2014) Vigor of Movements and the Cost of Time in Decision Making. J Neurosci 34:1212–1223.

      Cisek P, Puskas GA, El-Murr S (2009) Decisions in Changing Conditions: The Urgency-Gating Model. J Neurosci 29:11560–11571.

      Hayden BY (2018) Economic choice: the foraging perspective. Curr Opin Behav Sci 24:1–6.

      Labaune O, Deroche T, Teulier C, Berret B (2020) Vigor of reaching, walking, and gazing movements: on the consistency of interindividual differences. J Neurophysiol 123:234–242.

      Saleri Lunazzi C, Reynaud AJ, Thura D (2021) Dissociating the Impact of Movement Time and Energy Costs on Decision-Making and Action Initiation in Humans. Front Hum Neurosci 15:715212.

      Shadmehr R, Huang HJ, Ahmed AA (2016) A Representation of Effort in Decision-Making and Motor Control. Curr Biol 26:1929–1934.

      Shadmehr R, Orban de Xivry JJ, Xu-Wilson M, Shih T-Y (2010a) Temporal discounting of reward and the cost of time in motor control. J Neurosci Off J Soc Neurosci 30:10507–10516.

      Shadmehr R, Xivry JJO de, Xu-Wilson M, Shih T-Y (2010b) Temporal Discounting of Reward and the Cost of Time in Motor Control. J Neurosci 30:10507–10516.

      Sukumar S, Shadmehr R, Ahmed AA (2024) Effects of reward and effort history on decision making and movement vigor during foraging. J Neurophysiol 131:638–651.

      Thura D (2020) Decision urgency invigorates movement in humans. Behav Brain Res 382:112477.

      Thura D, Haith AM, Derosiere G, Duque J (2025) The integrated control of decision and movement vigor. Trends Cogn Sci:S1364-6613(25)00185-8.

      Verdel D, Bruneau O, Sahm G, Vignais N, Berret B (2023) The value of time in the invigoration of human movements when interacting with a robotic exoskeleton. Sci Adv 9:eadh9533.

      Yoon T, Geary RB, Ahmed AA, Shadmehr R (2018) Control of movement vigor and decision making during foraging. Proc Natl Acad Sci 115:E10476–E10485.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      The study by Luden et al. seeks to elucidate the molecular functions of AHL15, a member of the AT-HOOK MOTIF NUCLEAR LOCALIZED (AHL) protein family, whose overexpression has been shown to extend plant longevity in Arabidopsis. To address this question, the authors conducted genome-wide ChIP-sequencing analyses to identify AHL15 binding sites. They further integrated these data with RNA-sequencing and ATAC-sequencing analyses to compare directly bound AHL15 targets with genes exhibiting altered expression and chromatin accessibility upon ectopic AHL15 overexpression.

      The analyses indicate that AHL15 preferentially associates with regions near transcription start sites (TSS) and transcription end sites (TES). Notably, no clear consensus DNA-binding motif was identified, suggesting that AHL15 binding may be mediated through interactions with other regulatory factors rather than through direct sequence recognition. The authors further show that AHL15 predominantly represses its direct target genes; however, this repression appears to be largely independent of detectable changes in chromatin accessibility.

      In addition to the AHL protein family, the globular H1 domain-containing high-mobility group A (GH1-HMGA) protein family also harbors AT-hook DNA-binding domains. Recent studies have shown that GH1-HMGA proteins repress FLC, a key regulator of flowering time, by interfering with gene-loop formation. The observed enrichment of AHL15 at both TSS and TES regions, therefore, raises the intriguing possibility that AHL15 may also participate in regulating gene-loop architecture. Consistent with this idea, the authors report that several direct AHL15 target genes are known to form gene loops.

      Overall, the conclusions of this study are well supported by the presented data and provide new mechanistic insights into how AHL family proteins may regulate gene expression.

      However, it is important to note that the genome-wide analyses in this study rely predominantly on ectopic overexpression of AHL15 at developmental stages when the gene is not usually expressed. Moreover, loss-of-function phenotypes for AHL15 have not been reported, leaving unresolved whether AHL15 plays a physiological role in regulating plant longevity under native conditions. It therefore remains possible that longevity control is mediated by other AHL family members rather than by AHL15 itself. In this regard, the manuscript's title would benefit from more accurately reflecting this broader implication.

      The ahl15 loss-of-function phenotype has previously been described in Karami et al., 2020 (Nat. Plants), Rahimi et al., 2022a (New Phyt.), and Rahimi et al., 2022b (Curr. Biol.), showing that ahl15 loss-of-function among others results in accelerated vegetative phase change and flowering, a reduced number of leaves produced by axillary meristems in short day grown plants and reduced secondary growth in the inflorescence stem. The dominant-negative ahl15 delta-G allele, expressing a mutant protein lacking the conserved G motif in the PPC domain, shows these phenotypes more clearly in the heterozygous ahl15 +/- background, and is embryo lethal in the homozygous ahl15 background (Karami et al., 2021, Nature Comm.). In addition, we recently show that leaf senescence is significantly accelerated in the ahl15 loss-of-function mutant (Luden et al., 2025, BioRxiv). These results show that AHL15 is involved in several aspects of ageing in Arabidopsis, and we have adjusted the introduction to discuss these previous findings more explicitlyWe agree with reviewer 1 on the possibility that multiple AHLs could have an effect on longevity, which is partially supported by the delayed flowering time observed in the AHL20, AHL27, or AHL29 overexpression lines (Karami et al., 2020, Street et al., 2008). However, the induction of the AHL15-GR fusion alone by DEX shows a clear delay of developmental phase transitions and the aging process in general, indicating that AHL15 by itself is able to extend longevity as other AHLs are not affected by DEX treatment (proven by the fact that their expression is not significantly changed in our RNA-seq analysis of DEX-treated 35S:AHL15-GR seedlings).

      Reviewer #2 (Public review):

      Summary:

      The manuscript by Luden et al. investigates the molecular function and DNA-binding modes of AHL15, a transcription factor with pleiotropic effects on plant development. The results contribute to our understanding of AHL15 function in development, specifically, and transcriptional regulation in plants, more broadly.

      Strengths:

      The authors developed a set of genetic tools for high-resolution profiling of AHL15 DNA binding and provided exploratory analyses of chromatin accessibility changes upon AHL15 overexpression. The generated data (CHiP-Seq, ATAC-Seq and RNA-Seq is a valuable resource for further studies. The data suggest that AHL15 does not operate as a pioneer TF, but is likely involved in gene looping.

      Weaknesses:

      While the overall message is conveyed clearly and convincingly, I see one major issue concerning motif discovery and interpretation. The authors state that because HOMER detected highly enriched motifs at frequencies below 1%, they conclude that "a true DNA binding motif would be present in a large portion of the AHL15 peaks (targets) and would be rare in other regions of the genome (background)."

      I agree that the frequency below 1% is unexpectedly low; however, this more likely reflects problems in data preprocessing or motif discovery rather than intrinsic biological properties of the transcriptional factor that possesses a DNA-binding domain and is known to bind AT_rich motifs. As it is, Figure 2 cannot serve as a main figure in the manuscript: it rather suggests that the generated CHiP-Seq peakset is dominated by noise (or motif discovery was done improperly) than that AHL15 binds nonspecifically.

      Since key methodological details on the HOMER workflow are missing in the M&M section, it is not possible to determine what went wrong. Looking at other results, i.e. the reasonably structured peak distribution around TSS/TTS and consistent overlap of the peaks between the replicas, I assume that the motif discovery step was done improperly.

      Therefore, I recommend redoing the motif analysis, for example, by restricting the search to the top-ranked peaks (e.g. TOP1000) and by using an appropriate background set (HOMER can generate good backgrounds, but it was not documented in the manuscript how the authors did it). If HOMER remains unsuccessful, the authors should consider complementary methods such as STREME or MEME, similar to the approach used for GH1-HMGA (https://pmc.ncbi.nlm.nih.gov/). If the peakset is of good quality, I would expect the analysis to identify an AT-rich motif with a frequency substantially higher than 1%-more likely in the range of at least 30%. If such a motif is detected, it should be reported clearly, ideally with positional enrichment information relative to TSS or TTS. It would also be informative to compare the recovered motif with known GH1-HMGA motifs.

      If de novo motif discovery remains inconclusive, the authors should, at a minimum, assess enrichment of known AHL binding motifs using available PWMs (e.g. from JASPAR). As it stands, the claim that "our ChIP-seq data show that AHL15 binds to AT-rich DNA throughout the Arabidopsis genome with limited sequence specificity (Figure 2A, Figure S2-S4)" is not convincingly supported.

      Another point concerns the authors' hypothesis regarding the role of AHL15 in gene looping. While I like this hypothesis and it is good to discuss it in the discussion section, the data presented are not sufficient to support the claim, stated in the abstract, that AHL15 "regulates 3D genome organization," as such a conclusion would require additional, dedicated experiments.

      The motifs discovered by HOMER are ranked by their enrichment over background, of which the highest-scoring motifs are very rare in the AHL15-bound targets, but even rarer in the background, which is why they score highly on the percent enrichment score. As expected by reviewer 2, we identified AT-rich motifs that were present in a larger percentage of AHL15 targets (found in 3-18% of targets, depending on the motif, see for example motif #5 in figure S4A), which can be seen at the right tail of the histograms shown in figures 2B-C and figures S2-S4 B-C. However, these motifs were also common in the background and were therefore not considered as significantly enriched in the AHL15-bound regions, with a target:background ratio of <2. As most of these motifs were flagged by HOMER as possible false-positives, and to limit the size of the (supplemental) figures, we did not show each of the motifs identified by HOMER in table form, but the full tables of de novo motifs identified by HOMER, including possible false-positive results are included in Additional file 3.

      Although the identification of AT-rich motifs shows that AHL15 (and very likely most other AHL proteins as well) binds AT-rich regions, it does not sufficiently explain the binding of AHL15 to its target genes, as these motifs are found at almost equal frequencies in non-AHL15-bound regions. In addition, a sequence found at this frequency in the genomic background is, in our view, too unspecific to be considered as a transcription factor binding site. Based on this, we concluded that AHL15 lacks a specific binding motif that can define the genes it binds.

      We have updated the methods section to include more details on the HOMER analysis and have also run the analysis in the top1000 shared peaks as suggested by reviewer 2 for both AHL15 and AHL29 ChIP-seq peaks, which showed that unlike in AHL29, a clear AT-rich motif cannot be found for AHL15 (Additional file 1: Figure S5).

      Reviewer #3 (Public review):

      Summary:

      This study investigated the role of AHL15 in the regulation of gene expression using AHL15 overexpression lines. Their results do show that more genes are downregulated when AHL15 is upregulated, and its binding does not affect the chromatin accessibility. Further, they investigated AHL15 binds in regions depleted in histone modifications and other epigenetic signatures. Subsequently, they investigated the presence of AHL15 in the gene chromatin loops. They found overlaps with both upregulated and downregulated genes. The methods are appropriately described, but could be improved to include the analysis of self-looping gene boundaries.

      Strengths:

      Their study clearly showed a lack of any specific sequence enrichment in the AHL15 binding sites, other than these being AT-rich, suggesting that AHL proteins do not recognize a specific DNA sequence but are recruited to their AT-rich target sites in another way. The study does suggest significant enrichment of AHL15 binding sites at TSS and TES, and AHL15 sites are depleted of any histone marks. They also identified that AHL15 binding sites overlap with self-looping gene boundaries.

      Weaknesses:

      The claim that AHL15 acts as a repressor and genes regulated by it are downregulated needs to be investigated based on AHL15 binding sites, to show enrichment/ depletion of AHL15 binding sites in overexpressing genes and repressed genes. The authors should provide data to support plant longevity with AHL15 overexpression using the DEX-induced system to support the claims in the title. Calculation of the enrichment score of AHL15 peaks in the self-looping genes that are upregulated or downregulated, and discussion about the different effects of AHL15 binding on self-looping regions to regulate gene expression may be helpful to understand the significance of the study. Motif enrichment in upregulated and downregulated genes separately to identify binding sequence preferences may be useful. It is not clear how the overlap of AHL15 peaks with self-looping genes has been carried out.

      A metagenome plot of AHL15 binding around genes that are differentially expressed upon DEX treatment can be found in Figure 3F. This analysis shows that AHL15 binding near differentially expressed genes is more pronounced compared to all AHL15-bound genes, and that AHL15 binding near the TSS is especially enriched for upregulated genes.

      As also suggested by reviewer 2, we ran a motif enrichment analysis on the differentially expressed genes that are bound by AHL15 to see if any motifs are enriched compared to the background and overrepresented in the AHL15-bound genes. Again, this did not reveal an AT-rich motif nor a motif that was conserved between up- and downregulated AHL15-bound genes (Additional file 1: Figure S6).

      Plant longevity in 35S:AHL15-GR Arabidopsis plants treated with DEX has been reported previously.. DEX treatment extended vegetative development after flowering resulting in polycarpy (Karami et al., 2020, Nature Plants), enhanced secondary growth resulting in woody stems (Rahimi et al., 2022, Current Biol.) and recently we showed that it delays leaf senescence in Arabidopsis (Luden et al., 2025, bioRxiv). All these observations have now been incorporated in the results section where the p35S::AHL15-GR plants are first presented. In addition, we show that 35S:AHL15-GR plants treated a single time with DEX at 10 days after germination show a significantly delayed flowering time in figure 4C-D of this manuscript.

      The enrichment of AHL15 ChIP-seq peaks in self-looping genes will be analyzed as suggested and compared to a random set of genes as a control, and the methods section will be updated to clarify how the analyses on self-looping genes were carried out.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      The authors need to correct Line 28 on page 10:

      By comparing the AHL15 ChIP-seq data with 1766 previously identified self-looping genes -> By comparing the AHL15 ChIP-seq data with 1792 previously identified self-looping genes (Liu et al., 2016)

      Note: 1792 genes with self-loops were first reported by Liu et al. (2016)

      Liu, C., Wang, C.M., Wang, G., Becker, C., Zaidem, M., and Weigel, D. (2016). Genome-wide analysis of chromatin packing in at single-gene resolution. Genome Res 26, 1057-1068.

      These numbers will be corrected in the text.

      Reviewer #2 (Recommendations for the authors):

      (1) The newly generated datasets have been deposited only as raw sequencing reads. For reusability and reproducibility, the authors should also provide processed data accompanied by detailed metadata.

      We will upload the processed data and corresponding metadata to GEO.

      (2) Figures 4B and 5E are of low quality; can they be improved?

      We have submitted the original high-quality images to the publisher, which should resolve the issue.

      (3) Supplementary Table 5 lacks description (columns do not have names).

      This has been fixed.

      Reviewer #3 (Recommendations for the authors):

      Suggestions:

      (1) Motif enrichment in upregulated and downregulated genes separately to identify binding sequence preferences may be useful.

      This analysis will be performed and included in the revised manuscript as Additional file 1: Figure S6.

      (2) Investigate AHL15 binding sites to show enrichment/ depletion of AHL15 binding sites in overexpressing genes than repressed genes.

      This analysis has been done, please see figure 3F.

      (3) Provide data to support plant longevity with AHL15 overexpression using the DEX-induced system to support the claims in the title.

      For the effect of AHL15-GR induction by DEX on vegetative phase change and flowering time, please see figure 4C-D and Rahimi et al., (2022, New Phytologist). For other phenotypic changes induced by DEX treatment of 35S:AHL15-GR plants, please see Karami et al. (2020; Nature Plants), Rahimi et al., (2022, Current Biology) and Luden et al., (2025; BioRxiv). Text has been added to the results section where the 35S:AHL15-GR line is first introduced to refer to these previous publications.

      (4) Calculation of the enrichment score of AHL15 peaks in the self-looping genes that are upregulated or downregulated, and discussion about the different effects of AHL15 binding on self-looping regions to regulate gene expression, may be helpful to understand the significance of the study.

      This analysis has been done and included in the revised manuscript as Additional file 1: Table S1.

      (5) Describe how the overlap of AHL15 peaks with self-looping genes has been carried out.

      The methods section has been updated with detailed information on this analysis.

    1. Author response:

      The following is the authors’ response to the original reviews.

      eLife Assessment:

      This study provides important findings on the expression of glutamate receptor (GluR) subunits across developmental stages and muscle types in Drosophila. It shows that adult muscle differs in GluR composition from larval body wall muscles, which have been the focus of most past studies. The study, while convincing, could be strengthened by acknowledging that it relies on heterogeneous methods and the absence of positive signals to infer receptor loss, which limits confidence in some of its claims. The findings illuminate how Drosophila excites muscles in diverse tissue types at different life stages, and are of interest to researchers across neuroscience.

      A note on the eLife assessment

      We are grateful for the assessment and for the reviewers' engagement. The assessment notes that the study "could be strengthened by acknowledging that it relies on heterogeneous methods and the absence of positive signals to infer receptor loss." We have taken this seriously and have addressed it in three ways in the revised manuscript:

      (i) We have replaced claims of absence with "not detected" throughout;

      (ii) We have added a paragraph describing the discrepancies between methods and the specific false-negative risks of each; and

      (ii) We have made explicit the internal positive controls that constrain our negative results, including the reciprocal GluRIIB/GluRIIC labeling within a single femur and the detection of Brp, Neto-β, and GluClα in the same flight muscle preparations in which GluRII subunits were not detected.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      The manuscript by Sustar et al. takes a methodical approach to document the types of glutamate receptor subunits that reside in Drosophila muscles, examining developmental stages spanning from larvae to adults. Prior work thoroughly documented the subunits operating in Drosophila larval body wall muscles. Most subsequent research focused on the glutamate receptor heterotetramers found in the body wall, composed of GluRIIA/C/D/E or GluRIIB/C/D/E subunits, along with auxiliary subunits like isoforms of Neto.

      For the current work, the authors report that the larval muscle glutamate receptor composition is not universal for all Drosophila muscles. They examine the following muscle systems: larval body wall, adult abdomen, adult leg coxa, and adult indirect flight. They also briefly examine adult muscle structures associated with the proboscis, neck, and haltere. The authors find that the receptor subunits in the adult abdomen (mostly) match those in the larval body wall. This makes sense given that the adult abdominal muscles are derived from the larval body wall. Yet not much else matches the larval body wall. For example, all (or most) of the GluRII-type subunits are missing from the adult indirect flight muscles. Leg muscles have GluRII-type subunits, but they do not have all of them expressed prominently, and they are missing GluRIIB. Additionally, leg muscles express a glutamate-gated chloride channel, which could be a source of inhibitory glutamatergic transmission. Interestingly, when it comes to non-abdominal adult muscles, one general theme seems to be an active promoter (GAL4 driver) for the kainate-type glutamate receptor called Clumsy. The authors propose that Clumsy could be key to understanding how functional GluR complexes are assembled in adult insects.

      Strengths:

      (1) Documenting the types of glutamate receptors that operate in diverse insect muscle systems is important because it uncovers fundamental information.

      (2) Much of the prior research focus has been on how the body wall muscle tetramers assemble and operate. It is a strength to demonstrate the other receptor solutions used by adult NMJs.

      (3) The work uses GAL4 drivers and immunohistochemistry (when possible) in combination to draw conclusions.

      (4) The muscle anatomical analyses are of high quality. This allows the research group to reach refined conclusions.

      (5) The confocal-level images of synaptic active zones and their apposed glutamate receptor clusters are of high quality.

      Weaknesses:

      (1) There is a strawman argument that is used repeatedly to highlight the significance of the work. The argument implies that the field broadly assumes (or “tacitly” assumes) that the larval body wall glutamate receptor composition extrapolates to all muscles of the fly, including the adult. This reviewer cannot find evidence that this assumption or argument has been explicitly promulgated by others. More likely, others have not examined these muscles directly, and thus, they have not speculated one way or the other.

      The reviewer is correct that we could not find a paper stating explicitly that "the adult NMJ is molecularly identical to the larval NMJ," and we have revised the text to avoid implying that such an explicit claim exists. However, we do argue that larval body-wall findings are routinely presented as properties of "the Drosophila NMJ," "the fly NMJ," or "Drosophila muscle". That unqualified generalization is what has led readers (ourselves included) to extrapolate the canonical larval architecture to the adult.

      Many concrete examples can be found in the literature. He and Dickman (2025, Curr Opin Neurobiol) state that "two subtypes of ionotropic glutamate receptors (GluRs) mediate postsynaptic currents in Drosophila muscle, GluRIIA- and GluRIIB-containing," and describe their regulation by Neto as a general feature of "the fly NMJ". The word "adult" does not appear in the review. Chou et al. (2020, Neural Development) similarly assert that "at the Drosophila NMJ, iGluRs are heterometric tetramers composed of three invariant subunits, GluRIII/GluRIIC, GluRIID, and GluRIIE, as well as one of either GluRIIA or GluRIIB". A highly cited review of these receptors is titled "Glutamate receptors at the Drosophila neuromuscular junction" (DiAntonio, 2006) yet describes only the larval body-wall system, and Harris and Littleton (2015, Genetics) introduce the larval NMJ as "a well-established model glutamatergic synapse" before discussing "the fly NMJ" throughout. Notably, we could not find a review paper about Drosophila neuromuscular control that discussed differences in receptor composition between larval and adult muscles.

      This assumption is related to the genesis of this project, which came about due to the failure of pharmacological tools used in the larva (e.g., philanthotoxin) to block synaptic transmission at adult fly muscles. We (the Tuthill Lab) contacted several principal investigators studying adult fly motor control and within the larval NMJ field (including now co-author Dion Dickman) and asked for advice about why these drugs were not effective in paralyzing leg muscles. Nobody suggested that this could be because adult muscles use different glutamate receptors than the larvae. Indeed, it was only years later when we noticed a high level of GluCl expression in the FlyCellAtlas data that we realized it could be due to differences in receptor expression.

      We agree with the reviewer that adult muscle has rarely been examined directly (Rivlin et al., 2004 being the principal exception, which we cite and now discuss at greater length). Our argument is that this gap has been filled by an untested extrapolation from larvae rather than by data. Of the ~50 papers citing Rivlin et al. (2004), we could not find any that compare glutamate‑receptor subunit expression between larval and adult muscle. Follow‑up work pursued NMJ morphology, remodeling, adhesion molecules, and transporters, leaving the receptor question open.

      Overall, we respectfully disagree with the reviewer that this argument is a strawman, because it reflects our lived experiences as active investigators of adult and larval fly motor control. However, we take the reviewer’s point. We have removed language implying that an explicit model was being overturned, and we now frame the assumption as implicit and not universally held. We note only that the assumption was operative in practice: this project began when pharmacological tools that reliably block transmission at the larval NMJ (e.g., philanthotoxin) failed to paralyze adult leg muscles, and when we consulted colleagues who work on the larval NMJ and adult fly motor control, differences in receptor composition were not among the explanations offered. We recognize this is an anecdote rather than evidence, and we have kept it out of the manuscript.

      (2) Related - to the extent that there has been any tacit assumption about GluRIIC/D/E-anchored receptors being ubiquitous among adult muscles, tacit doubt was raised by Rivilin et al., 2004 (cited by the authors but not as a source of doubt) and by RNAseq datasets like FlyAtlas from 2022 (replicated in Figures s11 and s12). To be clear, the current analysis is better than a bulk transcript analysis from adult tissues. But rather than “overturning” a field or being paradigm-shifting, the current data seem confirmatory of FlyAtlas - and confirmatory of Rivlin et al., 2004, which explicitly concluded that larval and adult NMJs were different

      Rivlin et al. did not examine GluRIIC, D and E, or most of the other glutamate receptor subunits. Nevertheless, we revised the beginning of our Discussion (pg 8) to position our work in the context of their important findings:

      In 2004, Rivlin and colleagues conducted a careful survey of NMJs in seven muscles in the adult Drosophila thorax. They established that adult NMJs are morphologically distinct from larval NMJs, and that GluRIIA and GluRIIB are expressed in muscle-specific subsets, with some muscles mysteriously lacking both. Importantly, they speculated that some adult muscles must be using different glutamate receptor subunits (which were unknown at the time) to build synapses. This problem has remained unexplored for the last two decades.

      As the reviewer requested, we have removed "overturning"/"paradigm-shifting" language throughout. But we respectfully disagree that our analysis is “confirmatory” of the Fly Cell Atlas. The Fly Cell Atlas (Li et al., 2022) does not mention glutamate receptors, or the NMJ, anywhere in its analysis. It is a general single-nucleus transcriptomic resource whose adult-muscle glutamate-receptor content was never extracted, curated, or interpreted. Extracting meaning from the dataset required posing the question, curating the relevant cells and genes, and analyzing them, which is itself a meaningful scientific contribution.

      (3) One can draw expression-level conclusions from these data. But genetic tests (e.g., would clumsy losses of function impair leg muscles?) could help the authors and the field draw stronger conclusions about the roles of some of these glutamate receptor gene products. The current dataset falls short of definitively establishing the function of alternate glutamate receptor modules.

      We intend to perform functional and behavioral experiments with clumsy loss-of-function flies. However, this work will require creation of new genetic reagents and behavioral experiments that make it beyond the scope of this manuscript. We intend to address this important topic in a future paper.

      (4) The confocal synaptic images are of high quality. They are good enough that one could analyze how well Brp directly apposes a specific glutamate receptor subunit for all the associated imaging data underlying Figures S1-S8. No such analysis is done, but understanding what components seem to directly oppose the site of release could lead to better conclusions.

      In all tissues where IIA-E are expressed at the NMJ, the protein localization is directly adjacent to Brp (see representative images in Figure 2B and s5-8). This localization is often clear in single z-slices. We attempted to perform more detailed analyses, like measure the distance between Brp and GluR puncta, but found it very challenging due to the 3D orientation of the NMJ structure. We added a sentence to page 4 of the manuscript describing what we see and the overall similarity of IIA-E localization.

      Overall Assessment and Discussion:

      The data in this study are of high quality, and the results support the main conclusion: adult muscle glutamate receptor clusters do not recapitulate the “canonical” larval body wall clusters. This is important, and the data stand on their own. That is the most important part. This reviewer does have suggestions on how to put the current work in proper context; the current draft appears to overstate the novelty of the findings. Additionally, some sentences need editing for accuracy. None of those concerns impeach the excellent foundational data.

      Reviewer #2 (Public review):

      Summary:

      This manuscript presents a broad survey of glutamate receptor composition at the neuromuscular junction in Drosophila across developmental stages and muscle types. The topic is clearly important, and the central observation-that adult muscles differ substantially from the canonical larval NMJ-is interesting and potentially impactful. The dataset is extensive and will likely be of value to the community. However, in my view, there are significant limitations in how the data are generated and interpreted, which at present reduce the strength of the conclusions.

      Strengths:

      The study addresses a relevant and timely question and provides a large and systematic dataset. The finding that adult muscles diverge from larval NMJ organization is compelling and challenges a widely held assumption in the field. The breadth of approaches, including genetic reporters, immunohistochemistry, endogenous tagging, and transcriptomic data, is, in principle, a strong aspect of the work and allows for a broad overview of receptor expression across tissues and developmental stages. Even in its current form, the manuscript provides useful descriptive information that will be of interest to the community.

      Weaknesses:

      A major concern is the reliance on a heterogeneous combination of detection methods (GAL4 reporters, antibody staining, endogenous tagging, and RNA), which are treated largely as equivalent lines of evidence. These approaches differ substantially in what they measure and in their sensitivity and specificity. While convergence across methods can in principle be convincing, here this convergence is often inferred from the shared absence of signal. This is problematic because all methods used are susceptible to false negatives for different reasons. As a result, the repeated conclusion that specific GluR subunits are “absent” from adult muscles, including those previously considered essential, is not fully justified by the data presented.

      This issue is not only theoretical. The manuscript itself seemingly contains examples where methods disagree, demonstrating that detection is incomplete and method-dependent. These discrepancies could be better integrated into the interpretation. Instead, negative results across methods are often taken as strong evidence for absence, which overstates the certainty of the findings.

      In addition, antibody validation appears to rely largely on prior work in larval tissue. Given the structural and biochemical differences in adult muscles, it is not clear that staining performance is equivalent, particularly in cases where the signal is weak or undetected. This further complicates the interpretation of negative results.

      More generally, the manuscript moves in several places from descriptive observations to functional or mechanistic implications that are not directly supported. The suggestion that adult muscles operate with fundamentally different receptor assemblies is intriguing, but remains speculative without functional validation. At a minimum, the distinction between observation and interpretation should be made more explicit.

      I thus think that the current conclusions need to be more carefully constrained. Ideally, the study would be strengthened by at least one functional experiment, such as electrophysiological recordings from adult NMJs or perturbation of candidate receptors like GluClα or Clumsy. This would help to anchor the expression data in synaptic function.

      We thank the reviewer for a careful and constructive critique. We agree that inference from the absence of signal requires caution, and we have revised both the wording and the framing of the manuscript substantially in response. We would also like to draw attention to a feature of our dataset that we did not previously make explicit, and which we believe speaks directly to the core concern: a number of our negative results are internally controlled by positive signal from the same reagent, in the same tissue, in the same preparation.

      (i) In the adult femur, anti-GluRIIB labels NMJs on tibia extensor fibers but not on accessory tibia flexor fibers within the same bisected femur, processed, stained, and imaged together (Figure 3C-D).

      (ii) Anti-GluRIIC shows the reciprocal pattern in the same preparations (Figure 3E-F). The failure to detect GluRIIC in the tibia extensor therefore cannot be attributed to a general failure of that antibody in adult tissue, to fixation, or to reagent penetration, because the same antibody labels NMJs tens of microns away in the same section.

      (iii) In indirect flight muscle, where we detected none of the five GluRII subunits, we reliably detected Brp, Neto-β::sfGFP, and GluClα:V5 at and around NMJs in the same preparations (Figures 2B, 2D, 4C). Reagent access, epitope preservation, and NMJ identification are therefore all demonstrated in the same tissue where our negative results are strongest.

      These controls do not exclude the possibility that receptors are present below our detection threshold, and we have accordingly replaced "absent" with "not detected" throughout the manuscript. They do, however, argue that the muscle-specific differences we report reflect genuine biological variation rather than method failure. We have added a paragraph to the Discussion making this argument explicitly, alongside a new paragraph describing the discrepancies between methods, and we have added a description of antibody validation to the Methods.

      In summary, this is an interesting and potentially important study, but the current manuscript somewhat overinterprets heterogeneous and partly indirect evidence. It will already be useful in its present form, but could be more convincing if the authors more rigorously account for methodological limitations and moderate their claims accordingly.

      Reviewer #3 (Public review):

      The Sustar et al. manuscript catalogs glutamate receptor composition across distinct Drosophila NMJs: larval and adult abdominal NMJs, as well as NMJs on adult leg and flight muscles. This work is important and probably overdue. The larval NMJ is the exemplar NMJ in this system, and the identity of “essential” and “alternative” subunits at this stage is assumed by many to hold across developmental stages and NMJ types. Here, the authors show that there is surprising diversification among NMJ types and that the notion of essential/alternative subunits only holds true at larval NMJs.

      The study will generate interest in the Clumsy GluR subunit, which has not been well-characterized at all, but is widely expressed at adult NMJs. They also find striking extrasynaptic expression of glutamate-gated chloride channel GluRClalpha in adult leg and flight muscles, raising questions about its role. The study is interesting, logical, and well-written. The figures are clear, and the discussion was particularly thoughtful. I have a couple of comments that the authors could consider.

      (1) They cite Rivlin et al., (2004) in the Introduction as the sole previous study to investigate the molecular composition of adult NMJs, but do not mention this work again. In the Discussion, it would be helpful to compare/contrast their finding with those of the earlier work.

      Thank you for the suggestion. We have revised the beginning of our Discussion (pg. 8) to position our work in the context of Rivlin et al.’s important findings.

      (2) Were these analyses done in adults of consistent ages? It seems possible that the GluR subunit composition could be different in very young adults or in aged flies. The age of the animals should be mentioned in the Methods.

      Thank you for noticing this gap. We added age of flies to the Methods section, including the important detail that in cases where we failed to detect any GAL4 signal (e.g., GluRIID-GAL4), we additionally imaged very young and very old flies (0-2 hours old and 20-day-old). It did not change the results.

      (3) The broad expression of GluCl:V5 in adult leg and flight muscles is surprisingly robust and appears to light up the edges of all muscle fibers. Would the authors comment on the controls that were done to ensure that this staining is real and specific to animals carrying that V5 endogenous tag?

      We added a sentence to the results section (pg 8) to highlight the V5 negative staining controls that are shown in Figure s15.

      (4) The snRNAseq data in Figure S12 differ a bit from the IHC/GAL4 data summarized in the table in Figure 2. In particular, the data suggests that Ukar and Grik are widely expressed in adult muscles. Is there a reason not to include an “snRNA seq” column in Figure 2 alongside the data from GAL4 lines and IHC? To my mind, it is about as reliable as GAL4 lines that often capture only a subset of the full expression pattern. In this case, the snRNAseq data suggest that Ukar/Grik are likely at adult flight muscle NMJs, which might be important since NMJ was negative for everything except Neto-beta by IHC.

      We liked your suggestion to put these data together in one figure, and we tried to incorporate this during our revisions. However, because of the difficulty of combining multiple types of data into one table, we ultimately decided to keep them separate to avoid any confusion. The GAL4 analysis is qualitative (no expression, weak expression, strong expression) in percent of muscles. The RNA-seq data is quantitative and measured in fraction of muscle cells. Figure s13 now shows RNA-seq results in a table format that is parallel to the table with GAL4 results in Figure 2.

      We also added a paragraph to the end of the discussion to mull several discrepancies in results (e.g. Grik and Ukar) when using different methods.

      We did observe some discrepancies across the different experimental approaches. For GAL4 reporter lines, we used T2A gene trap lines where possible (for 15 of the 16 GluR genes) to determine receptor expression. However, some of these reporters were extremely weak and may have resulted in false negatives. For example, we did not detect Grik-GAL4 or Ukar-GAL4 expression in any tissue (Figure 2C), despite RNA-seq evidence that these are expressed robustly in adult muscles (Figures s11, s12). We do not have antibodies or protein reporters for these genes to help resolve this. Another discrepancy was with GluRIIE. In this case, antibody staining and RNA-seq did not detect GluRIIE in flight muscles (Figures s8, s11), while the GAL4>GFP reporter showed extremely faint signal in the flight muscles. Because of the marginal signal and the discrepancy with the other methods, we believe this could likely be a false positive. The table in Figure 2 does not effectively capture the nuance of this otherwise confusing result. Overall, however, we found that results from different approaches generally agreed and revealed intriguing differences between different muscle types.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      Most of these recommendations are for text edits. Where experiments are noted (#8 and #9 below), they could be helpful, but they are not essential because the study has value as is.

      (1) It would be appropriate to scrub the entire manuscript of statements that say that the work is overturning an incorrect model about larval GluRII receptor tetramers working the same way in adult muscles. First, it is not necessary. But more importantly, by this reviewer’s reading, there is not an explicit model promoted by others that the larval body wall findings extrapolate to other muscles. The better way to frame the work is to state that it clearly shows the field has a lot of work to do to properly characterize glutamate receptor composition and function in Drosophila adults. Places in the text that the authors should edit include:

      - “...challenging assumptions about the uniformity of neuromuscular function” (Abstract)

      We deleted this clause.

      - “...it is often tacitly assumed...This extrapolation overlooks...during metamorphosis.” (Introduction)

      New wording: … “…it has commonly been assumed…” (Abstract) and “…we and others assumed…” (Intro)

      - “(With one notable exception, Rivlin et al., 2004)” (Introduction). This reference deserves more than an obscure parenthetical because it explicitly concluded that larval and adult NMJs differ.

      As described above, we revised the beginning of our Discussion (pg 8) to position our work in the context of Rivlin et al.’s important findings.

      In 2004, Rivlin and colleagues conducted a careful survey of NMJs in seven muscles in the adult Drosophila thorax. They established that adult NMJs are morphologically distinct from larval NMJs, and that GluRIIA and GluRIIB are expressed in muscle-specific subsets, with some muscles mysteriously lacking both. Importantly, they speculated that some adult muscles must be using different glutamate receptor subunits (which were unknown at the time) to build synapses. This problem has remained unexplored for the last two decades.

      - “Collectively, these results overturn the assumption of NMJ uniformity...” (Introduction)

      New wording: Collectively, these results reveal a diversity in NMJ composition”

      - “Our findings challenge the assumption...” (Conclusions)

      We deleted this clause.

      (2) (Related) The authors quibble in a couple of places that the GluRIIC/D/E subunits have been “previously considered essential for viability and NMJ function.” This reviewer’s understanding of those subunits has always been that they are essential for life, and indeed, they are essential because null mutants arrest as embryos. The places where the text seems to combine viability and NMJ function (including the Abstract) as incorrectly assigned roles for these subunits, should be more carefully edited. This reviewer agrees with the “NMJ function” conclusion since the authors are considering so many NMJs. Viability still holds.

      We agree with the reviewer, and we thank them for catching an imprecision that recurred throughout the manuscript. GluRIIC, GluRIID, and GluRIIE are essential for viability, and nothing in our data contradicts that conclusion.

      We think the point we were trying to make is narrower and sharper when stated precisely. Null mutants for these subunits arrest as embryos — that is, they die before the adult leg and flight muscles are formed. Those experiments therefore established a requirement for viability and for larval NMJ function, but they could not, in principle, have tested whether the same subunits are required at NMJs that arise only during pupal development. Our data do not revise the viability conclusion. They show that the subunit requirement established at the larval body-wall NMJ does not generalize to every NMJ in the animal.

      We have decoupled "viability" from "NMJ function" throughout the manuscript (Abstract, Introduction, Discussion) and have added a sentence to the Discussion making the developmental logic explicit:

      Importantly, because these mutants die before metamorphosis, these experiments established a requirement for viability and for larval NMJ function, but could not test whether the same subunits are required at adult NMJs, which are formed during pupal development.

      (3) “...the physiology and molecular architecture of adult fly NMJs remain largely unexplored...” The authors cite the Rivilin paper that examined the prothorax. But physiology has certainly been examined at DLMs as well as proboscis NMJs.

      As the manuscript says on page 2, the topic is largely unexplored compared to the larva. The Rivlin paper is an excellent contribution but was conducted over 20 years ago with more limited genetic reagents. There were also no follow-up studies. In the same amount of time, over 1000 papers have been published regarding the Drosophila larval NMJ.

      The reviewer is correct that physiology has been performed in adult DLMs and proboscis muscles. These studies, however, have focused on other biological questions and did not investigate the makeup of the NMJ or manipulate glutamate receptors with pharmacology or genetic tools. Our study reveals the need for such experiments.

      (4) “Surprisingly, we found that none of the primary GluRII subunits was strongly expressed in adult indirect flight muscles...” This sentence was difficult to parse when simultaneously examining the large dot for GluRIIE-Gal4 in the IFMs (Figure 2C), until the realization that the blank IHC result was driving the conclusion (no expression). The authors may want to delineate Gal4 vs. IHC for each dataset to avoid confusion for readers.

      We agree with the reviewer that this result is confusing. GluRIIE-GAL4 expression was a case in which a dot in the table didn’t capture the subtlety of the result. The GluRIIE-GAL4 was expressed very faintly in the IFM, to a degree that we almost called it negative.

      We added a paragraph to the Discussion in which we reflect on some data discrepancies:

      We did observe some discrepancies across the different experimental approaches. For GAL4 reporter lines, we used T2A gene trap lines where possible (for 15 of the 16 GluR genes) to determine receptor expression. However, some of these reporters were extremely weak and may have resulted in false negatives. For example, we did not detect Grik-GAL4 or Ukar-GAL4 expression in any tissue (Figure 2C), despite RNA-seq evidence that these are expressed robustly in adult muscles (Figures s11, s12). We do not have antibodies or protein reporters for these genes to help resolve this. Another discrepancy was with GluRIIE. In this case, antibody staining and RNA-seq did not detect GluRIIE in flight muscles (Figures s8, s11), while the GAL4>GFP reporter showed extremely faint signal in the flight muscles. Because of the marginal signal and the discrepancy with the other methods, we believe this could likely be a false positive. The table in Figure 2 does not effectively capture the nuance of this otherwise confusing result. Overall, however, we found that results from different approaches generally agreed and revealed intriguing differences between different muscle types.

      (5) “GluClalpha in adult muscles establishes the molecular identity of inhibitory glutamate responses described decades ago in other insects...” This reviewer really likes this idea. But the current data fall far short of the conclusion in this sentence.

      You are correct. We tempered this statement to “The identification of extrasynaptic GluClα in adult muscles establishes a possible mechanism for inhibitory glutamate responses described decades ago […]”

      (6) “One past study (Han et al., 2015) explored many combinations....” Nothing in this sentence is untrue. This reviewer just wanted to point out that one interesting observation from the Han paper was that an A/E combination alone yielded significant function in the heterologous system. To the extent that A and B have been described as competitive for the same C/D/E core, it is not a stretch to imagine that a B/E combination would have significant function, just like A/E. Or B/D/E as well.

      We thank the reviewer for this observation, which we think materially strengthens the plausibility of our interpretation, and we have incorporated it into the Discussion. Han et al. (2015) found that GluRIIA and GluRIIE together were sufficient to reconstitute functional receptors in a heterologous system, without GluRIIC or GluRIID. Because GluRIIA and GluRIIB are thought to compete for the same position within the tetramer, there is no obvious reason a GluRIIB/IIE or GluRIIB/IID/IIE complex should not also be functional. This provides a concrete precedent for exactly the kind of non-canonical combinations our expression data imply — for example, GluRIIB in the absence of detectable GluRIIC in tibia extensor fibers. We have added the following to the Discussion (p. 9):

      Notably, Han et al. (2015) found that GluRIIA and GluRIIE alone were sufficient to reconstitute functional receptors, without GluRIIC or GluRIID. Because GluRIIA and GluRIIB are thought to occupy the same position within the tetramer, this raises the possibility that GluRIIB-containing complexes lacking GluRIIC — such as the GluRIIB/IID/IIE combination implied by our data in the tibia extensor — could likewise be functional. Neto-β, which is required for receptor gating and synaptic clustering (Han et al., 2024; Kim et al., 2012), is expressed at all adult NMJs we examined (Figures 2D, 3B), so the auxiliary subunit requirement for such complexes would be satisfied. Direct tests of these subunit combinations by heterologous reconstitution are an important next step.

      (7) GluClalpha roles: The idea of a negative feedback controller is a good one. An alternative idea can be gleaned from the NMJ anatomy of circuits like the Mauthner Cell Escape Circuit in zebrafish. In that circuit, the fish have excitatory connections on some muscles and simultaneous control of inhibitory connections wired for other muscles to enable fast changes of direction.

      We thank the reviewer for this interesting comparison. We think the Mauthner arrangement is unlikely to apply here, for two reasons. First, GluClα appears to be expressed broadly across the leg and flight muscles we examined, rather than in a subset complementary to the excitatory receptors. Second, and more importantly, GluClα is extrasynaptic: it is distributed along the periphery of the muscle fiber and is not apposed to Brp-positive active zones (Figure 4C-D). Target-specific inhibitory transmission of the kind used in the Mauthner circuit requires inhibitory receptors positioned at synapses, whereas the localization we observe is better suited to tonic or slowly varying modulation of muscle excitability. We have added a sentence to the Discussion making this distinction, since the reviewer's question is one that readers will also have. And add to the manuscript, at the end of the GluClα hypothesis paragraph in the Discussion:

      We note that this arrangement differs from circuits in which excitatory and inhibitory transmission are targeted to different muscles to produce rapid directional control, as in the Mauthner cell escape circuit of larval zebrafish. While most arthropods possess GABAergic motor neurons that directly inhibit leg muscles, holometabolous insects such as Drosophila do not (Witten and Truman, 1998). And because GluClα is extrasynaptic rather than apposed to active zones, it is unlikely to support fast, target-specific inhibitory transmission.

      Two optional experimental suggestions:

      (8) The authors’ findings with Clumsy expression along with Clumsy message expression in the FlyAtlas RNAseq datasets - and finally, the unpublished work on Clumsy - all collectively suggest that it is a great target for adult knockdown. It is not required, but the authors’ conclusions would be bolstered if they were to test RNAi against Clumsy in chosen adult NMJs and check behavior (e.g., walking?) for defects.

      We intend to perform functional and behavioral experiments with clumsy loss-of-function flies. However, this work will require creation of new genetic reagents and behavioral experiments that make it beyond the scope of this manuscript. We intend to address this in a future paper.

      (9) The confocal synaptic images are of high quality. They are good enough that one could analyze how well Brp directly apposes a specific glutamate receptor subunit for all the associated imaging data underlying Figures S1-S8. No such analysis is done, but understanding what components seem to directly oppose the site of release could lead to better conclusions.

      In all tissues where IIA-E are expressed at the NMJ, the protein localization is directly adjacent to Brp (see representative images in Figure 2B and s5-8). This localization is often clear in single z-slices. We attempted to perform more detailed analyses, like measure the distance between Brp and GluR puncta, but found it very challenging due to the 3D orientation of the NMJ structure. We added a sentence to page 4 of the manuscript describing what we see and the overall similarity of IIA-E localization.

      Reviewer #2 (Recommendations for the authors):

      The authors should revise the wording throughout to more clearly distinguish between “absence” and “not detected,” in particular for statements regarding GluRII subunits in adult muscles. In the current form, some claims appear stronger than supported by the methods.

      Thank you for this important suggestion. We replaced “absence” with “not detected” throughout the manuscript. We also note this distinction explicitly in the Discussion.

      It would also improve clarity if the different experimental approaches (GAL4, antibody staining, tagging, RNA-seq) were presented more explicitly separated, rather than combined into a single readout. This would allow a better assessment of the evidence.

      We have kept the Results organized by finding rather than by technique, because the majority of our results were concordant across approaches and a technique-by-technique presentation would fragment each biological conclusion across four sections. However, we agree that the evidence should be separable by the reader, and it now is: Figure 2C reports GAL4 and IHC in separate columns, Figure s13 presents the RNA-seq results in a parallel table format, and the new Discussion paragraph identifies each case in which the methods disagreed and states which result we consider likely to be a false positive or false negative. Where a single method underlies a conclusion, we now say so in the text.

      The discrepancies between methods (e.g., RNA-seq vs GAL4 expression) should be discussed more directly, and the possibility of false negatives, especially for antibody staining in adult tissue, should be acknowledged more clearly.

      Thank you. Other reviewers also noticed this weakness of our manuscript, and as noted above, we added a paragraph in the discussion to highlight several important discrepancies in methods and possibilities of false positives.

      A functional experiment is not strictly required, but would clearly strengthen the manuscript. For example, electrophysiology at adult NMJs or perturbation of candidate receptors (e.g., GluClα or Clumsy) would help to link expression to function.

      We intend to perform functional and behavioral experiments with clumsy loss-of-function flies. However, this work will require creation of new genetic reagents and behavioral experiments that make it beyond the scope of this manuscript. These experiments and the accompanying behavioral analysis will form a separate study, which will be the foundation of a future paper.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      (1) The authors mentioned the development of single-chain variable fragment (scFv) recombinant antibodies raised by the SGC against the six proteins (ANXA11, OPTN, MATR3, PFN1, UBQLN2 and VCP) that had limited renewable antibodies that are commercially available. The development was optimized to generate antibodies particularly suitable for IP, and the clone selection process was carried out using IP coupled to mass spectrometry. Even though the generation of these novel reagents is not the focus of this work, the authors do not provide any data on this aspect.

      The scFv reagents represent an important component of this resource and warranted additional description. In the revised manuscript, we expanded the section describing their origin, selection strategy, and intended use. We also added an updated reference describing the scFv discovery methodology, together with a brief summary of the workflow. In addition, the sequences of all six scFvs (ANXA11, OPTN, MATR3, PFN1, UBQLN2, and VCP) are now provided in Supplementary Table 2. During the revision process, we also identified that two scFv plasmids were missing from Add gene; these have now been deposited, making all six reagents and their sequences publicly available.

      (2) The protein profiling study is limited to WB data, and the authors did not provide any explanation on why there was no integration with IP and IF data, not even for those targets that have validated antibodies. Also, not all the cell types have been screened by chemiluminescence-based detection and by fluorescence-based WB, and the authors do not elaborate on the reason for such a choice.

      ALS-RAP was conceived as an open science resource for the ALS community. Given the breadth of the project (33 ALS-associated proteins), it is unrealistic for a single laboratory to investigate the biochemical and cellular biology of every target. We therefore generated and openly disseminated antibody characterization data across three complementary applications—western blot (WB), immunoprecipitation (IP), and immunofluorescence (IF)—to provide the community with validated tools that can support diverse downstream studies, including protein abundance, protein interactions, and subcellular localization.

      The primary objective of the protein profiling study presented in this manuscript, however, was to compare relative protein abundance across multiple neuronal and glial cell types. Western blotting was selected because it provides a robust and semi-quantitative measurement of protein abundance across biological samples, making it well suited for systematic comparisons between cell types. In contrast, IP and IF were primarily included as antibody validation assays and as community resources for future mechanistic studies rather than for quantitative expression profiling.

      Generating the large quantities of iPSC-derived neuronal and glial cells required to profile 33 ALS-associated proteins is technically demanding and resource-intensive. Consequently, a limited number of protein-cell type combinations are absent from one of the two detection modalities because insufficient lysate remained for repeat analyses. Importantly, every protein was evaluated across the complete panel of neurological cell types in at least one western blot detection modality. In most cases, the omitted samples corresponded to cell types in which the target protein was undetectable or expressed at very low levels in the initial experiment.

      Reviewer #2 (Public review):

      (1) The rationale for the selection of these 33 genes is insufficient. The authors lean on the Nijs & VanDamme classification and on PubMed entry counts, but the number of PubMed entries is not a meaningful criterion for what constitutes an important ALS protein - some of the most disease-relevant genes are precisely those with fewer publications, while heavily cited genes such as CAV1 carry weak ALS-specific evidence. The authors should provide a more transparent and biologically motivated rationale for inclusion and exclusion (ClinGen evidence tier, replicated GWAS signals, large meta-analyses, ALSoD) and explain why specific risk genes outside this list were not part of ALS-RAP.

      We thank the reviewer for this comment and apologize if our rationale for target selection was not sufficiently clear. We agree that the number of PubMed entries should not be interpreted as a criterion for inclusion. Rather, we included this metric as a descriptive measure of how extensively each gene has been studied in the context of ALS. Specifically, comparing the number of publications for Gene versus Gene + ALS provides an indication of the relative attention a target has received within the ALS field, but it was not used to prioritize genes for inclusion.

      The selection of the 33 ALS-RAP targets was instead based on established genetic evidence for disease association. Specifically, we prioritized ALS-associated genes supported by replicated human genetic studies, including rare variants with high, intermediate, or modest effect sizes, following the classification framework proposed by Nijs and Van Damme. As described in the manuscript, 25 of the 33 targets have also been independently curated by the Clinical Genome Resource (ClinGen) ALS Gene Curation Expert Panel and classified as having evidence supporting an association with ALS (Table 1). The remaining genes were selected based on published human genetic studies and emerging evidence supporting their relevance to ALS biology.

      (2) "107 of 231 (46%) demonstrated specific target staining in IF." The criteria used to define "specific target staining" at the IF level are not stated. From the Galectin-1 example, the mosaic WT/KO strategy provides a binary readout, but for proteins with low expression, weak punctate staining or unusual subcellular distributions, a single threshold is unlikely to capture specificity uniformly across 231 antibodies.

      We thank the reviewer for highlighting this omission. We agree that the criteria used to classify antibodies in each application should be explicitly stated. In the revised manuscript, we now define the classification criteria for Western blot (WB), immunoprecipitation (IP), and immunofluorescence (IF) in the Methods section. Briefly, WB antibodies were considered target-selective when the predominant immunoreactive band at the expected molecular weight was substantially reduced or absent in the corresponding knockout (KO) lysate. IP antibodies were considered successful when they specifically enriched the target protein from wild-type lysates, as assessed by immunoblotting of the immunoprecipitated material. For IF, antibodies were considered specific when the mean fluorescence intensity in wild-type cells was at least 1.5-fold higher than that measured in KO cells using the mosaic WT/KO assay. A minimum of 250 WT and 250 KO cells were quantified for each antibody. These criteria were applied uniformly across all antibodies to provide a standardized and objective benchmarking framework. We have also added references to the detailed YCharOS characterization workflows previously described in Ayoubi et al., Nature Protocols (2025).

      (3) Several claims in the manuscript depend on differential protein abundance across cell types. As presented, these claims are supported by qualitative Western blot images only. They should be substantiated by quantification across multiple biological replicates.

      The expression patterns observed were reproducible across two independent batches of iPSC-derived neuronal and glial cell types generated using the same differentiation protocols. In addition, several proteins enriched in iPSC-derived microglia also showed enrichment in primary human microglia and monocyte-derived macrophages, providing independent support for these observations.

      We agree that quantification across multiple biological replicates would be required to establish definitive differences in protein abundance between neuronal and glial cell types. However, this was not the objective of the present study. Rather, our goal was to perform an initial survey of ALS-associated protein expression using rigorously validated antibodies and to identify expression patterns that may warrant further investigation.

      ALS-RAP was conceived as an open science resource for the ALS community. Given the breadth of the project (33 ALS-associated proteins), we do not envision that a single laboratory can comprehensively define the expression, localization, and function of every target across all relevant cell types, tissues, and disease states. Instead, we provide validated reagents together with an initial characterization of protein expression in well-defined iPSC-derived neuronal and glial cell models to enable and accelerate future studies by the broader research community.

      (4) This manuscript represents a unique opportunity to address antibody recognition of splicing variants, which is something of considerable value to the community. For each target, the predicted isoforms in Ensembl could be cross-referenced against the observed bands, and the pattern of bands compared across cell types could be informative about which isoforms each antibody captures. This would convert ambiguous "extra bands" into useful biological information and would substantially increase the value of the resource. I strongly encourage the authors to include this analysis.

      We agree that defining which protein isoforms are recognized by individual antibodies would be valuable to the research community. However, we believe that such an analysis would be difficult to interpret and potentially misleading based on the data generated in the present study.

      All antibodies were initially characterized in a common cancer cell line, and the best-performing reagents were subsequently used to profile ALS-associated proteins in iPSC-derived neuronal and glial cell types. Additional bands observed in neurological cells, but not in the original characterization cell line, may reflect several nonmutually exclusive possibilities, including cross-reactivity with proteins specifically expressed in neurological cells, recognition of cell type-specific splice isoforms, or post-translationally modified forms of the target protein.

      Without knockout validation in each neurological cell type, these possibilities cannot be distinguished confidently.

      In addition, protein migration on SDS-PAGE frequently differs from the theoretical molecular weight predicted from amino acid sequence alone. Consequently, assigning individual immunoreactive bands to Ensembl-predicted isoforms based solely on apparent molecular weight would be speculative and could lead to incorrect conclusions. We therefore believe that a rigorous isoform analysis would require complementary experimental approaches beyond the scope of the present resource study.

      (5) The iPSC-derived microglia receive a comprehensive QC panel (IBA1/PU.1 IF, CD45/CD11b flow, qRT-PCR for nine canonical markers; Figure S4), which allows the reader to assess culture purity. The other iPSC-derived lineages - motor neurons, dopaminergic neurons, oligodendrocytes and astrocytes- are validated by a single marker each in WB (Figure S3) without purity quantification. Given that several conclusions of the manuscript rest on the cell-type-specific detection of ALS-associated proteins, equivalent quality control should be performed for the other lineages so that the reader can evaluate the purity of each preparation.

      We thank the reviewer for this important comment and agree that documenting the identity of iPSC-derived cell populations is essential given their inherent heterogeneity. The differentiation protocols used in this study follow well-established, published methods that have been extensively validated by their developers and the broader stem cell community. We confirmed the identity of each differentiated lineage using established lineage-specific markers, including ISL1 for motor neurons, TH for dopaminergic neurons, SATB2 and CTIP2 for cortical neurons, MBP for oligodendrocytes, GFAP and CD44 for astrocytes, and CD11b and Iba1 for microglia.

      We agree that comprehensive quantitative purity analyses for every differentiated lineage would further strengthen the study. However, we believe that these experiments fall beyond the scope of the present work, whose primary objective was to establish a validated antibody resource rather than to optimize or benchmark differentiation protocols. We also note that our conclusions are intentionally limited to broad protein expression patterns rather than definitive quantitative comparisons between cell types.

      Finally, the inclusion of primary human microglia, fetal astrocytes, and monocyte-derived macrophages provides an independent layer of biological validation. The concordance of expression patterns observed between these primary cells and the corresponding iPSC-derived populations supports the robustness of our principal observations.

      (6) The robustness of the resource would be substantially increased by validating at least a subset of the targets in a second iPSC background, in at least some of the cell types analysed.

      We agree that validating antibody performance and protein expression across multiple iPSC genetic backgrounds would further strengthen the resource. However, we believe that this objective falls beyond the scope of the present study, whose primary aim was to establish a rigorously validated antibody toolbox for ALS-associated proteins and to provide an initial survey of their expression in representative neuronal and glial cell types.

      We envision ALS-RAP as the foundation of a broader community effort. Rather than comprehensively evaluating all 33 proteins across multiple genetic backgrounds and tissues, our goal is to provide validated, renewable reagents that will enable such studies by the broader ALS research community.

      (7) The newly developed SGC scFv antibodies are arguably the most novel reagent contribution of this manuscript, yet they receive a single sentence in the body of the paper. A more thorough description is warranted.

      We agree that the scFv reagents represent an important component of this resource and warranted additional description. In the revised manuscript, we expanded the section describing their origin, selection strategy, and intended use. We also added an updated reference describing the scFv discovery methodology, together with a brief summary of the workflow. In addition, the sequences of all six scFvs (ANXA11, OPTN, MATR3, PFN1, UBQLN2, and VCP) are now provided in Supplementary Table 2. During the revision process, we also identified that two scFv plasmids were missing from Addgene; these have now been deposited, making all six reagents and their sequences publicly available.

      (8) Accessibility of the resource through Zenodo is not straightforward - the reader currently has to navigate to individual antibody characterization reports one by one to extract recommendations for a given target. While the use of an established public repository is important for permanence, a dedicated ALS-RAP website with an interactive, searchable interface - filterable by target, application, host species and clonality - would meaningfully improve uptake. The relationship between such a portal and the existing OGA platform should also be clarified.

      We agree that navigating individual antibody characterization reports on Zenodo can be cumbersome for end users. This challenge was one of the motivations behind the development of the Only Good Antibodies (OGA) platform, which curates YCharOS antibody characterization data, including the ALS-RAP dataset, into an interactive and searchable interface. OGA allows users to identify antibodies by target, application, host species, clonality, and other relevant attributes, while providing direct links to the complete characterization reports archived on Zenodo. In this way, Zenodo serves as the permanent open repository for the complete datasets, whereas OGA provides a user-friendly interface for data exploration and antibody selection.

    1. Author response:

      The following is the authors’ response to the previous reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      This is a study utilizing several types of analyses (computational modeling, neuronal cultures, rodent epilepsy model, and human intracranial multi-scale recordings) to address a highly relevant conceptual question: Are fast ripples (FRs) distinct pathological entities or largely emergent products of stochastic spike clustering? The results can potentially reshape current approaches to incorporating fast ripples into the epilepsy surgery evaluation.

      Strengths:

      The conceptualization of fast ripples as potentially arising by chance is highly novel and builds effectively on questions raised in prior studies that have never been satisfactorily resolved. Integration across biological scales and models provides a rigorous approach, now improved by addressing theoretical concerns regarding validity of the shuffling approach and state dependence. The discussion has been updated to provide a more nuanced interpretation of the study's findings.

      Weaknesses:

      The authors have satisfactorily and thoughtfully addressed the critiques provided in the first review. However, there remain two points that I would like authors to address:

      (1) Synchronized burst firing is a key feature of an epileptic site generating interictal discharges, and one that could generate either oscillatory or stochastic FRs as documented in multiple prior publications cited in the manuscript and/or in the prior review. Paroxysmal depolarization, for example, has been very well described, and consists of strong, disorganized burst firing (resulting in summated postsynaptic potentials strong enough to generate high gamma signal) in a neuronal population coinciding with a large low-frequency deflection. I would like to see the results described in this context, and to avoid blanket dismissal of stochastic FRs without a clear oscillatory component.

      To describe the results in this context, we have updated the Discussion. It reads:

      “Depolarizations that promote burst firing should also increase the likelihood of FRs. Paroxysmal depolarization shifts, which are the cellular events underlying epileptiform abnormalities, would therefore be expected to co-occur with FRs. Accordingly, epileptiform abnormalities should be associated with increased gamma/high-gamma (> 80 Hz) activity at their source as has been observed in epileptogenic parenchyma (Ren et al., 2015; Sheybani et al., 2021; Weiss et al., 2015).”

      (2) It would be highly useful to add a conclusion paragraph that spells out implications of the study for use of FRs as epileptic biomarkers in clinical invasive EEG recordings.

      We fully agree that the main message should be further clarified. We have added this paragraph to this end:

      “Clinically, our findings do not argue for or against the use of FRs as epilepsy biomarkers, as we did not assess their relationship with the epileptogenic zone. However, they do indicate that FRs are not highly specific to epileptic tissue. We would, however, recommend selecting FRs with particularly long duration, which may offer greater specificity and potentially better reliability as a biomarker. The clinical value of FRs as distinct entities or as emergent oscillations remains to be clarified.”

      Please address the above critiques in Discussion, or elsewhere as deemed necessary by the authors.

      Reviewer #2 (Public review):

      Summary:

      This paper asks an important question that has not been discussed much in the extensive literature on the High Frequency Oscillations (HFOs) that have been extensively studied in patients with epilepsy and experimental models of epilepsy. The question is whether the Fast Ripples (FRs), the HFOs in the 250-500 Hz frequency band, represent a pathological phenomenon or represent a physiological phenomenon that occurs in the healthy brain but happens to be more frequent in epileptic tissue. It is an important question that has not been systematically addressed until now. The authors conclude, from very extensive simulations, from extensive experimental animal studies (the systemic kianate model of epilepsy in rats), and from a modest amount of human data, that FRs occur in healthy brains as a result of the chance occurrence of bursts of action potentials, and that in epileptic tissue, their frequency of occurrence is approximately 30% higher than what is expected by chance. They conclude that FRs are not a separate phenomenon of epileptic tissue. This finding is reinforced by the recent findings of FRs in experimental models of Alzheimer's disease.

      Strengths:

      This is a valuable study because it asks an important and original question and because it evaluates it from several angles (simulation, tissue culture, experimental animals, and human patients). The simulations and the analyses of real data are performed very carefully and with original and solidly documented approaches, using extensive simulations and extensive data sets in the cultured cell data and in the in vivo experiments. The paper is clearly written and well-illustrated.

      Comments on revised version.

      The authors have appropriately addressed the questions I raised in the first review.

      Reviewer #3 (Public review):

      Summary:

      An outstanding question in the field of high-frequency oscillations (HFOs) in the context of epilepsy is how these oscillations emerge, considering that they occur at such high frequencies i.e., 250Hz well above the firing ability of single neurons. One hypothesis that has been suggested in the past is that neurons that fire in an out-of-phase fashion or rather at random intervals may contribute to a spectrum of HFOs ranging from 250-500Hz that observed in epilepsy. However, how possible it is that random action potentials could aggregate to the extent that they could give rise to HFOs in the so-called fast ripple (FRs) frequency range (>200 according to the authors) remains unclear. To test this hypothesis, they used computational modeling to randomly insert action potentials in a signal, and they found that this approach is sufficient to generate FRs. Some of the predictors of whether FRs could occur were neuronal count, firing rate and synchronization. Besides computational modeling, they used different model systems to test whether that would be possible to be observed in neuronal cultures, in epileptic rats (intrahippocampal kainic acid model), and human data. Neuronal cultures treated with picrotoxin did not show evidence that FRs could be generated more than chance aggregation of action potentials. They then asked whether synchronization and firing rate could play a role in the emergence of FRs. They found that changes in neural firing and synchronization, such as those occurring during different phases of the sleep-wake cycle could affect the number of FRs occurring by chance aggregation, with more FRs seen during periods of wakefulness, a result that they replicated in human data.

      The authors largely achieve their proposed aims of demonstrating that random neuronal firing can, in principle, generate FRs. Results from this study could influence current thinking around mechanisms generating FRs in epilepsy. The use of different computational approaches and model systems could offer new analytical methodologies for the study of FRs in the context of brain disease.

      Strengths:

      (1) The authors used a multi-level approach combining computational modeling with experimental datasets, including neuronal cultures, a rat model of temporal lobe epilepsy and human data.

      (2) Identification of key parameters such as neuronal count, firing rate, synchronization and brain state in observed incidence of FRs generated through random aggregation of neural firing.

      (3) Cross-species validation increases the likelihood of generalizability of the findings.

      Minor weakness:

      (1) The analyses conducted in human data lack direct comparison with sleep data due to no available data, but would encourage future investigations directly comparing HFOs during wakefulness and nocturnal sleep.

      Comments on revised version.

      The authors have addressed my comments and I have no further suggestions.

    1. Author response:

      The following is the authors’ response to the original reviews.

      eLife Assessment

      This fundamental study is part of an impressive, large-scale effort to assess the reproducibility of published findings in the field of Drosophila immunity. In a companion article, the authors analyze 400 papers published between 1959 and 2011, and assess how many of the claims in these papers have been tested in subsequent publications. In this article, the authors report the results of validation experiments to assess a subset of the claims that, according to the literature, have not been corroborated. While the evidence reported for some of these validation studies is convincing, it remains incomplete for others.

      We thank the reviewers for their careful assessment of our manuscript. We are fully aware that this review process required a substantial investment of time and effort, and we are deeply grateful for their engagement. We also thank the eLife editors for enabling an open and constructive evaluation process of the highest standard.

      We fully agree with the eLife assessment, including the concluding statement highlighting the limitations of our analysis. We also concur with most of the reviewers’ comments, which we have addressed in detail in the revised manuscript. Addressing these comments required extensive additional work, which explains the duration of the revision. This period was also valuable in allowing colleagues from the Drosophila community to provide feedback on our study, including identifying potential issues—for instance regarding SR-C1—that we have carefully re-examined.

      Major revisions include the addition of new experimental data in the sections on Hemese, SR-C1, Sphinx1/2, and Caspar. These results largely confirm our initial conclusions, with the exception of SR-C1. We have therefore revised our interpretation of SR-C1, confirming earlier findings that it promotes bacterial binding, while maintaining that it does not function as a major phagocytic receptor. A table with new list of new reagents has been added at the end of the supplement (Table Supplement S4). We also add a comment on the fact that mutation in the serine protease MP1 (work from B.L.) does not affect wound melanization as initially proposed (Tang et al., 2006).

      One final point: our study assesses replicability using alternative experimental approaches, and we cannot exclude the possibility that our conclusions may be inaccurate. This limitation is inherent to all reproducibility studies. Nonetheless, our work should encourage the community to exercise caution when interpreting certain previous claims, some of which have become widely accepted.

      We thank the reviewers and editors for their constructive input, which has significantly improved the manuscript. At this stage, we are ready to proceed toward a version of record together with the eLife assessment (which may still evolve). We continue to believe that our reproducibility project is unique in its scope and depth. It not only provides quantitative insight into replicability (See companion article)—suggesting that replication rates may be higher in certain fields, consistent with the maturation of knowledge over recent decades—but also contributes to clarifying and refining a number of statements within the field. Although aware of the cost of assessing reproducibility (hard work for articles that are not quoted and statements that are not taking in account), I consider it as one of my most important and original works.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      This work revisits a substantial part of the published literature in the field of Drosophila innate immunity from 1959 to 2011. The strategy has been to restrain the analysis to some 400 articles and then to extract a main claim, two to four major claims and up to four minor claims totaling some 2000 claims overall. The consistency of these claims with the current state-of the-art has been evaluated and reported on a dedicated Web site known as ReproSci and also in the text as well as in the 28 Supplements that report experimental verification, direct or indirect, e.g., using novel null mutants unavailable at the time, of a selected set of claims made in several articles. Of note, this review is mostly limited to the manuscript and its associated supplements and does not integrally cover the ReproSci website.

      Strengths:

      One major strength of this article is that it tackles the issue of reproducibility/consistency on a large scale. Indeed, while many investigators have some serious doubts about some results found in the literature, few have the courage, or the means and time, to seriously challenge studies, especially if published by leaders in the field. The Discussion adequately states the major limitations of the ReproSci approach, which should be kept in mind by the reader to form their own opinion.

      This study also allows investigators not familiar with the field to have a clearer understanding of the questions at stake and to derive a more coherent global picture that allows them to better frame their own scientific questions. Besides a thorough and up-to-date knowledge of the literature used to assess the consistency of the claims with our current knowledge, a merit of this study is the undertaking of independent experiments to address some puzzling findings and the evidence presented is often convincing, albeit one should keep in mind the inherent limitations as several parameters are difficult to control, especially in the field of infections, as underlined by the authors themselves. Importantly, some work of the lead author has also been re-evaluated (Supplements S2-S4). Thus, while utmost caution should be exerted, and often is, in challenging claims, even if the challenge eventually proves to be not grounded, it is valuable to point out potential controversial issues to the scientific community.

      While this is not a point of this review, it should be acknowledged that the possibility to post comments on the ReproSci website will allow further readjustments by the community in the appreciation of the literature and also of the ReproSci assessments themselves and of its complementary additional experiments.

      We praise the reviewer for this assessment of our project

      Weaknesses:

      Challenging the results from articles is, by its very nature, a highly sensitive issue, and utmost care should be taken when challenging claims. While the authors generally acknowledge the limitations of their approach in the main text and Supplements, there are a few instances where their challenges remain questionable and should be reassessed. This is certainly the case for Supplement S18, for which the ReproSci authors make a claim for a point that was not made in the publication under scrutiny. The authors of that study (Ramet et al., Immunity, 2001) never claimed that scavenger receptor SR-CI is a phagocytosis receptor, but that it is required for optimal binding of S2 cells to bacteria. Westlake et al. here have tested for a role of this scavenger receptor in phagocytosis, which had not been tested by Ramet et al. Thus, even though the ReproSci study brings additional knowledge to our understanding of the function of SR-CI by directly testing its involvement in phagocytosis by larval hemocytes, it did not address the major point of the Ramet et al. study, SR-CI binding to bacteria, and thus inappropriately concludes in Supplement S18 that "Contrary to (Ramet et al., 2001, Saleh et al., 2006), we find that SR-CI is unlikely to be a major Drosophila phagocytic receptor for bacteria in vivo." It follows that the results of Ramet et al. cannot be challenged by ReproSci as it did not address this program. Of note, Saleh et al. (2006) also mistakenly stated that SR-CI impaired phagocytosis in S2 cells and could be used as a positive control to monitor phagocytosis in S2 cells. Their assay appears to have actually not monitored phagocytosis but the association of FITC-labeled bacteria to S2 cells by FACS, as they did not mention quenching the fluorescence of bacteria associated with the surface with Trypan blue.

      We have revised our evaluation of Sr-C1, as we acknowledge that we did not initially read Rämet et al. carefully. We incorrectly assumed that this study demonstrated a role for SR-C1 in phagocytosis, whereas it actually reports a defect in binding only. We have updated our assessment of SR-C1, validating the results from Rämet et al., 2001. We still mention our results on phagocytosis (See below for more information).

      The inference method to assess the consistency of results with current knowledge also has limitations that should be better acknowledged. At times, the argument is made that the gene under scrutiny may not be expressed at the right time according to large-scale data or that the gene product was not detected in the hemolymph by a mass-spectrometry approach. While being in theory strong arguments, some genes, for instance, those encoding proteases at the apex of proteolytic activation cascades, need not necessarily be strongly expressed and might be released by a few cells. In addition, we are often lacking relevant information on the expression of genes of interest upon specific immune challenges such as infections with such and such pathogens.

      The pattern of expression is always used as an element supporting our assessment but never as the central point of decision (See below for more information).

      As regards mass spectrometry, there is always the issue of sensitivity that limits the force of the argument. Our understanding of melanization remains currently limited, and methods are lacking to accurately measure the killing activity associated with the triggering of the proPO activation cascade. In this study, the authors monitor only the blackening reaction of the wound site based on a semi-quantitative measurement. They are not attempting to use other assays, such as monitoring the cleavage of proPOs into active POs or measuring PO enzymatic activity. These techniques are sometimes difficult to implement, and they suffer at times from variability. Thus, caution should be exerted when drawing conclusions from just monitoring the melanization of wounds.

      We employed approaches similar to those used in the original studies under evaluation. However, we acknowledge that our analysis primarily relied on cuticular melanization, which is more straightforward to monitor. We have revised the manuscript to clarify this limitation, particularly in the case of PGRP-LE.

      Likewise, the study of phagocytosis is limited by several factors. As most studies in the field focus on adults, the potential role of phagocytosis in controlling Gram-negative bacterial infections is often masked by the efficiency of the strong IMD-mediated systemic immune response mediated by AMPs (Hanson et al, eLife, 2019). This problem can be bypassed in rare instances of intestinal infections by Gram-negative bacteria such as Serratia marcescens (Nehme et al., PLoS Pathogens, 2007) or Pseudomonas aeruginosa (Limmer et al. PNAS, 2011), which escape from the digestive tract into the hemocoel without triggering, at least initially, the systemic immune response. It is technically feasible to monitor bacterial uptake in adults by injecting fluorescently labeled bacteria and subsequently quenching the signal from noningested bacteria. Nonetheless, many investigators prefer to resort to ex vivo assays starting from hemocytes collected from third-instar wandering larvae as they are easier to collect and then to analyze, e.g., by FACS. However, it should be pointed out that these hemocytes have been strongly exposed to a peak of ecdysone, which may alter their properties. Like for S2 cells, it is thus not clear whether third-instar larval hemocytes faithfully reproduce the situation in adults. The phagocytic assays are often performed with killed bacteria. Evidence with live microorganisms is better, especially with pathogens. Assays with live bacteria require however, an antibody used in a differential permeabilization protocol. Furthermore, the killing method alters the surface of the microorganisms, a key property for phagocytic uptake. Bacterial surface changes are minimal when microorganisms are killed by X-ray or UV light. These limitations should be kept in mind when proceeding to inference analysis of the consistency of claims. Eater illustrates this point well. Westlake et al. state that:" [...] subsequent studies showed that a null mutation of eater does not impact phagocytosis". The authors refer here to Bretscher et al., Biology Open, 2015, in which binding to heat-killed E. coli was assessed in an ex vivo assay in third instar larvae. In contrast, Chung and Kocks (JBC, 2011) tested whether the recombinant extracellular N-terminal ligand-binding domain was able to bind to bacteria. They found that this domain binds to live Gram-positive bacteria but not to live Gram-negative bacteria. For the latter, killing bacteria with ethanol or heating, but not by formaldehyde treatment, allowed binding. More importantly, Chung and Kocks documented a complex picture in which AMPs may be needed to permeabilize the Gram-negative bacterial cell wall that would then allow access of at least the recombinant secreted Eater extracellular domain to peptidoglycan or peptidoglycan-associated molecules. Thus, the systemic Imd-dependent immune response would be required in vivo to allow Eater-dependent uptake of Gram-negative bacteria by adult hemocytes. In ex vivo assays, any AMPs may be diluted too much to effectively attack the bacterial membrane. A prediction is then that there should be an altered phagocytosis of Gramnegative bacteria in IMD-pathway mutants, e.g., an imd null mutant but not the hypomorphic imd[1] allele. This could easily be tested by ReproSci using the adult phagocytosis assay used by Kocks et al, Cell, 2005. At the very least, the part on the role of Eater in phagocytosis should take the Chung &Kocks study into account, and the conclusions modulated.

      We agree that experimental conditions can always influence the outcome and may partly explain discrepancies in reproducibility. However, our approach is based on conceptual replication, with the aim of testing the generalizability of the original findings rather than reproducing them under identical conditions. We often used approaches quite similar to the initial statements.

      In the case of Eater, our results challenge the conclusion from Kocks et al. that phagocytosis of Gram-negative bacteria is impaired in the absence of Eater, as this was not confirmed when using null eater mutants. Nevertheless, our data support the idea that Eater contributes to the phagocytosis of Gram-negative bacteria, likely in cooperation with NimC1.

      Importantly, our findings are fully consistent with those of Chung and Knocks, who showed that the extracellular domain of Eater binds Gram-positive but not Gram-negative bacteria. Therefore, our work refines a specific aspect of the original conclusion, without questioning the overall significance of the initial Eater studies.

      Another point is that some mutant phenotypes may be highly sensitive to the genetic background, for instance, even after isogenization in two different backgrounds. In the framework of a Reproducibility project, there might be no other option for such cases than direct reproduction of the experiment as relying solely on inference may not be reliable enough.

      With respect to the experimental part, some minor weaknesses have been noted. The authors rely on survival to infection experiments, but often do not show any control experiments with mock-challenged or noninfected mutant fly lines. In some cases, monitoring the microbial burden would have strengthened the evidence. For long survival experiments, a check on the health status of the lines (viral microbiota, Wolbachia) would have been welcome. Also, the experimental validation of reagents, RNAi lines, or KO lines is not documented in all cases.

      We thank the reviewer for their careful and constructive assessment. We agree with most of the points raised and have revised the manuscript accordingly. In particular, we have softened the wording throughout to make our evaluation less abrupt. We have also added a dedicated section on limitations at the end of the manuscript, highlighting potential sources of bias and the inherent constraints of our reproducibility approach.

      In addition, we have expanded the description of the tools used and the validation of the RNAi experiments (see below). We consider it unlikely that factors such as Wolbachia or Nora virus significantly affect our conclusions, as our assays rely on short-term survival experiments, whereas these variables are more likely to influence ageing-related phenotypes. That said, we fully acknowledge that unrecognized parameters—such as environmental conditions (e.g., humidity), which we did not systematically control—could contribute to discrepancies. This limitation, however, applies broadly to most attempts at experimental reproduction.

      More generally, many of the claims we challenge have not been revisited for over a decade. Our inability to validate some of them suggests that the underlying biology may be more complex than initially proposed. We recognize that some of our conclusions may be incorrect, and it would be surprising if all were entirely accurate. At the same time, reproducibility studies often face an asymmetry in standards of evidence, whereby contradicting a published claim requires a higher burden of proof than establishing it. We believe it is important to document and share such discrepancies. We also explicitly acknowledge in the revised manuscript that the ReproSci framework itself may contain errors. Even if a significant proportion of our assessments are not correct, we believe this work contributes meaningfully to clarifying ongoing debates in the field for most of them.

      Finally, since the launch of the website, we have received three comments from the community—one addressing a major claim (Sr-C1) and two addressing more minor points— which have led us to refine our conclusions. The limited feedback we received suggest a broad agreement of the community with our assessment. It illustrates the value of maintaining an open, community-driven resource. The public and evolving nature of the project is, in our view, a key strength.

      Reviewer #2 (Public review):

      Summary:

      The authors present an ambitious and large-scale reproducibility analysis of 400 articles on Drosophila immunity published before 2011. They extract major and minor claims from each article, assess their verifiability through literature comparison and, when possible, through targeted experimental re-testing, and synthesize their findings in an openly accessible online database. The goal is to provide clarity to the community regarding claims that have been contradicted, incompletely supported, or insufficiently followed up in the literature, and to foster broader community participation in evaluating historical findings. The manuscript summarizes the major insights emerging from this systematic effort.

      Strengths:

      (1) Novelty and community value: This work represents a rare example of a systematic, transparent, and community-facing reproducibility project in a specific research domain. The creation of a dedicated public platform for disseminating and discussing these assessments is particularly innovative.

      (2) Breadth and depth: The authors analyze an impressive number of publications spanning multiple decades, and they couple literature-based assessments with new experimental data where follow-up is missing.

      (3) Clarity of purpose: The manuscript carefully distinguishes between assessing evidential support for claims and judging the scientific merit of historical work. This helps frame the project as constructive rather than punitive.

      (4) Metascientific relevance: The analysis identifies methodological and contextual factors that commonly underlie irreproducible claims, providing a useful guide for future study design and interpretation.

      (5) Transparency: Supplementary datasets and the public website provide an exceptional degree of openness, which should facilitate community engagement and further refinement.

      We praise the reviewer for this assessment of our project.

      Weaknesses:

      (1) Subjectivity in selection: Despite the authors' efforts, the choice of which papers and claims to highlight cannot be entirely objective. This is an inherent limitation of any retrospective curation effort, but it remains important to acknowledge explicitly.

      We have added a section at the end of the discussion to discuss the limitation of our study.

      (2) Emphasis on irreproducible claims: The manuscript focuses primarily on claims that are challenged or found to be weakly supported. While understandable from the perspective of novelty, this emphasis may risk overshadowing the value of claims that are well supported and reproducible.

      We have added two sentences at the end of the introduction and at the beginning of the discussion that most claims are reproducible.

      (3) Framing and language: Certain passages could benefit from more neutral phrasing and avoidance of binary terms such as "correct" or "incorrect," in keeping with the open-ended and iterative nature of scientific progress.

      We have carefully checked the phrasing of our article to be more nuanced and avoid black-and-white assessments.

      (4) Community interaction with the dataset: While the website is an excellent resource, the manuscript could further clarify how the community is expected to contribute, challenge, or refine the annotations, especially given the large volume of supplementary data.

      This point is already addressed in the revised sentence: “We hope that the community accessible website will encourage researchers to share their perspectives and contribute data from diverse sources, thereby improving objectivity.” In addition, we have proactively engaged with principal investigators to motivate them to contribute to this effort by sharing unpublished results and information. However, it remains unclear to what extent scientists are genuinely interested in reproducibility, as has been noted in other studies on the topic. For example, articles that challenge previous findings are often under-cited, and the presence of contradictory evidence does not necessarily prevent researchers from continuing to cite the original claims. This is clearly a challenge of reproducibility study. Comments, evidence and corrections will not be integrated in the ReproSci website. We have already updated this database when revising this article and will continue to do it.

      (5) Minor inconsistency: The manuscript states that papers from 1959-2011 were included, but the Methods section mentions a range beginning in 1940.

      This should be aligned for clarity.

      We have solved this discrepancy by correcting the method section. This should be 1959-2011. Thank you for spotting this mistake.

      Impact and significance:

      This contribution is likely to have a meaningful impact on both the Drosophila immunity community and the broader scientific ecosystem. It highlights methodological pitfalls, encourages transparent post-publication evaluation, and offers a reusable framework that other fields could adopt. The work also has pedagogical value for early-career researchers entering the field, who often struggle to navigate contradictory or outdated claims. By centralizing and contextualizing these discussions, the manuscript should help accelerate more robust and reproducible research.

      Reviewer #3 (Public review):

      Summary:

      In this ambitious study, the authors set out to analyse the validity of a number of claims, both minor and major, from 400 published articles within the field of Drosophila immunity that were published before 2011. The authors were able to determine initially if claims were supported by comparing them to other published literature in the field and, if required, by experimentally testing 'unchallenged' claims that had not been followed up in subsequent published literature. Using this approach, the authors identified a number of claims that had contradictory evidence using new methods or taking into account developments within the field post-initial publication. They put their findings on a publicly available website designed to enable the research community to assess published work within the field with greater clarity.

      Strengths:

      The work presented is rigorous and methodical, the data presentation is high quality, and importantly, the data presented support the conclusions. The discussion is balanced, and the study is written considerately and respectfully, highlighting that the aim of the study is not to assign merit to individual scientists or publications but rather to improve clarity for scientists across the field. The approach carried out by the researchers focuses on testing the validity of the claims made in the original papers rather than testing whether the original experimental methods produced reproducible results. This is an important point since there are many reasons why the original interpretation of data may have understandably led to the claims made. These potential explanations for irreproducible data or conclusions are discussed in detail by the authors for each claim investigated.

      The authors have generated an accompanying website, which provides a valuable tool for the Drosophila Immunity research community that can be used to fact-check key claims and encourages community engagement. This will achieve one important goal of this study - to prevent time loss for scientists who base their research on claims that are irreproducible. The authors rightly point out that it is impossible (and indeed undesirable) to avoid publication of irreproducible results within a field since science is 'an exploratory process where progress is made by constant course correction'. This study is, however, an important piece of work that will make that course correction more efficient.

      Weaknesses:

      I have little to recommend for the improvement of this manuscript. As outlined in my comments above, I am very supportive of this manuscript and think it is a bold and ambitious body of work that is important for the Drosophila immunity field and beyond.

      We thank the reviewer for this positive assessment. This was indeed a huge amount of work with the hope this would be useful.

      Reviewer #4 (Public review):

      This is an important paper that can do much to set an example for thoughtful and rigorous evaluation of a discipline-wide body of literature. The compiled website of publications in Drosophila immunity is by itself a valuable contribution to the field. There is much to praise in this work, especially including the extensive and careful evaluation of the published literature.

      However, there are also cautions.

      We praise the reviewer for this assessment of our project.

      One notable concern is that the validation experiments are generally done at low sample sizes and low replication rates, and often lack statistical analysis. This is slippery ground for declaring a published study to be untrue. Since the conclusions reported here are nearly all negative, it is essential that the experiments be performed with adequate power to detect the originally described effects. At a minimum, they should be performed with the same sample size and replication structure as the originally reported studies.

      Many of the original claims we are assessing were obtained with lower sample size than our replicability experiments. Furthermore, we are often complementing our data with alternative approaches that are more robust (survival with additional bacterial strains, AMP kinetics with several time points, etc.). Although we can never claim for a total absence of an effect, our experimental designs are largely sufficient to demonstrate that we cannot report the major effects reported in the initial publications.

      The first section of Results should be an overview of the general accuracy of the literature.

      Of all claims made in the 400 evaluated papers, what proportion fell into each category of "verified", "unchallenged", "challenged", "mixed", or "partially verified"? This summary overview would provide a valuable assessment of the field as a whole. A detailed dispute of individual highlighted claims could follow the summary overview.

      We have described the statistic of our analysis on claim validity in a companion article that will be published back-to-back with this article. We have preferred to divide assessment of claims and statistics on replicability in two articles. The present one is to provide an overview of the main claims that we considered to be fragile. Following the reviewer’s comment, we have added at the start of the manuscript a sentence stating that most of the claims were found to be validated, highlighting the solidity of the field with a link to the other article.

      Section headings are phrased as declarative statements, "Gene X is not involved in process Y", which is more definitive phrasing than we typically use in scientific research. It implies proving a negative, which is difficult and rare, and the evidence provided in the present manuscript generally does not reach that threshold. A more common phrasing would be "We find no evidence that gene X contributes to process Y". A good model for this more qualified phrasing is the "We conclude that while Caspar might affect the Imd pathway in certain tissue-specific contexts, it is unlikely to act as a generic negative regulator of the Imd pathway," concluding the section on the role of Caspar. I am sure the authors feel that the softer, more qualified phrasing would undermine their article's goal of cleansing the literature of inaccuracies, but the hard declarative 'never' statements are difficult to justify unless every validation experiment is done with a high degree of rigor under a variety of experimental conditions. This caveat is acknowledged in the 3rd paragraph of the Discussion, but it is not reflected in the writing of the Results. The caveat should also appear in the Introduction.

      We fully agree with the reviewer and we have softened the way we discuss all the claims in the result section.

      The article is clear that "Claims were assessed as verified, unchallenged, challenged, mixed, or partially verified," but the project is called "reproducibility project" in the 7th line of the abstract, and the website is "ReproSci". The fourth line of the abstract and the introduction call some published research "irreproducible". Most of the present manuscript does not describe reproduction or replication. It describes validation, or independent experimental tests for consistency. Published work is considered validated if subsequent studies using distinct approaches yielded consistent results. For work that the authors consider suspicious, or that has not been subsequently tested, the new experiments provided here do not necessarily recreate the published experiment. Instead, the published result is evaluated with experiments that use different tools or methods, again testing for consistency of results. This is an important form of validation, but it is not reproduction, and it should not be referred to as such. I strongly suggest that variations of the words "reproducible" or "replication" be removed from the manuscript and replaced with "validation". This will be more scientifically accurate and will have the additional benefit of reducing the emotional charge that can be associated with declaring published research to be irreproducible.

      We agree on this point. In response to the reviewer’s comment, we have clarified our terminology. Specifically, we now use the term “conceptual replicability” in the abstract and consistently refer to “replicability” and “irreplicability” throughout the manuscript. We hope this revised terminology improves clarity.

      The manuscript includes an explanatory passage in the Results section, "Our project focuses on assessing the strength of the claims themselves (inferential/indirect reproducibility) rather than testing whether the original methods produce repeatable results (results/direct reproducibility). Thus, our conclusions do not directly challenge the initial results leading to a claim, but rather the general applicability of the claim itself." Rather than first appearing in Results, this statement should appear prominently in the abstract and introduction because it is a core element of the premise of the study. This can be combined with the content of the present Disclaimer section into a single paragraph in the Introduction instead of appearing in two redundant passages. I would again encourage the authors to substitute the word validation for reproduction, which would eliminate the need for the invented distinction between indirect versus direct reproduction. It is notable that the authors have chosen to title the relevant Methods section "Experimental Validation" and not "Replication".

      The disclaimer has been moved at the end of the introduction and one sentence has been added in the abstract.

      Experimental data "from various laboratories" in the last paragraph of the Introduction and the first paragraph of the Results are ambiguous. Since these new experiments are part of the central core of the manuscript, the specific laboratories contributing them should be named in the two paragraphs. If experiments are being contributed by all authors on the manuscript, it would suffice to say "the authors' laboratories". The attribution to "various labs" appears to be contradicted by the Discussion paragraph 2, which states "the host laboratory has expertise in" antibacterial and antifungal defense, implying a single lab. The claim of expertise by the lead author's laboratory is unnecessary and can be deleted if the Lemaitre lab is the ultimate source of all validation experiments.

      The authors and laboratories that did the experiments are listed in the author list and are easy to identify for experts. At the same time, we did not want to highlight the specific authors to avoid a negative impact on their career. We were very happy that a small number of labs helped in our project. Since all the supplement were reviewed by Hannah Westlake (who has left the lab and the project) and myself (BL), our expertise was important as we did not want to test articles far from what we are doing in the lab. I rephrase the sentence to make it clear.

      The passage on the controversial role of Duox in the gut is balanced and scholarly, and stands out for its discussion of multiple alternative lines of evidence in the published literature and supplement. This passage may benefit from research by multiple groups following up on the original claims that are not available for other claims, but the tone of the Duox section can be a model for the other sections.

      Comments on other sections and supplements:

      I understand the desire to explain how original results may have been obtained when they are not substantiated by subsequent experiments. However, statements such as "The initial results may have been obtained due to residual impurities in preparations of recombinant GNBP1" and "Non-replicable results on the roles of Spirit, Sphinx and Spheroide in Toll pathway activation may be due to off-target effects common to first-generation RNAi tools" are speculation. No experimental data are presented to support these assertions, so these statements and others like them (currently at the end of most "insights" sections) should not appear in Results. I recognize that the authors are trying to soften their criticism of prior studies by providing explanations for how errors may have occurred innocently. If they wish to do so, the speculative hypotheses should appear in the Discussion.

      The statement in Results that "The initial claim concerning wntD may be explained by a genetic background effect independent of wntD" similarly appears to be a speculation based on the reading of the main text Results. However, the Discussion clarifies that "Here, we obtained the same results as the authors of the claim when using the same mutant lines, but the result does not stand when using an independent mutant of the same gene, indicating the result was likely due to genetic background." That additional explanation in the Discussion greatly increases reader confidence in the Result and should be explained with reference to S5 in the Results. Such complete explanations should be provided everywhere possible without requiring the reader to check the Supplement in each instance.

      In some cases, such as "The results of the initial papers are likely due to the use of ubiquitous overexpression of PGRP-LE, resulting in melanization due to overactivation of the Imd pathway and resulting tissue damage", the claim to explain the original finding would be easy to test. The authors should perform those tests where they can, if they wish to retain the statements in the manuscript. Similarly, the claim "The published data are most consistent with a scenario in which RNAi generated off-target knockdown of a protein related to retinophilin/undertaker, while Undertaker itself is unlikely to have a role in phagocytosis" would be stronger if the authors searched the Drosophila genome for a plausible homolog that might have been impacted by the RNAi construct, and then put forth an argument as to why the off-target gene is more likely to have generated the original phenotype than the nominally targeted gene. There is a brief mention in S19 that junctophilin is the authors' preferred off-target candidate, but no evidence or rationale is presented to support that assertion. If the original RNAi line is still available, it would be easy enough to test whether junctophilin is knocked down as an offtarget, and ideally then to use an independent knockdown of junctophilin to recapitulate the original phenotype. Otherwise, the off-target knockdown hypothesis is idle speculation.

      A good model is the passage on extracellular DNA, which states, "experiments performed for ReproSci using the original DNAse IIlo hypomorph show that elevated Diptericin expression in the hypomorph is eliminated by outcrossing of chromosome II, and does not occur in an independent DNAse II null mutant, indicating that this effect is due to genetic background (Supplementary S11)." In this case, the authors have performed a clear experiment that explains the original finding, and inclusion of that explanation is warranted. Similar background replacement experiments in other validations are equally compelling.

      We believe that offering possible explanations for discrepancies between results is valuable for readers. For this reason, we have generally retained these elements in the Results section, with the exception of PGRP-SD. In that specific case, we removed the sentence stating that we could not identify the expected mutation in the original PGRP-SD mutants (see below). Although these points could have been moved to the Discussion, doing so would have made it difficult to directly associate each explanation with the corresponding claim. We therefore consider that keeping them in the Results section provides greater clarity. Our hypotheses are grounded in well-established considerations. It is known, for example, that early generations of RNAi constructs often exhibited off-target effects, that commercially available LPS preparations (e.g., from Sigma) were sometimes contaminated, and that genetic background can significantly influence immunological outcomes. It is therefore essential to consider and discuss such confounding factors, particularly those that were not fully appreciated at the time the field emerged.

      Identifying motivated collaborators and coordinating experimental validation proved to be extremely time-consuming, making it impractical to systematically provide experimental verification for every discrepancy. As a result, most of our explanations remain speculative, except for the cases of WntD and DNase II, where the observed differences can be attributed to genetic background effects.

      The statement "Analysis of several fly stocks expected to carry the PGRP-SDdS3 mutation used in the initial study revealed the presence of a wild-type copy PGRP-SD, suggesting that either the stock used in this study did not carry the expected mutation, or that the mutation was lost by contamination prior to sharing the stock with other labs" provides a documentable explanation of a potential error in the original two manuscripts, but the subsequent "analysis of several fly stocks" needs citations to published literature or explanation in the supplement. It is unclear from this passage how the wildtype allele in the purportedly mutant stocks could have led to the misattribution of function to PGRP-SD, so that should be explained more clearly in the manuscript.

      We have removed this statement in the revised version from the result section

      The originally claimed anorexia of the Gr28b mutation is explained as having been "likely obtained due to comparison to a wild-type line with unusually high feeding rates". This claim would be stronger if the wildtype line in question were named and data showing a high rate of feeding were presented in the supplement or cited from published literature. Otherwise, this appears to be speculation.

      The wild-type fly stocks we used are named in the supplement.

      In the section "The Toll immune pathway is not negatively regulated by wntD", FlyAtlas is cited as evidence that wntD is not expressed in adult flies. However, the FlyAtlas data is not adequately sensitive to make this claim conclusively. If the present authors wish to state that wntD is not expressed in adults, they should do a thorough test themselves and report it in the Supplement.

      Alternatively, the statement "data from FlyAtlas show that wntD is only expressed at the embryonic stage and not at the adult stage at which the experiments were performed by (Gordon et al., 2005a)" could be rephrased to something like "data from FlyAtlas show strong expression of wntD in the embryo but not the adult" and it should be followed by a direct statement that adult expression was also found to be near-undetectable by qPCR in supplement S5. That data is currently "not shown" in the supplement, but it should be shown because this is a central result that is being used to refute the original claim. This manuscript passage should also describe the expression data described in Gordon et al. (2005), for contrast, which was an experimental demonstration of expression in the embryo and a claim "RT-PCR was used to confirm expression of endogenous wntD RNA in adults (data not shown)."

      We agree on this but the expression pattern provided from fly atlas and other genomic resource is an additional element that reinforce our conclusion. For instance, the observation that the expression pattern of WntD is limited to early embryo is consistent with a role in the regulation of Toll pathway in D/V patterning but not immunity. The use of the expression pattern is not the key element of our assessments that rely on the use of loss-of-function mutation. We have rephrased the text in the manuscript according to Reviewer’s suggestion.

      Inclusion of the section on croquemort is curious because it seems to be focused exclusively on clearance of apoptotic cells in the embryo, not on anything related to immunity. The subsection is titled "Croquemort is not a phagocytic engulfment receptor for apoptotic cells or bacteria", but the text passage contains no mention of phagocytosis of bacteria, and phagocytosis of bacteria is not tested in the S17 supplement. I would suggest deleting this passage entirely if there is not going to be any discussion of the immune-related phenotypes.

      The reviewer is correct and we have in the revised version removed ‘bacteria’ from the title. We have kept the section S17 because this statement ‘Crq recognize and uptake apoptotic cells’ (Science, Immunity)’ is still a source of confusion while the role of crq is more downstream. We agree that efferocytosis might not considered as part of innate immunity but we consider these articles were important in the Drosophila immunity community at that time.

      The claim "Toll is not activated by overexpression of GNBP3 or Grass: Experiments performed for ReproSci find that contrary to previous reports, overexpression of GNBP3 (Goear et al., 2006) or Grass (El Chamy et al., 2008) in the absence of immune challenge does not effectively activate Toll signaling (Supplementaries S6, S7)" is overly strongly stated unless the authors can directly repeat the original published studies with identical experimental conditions. In the absence of that, the claim in the present manuscript needs to be softened to "we find no evidence that..." or something similar. The definitive claim "does not" presumes that the current experiments are more accurate or correct than the published ones, but no explanation is provided as to why that should be the case. In the absence of a clear and compelling argument as to why the current experiment is more accurate, it appears that there is one study (the original) that obtained a certain result and a second study (the present one) that did not. This can be reported as an inconsistency, but the second experiment does not prove that the first was an error.

      We have softened our statement and revised the supplement document. The title of the section is now ‘Toll is not strongly activated by overexpression of GNBP3 or Grass’. However we want to keep these supplements. The comment of the reviewer applies to all our assessment as we could be wrong. We are using experimental validation and not replication, although in this present case, we are using very similar approach to the described in the original study. Of note, the fact that over-expression of GNBP3 does not consistently activate Drs was already stated in Buchon et al 2019 and we spend quite sometimes in attempts to repeat this experiment. Finally, the Ferrandon team that produce this claim can easily repeat the experiment. This does not affect the main conclusion of their landmark article on GNBP3.

      The same comment applies to the refutation of the roles for Edin and IRC. Even though the current experiments are done in the context of a broader validation study, this does not automatically make them more correct. The present work should adhere to the same standards of reporting that we expect in any other piece of science.

      We fully agree with the reviewer but the comments he/she raised apply to all the assessments made in our article and nearly all the reproducibility experiments. Our assessment does not state that we are right but that we fail to conceptually reproduce the claim. This is clearly mentioned in our article. We hope to see clarification in the future. It may be one day shown that i) IRC indeed regulates intestinal immunity, ii) PGRP-LE will be shown to have an extracellular form, iii) 18W could indeed be a PRR for LPS (maybe in a specific tissues), iv) PGRPSD will be shown to function upstream of Toll, v) that Crq indeed binds apoptotic cell to internalize them… Our study highlights statements that are source of debate, but this is far from being clear. The authors of these challenged claims have the opportunity to contradict us.

      The statement "Furthermore, evidence from multiple papers suggests that this result, and other instances where mutations have been found to specifically eliminate Defensin expression, is likely due to segregating polymorphisms within Defensin that disrupt primer binding in some genetic backgrounds and lead to a false negative result (Supplementary S20)" should include citations to the multiple papers being referenced. This passage would benefit from a brief summary of the logic presented in S20 regarding the various means of quantifying Defensin expression.

      We appreciate the value of citing some of the papers underlying this claim. Key papers in question are discussed at length in Supplement S20, and the original papers do not realize the issue we are reporting. We therefore modified the text as follows: "Furthermore, this result, and other instances where mutations have been found to specifically eliminate Defensin expression, is likely due to segregating polymorphisms within Defensin that disrupt primer binding in some genetic backgrounds, leading to false negative results (Brennan 2007,Neyen 2014 and see Supplementary S20)”. The hypothesis we raise, namely that defensin function may involve specific polymorphisms that are absent from the reference Drosophila genome, is an important consideration that should be communicated to the community.

      In S22 Results, the statement "For general characterization of the IrcMB11278 mutant, including developmental and motor defects and survival to septic injury, see additional information on the ReproSci website" is not acceptable. All necessary information associated with the paper needs to be included in the Supplement. There cannot be supporting data relegated to an independent website with no guaranteed stability or version control. The same comment applies to "Our results show that eiger flies do not have reduced feeding compared to appropriate controls (See ReproSci website)" in S25.

      The ReproSci website contains additional data that we could not display in the supplement but may be useful to scientists. We believe that it is worth to mention them. We have however changed the writing stating ‘Experiments reported in the ReproSci website’ rather than ‘See ReproSci website’ to make it clear that the data are not part of the supplement.

      For IRC: We have added a new section that addresses the general characterization of the IrcMB11278 mutant in the revised version (Supplement 22 Figure 2 and 3 with associated text). We do not refer to the ReproSci website anymore.

      Supplement S21 appears to show a difference between the wildtype and hemese mutants in parasitoid encapsulation, which would support the original finding. However, the validation experiment is performed at a small sample size and is not replicated, so there can be no statistical analysis. There is no reported quantification of lamellocytes or total hemocytes. The validation experiment does not support the conclusion that the original study should be refuted. The S21 evaluation of hemese must either be performed rigorously or removed from the Supplement and the main text.

      To address reviewers’ comment, we generated two new Hemese null mutants, Hemese<sup>JP187</sup> and Hemese<sup>JP828</sup>, carrying deletions in the central region of the gene. Using these lines, we show that wild-type and Hemese mutant larvae display comparable levels of lamellocytes and similar numbers of melanized capsules following wasp infestation. We further quantified lamellocyte differentiation and included appropriate statistical analyses. We have removed the previous results obtained with the Hemese<sup>SK2</sup> mutant, which yielded similar observations. By reproducing our previous findings with independent mutant lines and by providing quantitative analyses, we strengthen our conclusion that Hemese does not act as a negative regulator of lamellocyte differentiation upon wasp infestation.

      In S22, the second sentence of the passage "Due to the fact that IrcMB11278 flies always survived at least 24h prior to death after becoming stuck to the substrate by their wings, we do not attribute the increased mortality in Ecc15-fed IrcMB11278 flies primarily to pathogen ingestion, but rather to locomotor defects. The difference in survival between sucrose-fed and Ecc15-fed IrcMB11278 flies may be explained by the increased viscosity of the Ecc15-containing substrate compared to the sucrose-containing substrate" is quite strange. The first sentence is plausible and a reasonable interpretation of the observations. But to then conclude that the difference between the bacterial treatment versus the control is more plausibly due to substrate viscosity than direct action of the bacteria on the fly is surprising. If the authors wish to put forward that interpretation, they need to test substrate viscosity and demonstrate that fly mortality correlates with viscosity. Otherwise, they must conclude that the validation experiment is consistent with the original study.

      The viscosity of a vial can easily be assessed by direct observation. Here, we provide an information that may guide further research but this is by no way a strong point of our article. Thus, we did not do any change to address this comment. We agree that the function of IRC should be entirely re-visited. We have however changed the name viscosity for stickiness to be more neutral.

      In S27, the visualization of eiger expression using a GFP reporter is very non-standard as a quantitative assay. The correct assay is qPCR, as is performed in other validation experiments, and which can easily be done on dissected fat body for a tissue-specific analysis. S27 Figure 1 should be replaced with a proper experiment and quantitative analysis. In S27 Figure 2, the authors should add a panel showing that eiger is successfully knocked down with each driver>construct combination. This is important because the data being reported show no effect of knockdown; it is therefore imperative to show that the knockdown is actually occurring. The same comment applies everywhere there is an RNAi to demonstrate a lack of effect.

      Eiger expression: Previous RNA-seq (Flyseq, Troha et al., 2018) or Affymetrix array using poly (A)- RNA (De Gregorio et al., 2001) have never identified eiger as an immune-induced gene. We have used a previously characterized GFP reporter gene using the same approach done by the author to attempt to see an induction in the fat body without success. Our conclusions have been nuanced.

      Eiger RNAi KD: The two RNAi lines we are using have already been used in many studies assessing the function of eiger ((#108814, reference here, #45253 reference here)

      The Drosomycin expression data in S3 Figure 2A look extremely noisy and are presented without error bars or statistical analysis. The S4 claim that sphinx and spheroid are not regulators of the Toll pathway because quantitative expression levels of these genes do not correlate with Toll target expression levels is an extremely weak inference. The RNAi did not work in S4, so no conclusion should be inferred from those experiments. Although the original claims in dispute may be errors in both cases, the validation data used to refute the original claims must be rigorous and of an acceptable scientific standard.

      S3: The inducibility of antimicrobial peptide genes is high, albeit very variable. Importantly, we do not observe any inhibition of Drs expression at the two time points (24 and 48 h) following infection with two distinct bacteria, M. luteus and E. faecalis. Although each experiment was performed once, this corresponds to four independent tests challenging the claim from my lab that “Spheroide is required for activation of the Toll pathway.” Furthermore, if Spheroide played a significant role in Toll pathway activation, increased susceptibility to E. faecalis, B. subtilis, and B. bassiana would be expected. However, both survival data (three independent experiments) and Drs expression profiles (four conditions) consistently indicate that Spheroide is not required for Toll pathway activation. For clarity, we have removed the data related to S. aureus.

      S4: To address the reviewer’s comments and reinforce our conclusion, we generated a deletion removing both sphinx 1 and sphinx 2 and analyzed Toll pathway activity in the absence of these two serine proteases. We find that flies lacking sphinx 1 and sphinx 2 exhibit wild-type induction of Drosomycin following M. luteus infection, as well as normal survival upon E. faecalis challenge. These new data provide strong evidence supporting our claim that, in contrast to our previous report (Kambris et al., 2006), Sphinx 1 and Sphinx 2 do not regulate the Toll pathway. Accordingly, we have replaced the earlier RNAi-based results with data obtained from loss-of-function mutants.

      In S6 Figure 1, it is inappropriate to plot n=2 data points as a histogram with mean and standard errors. If there are fewer than four independent points, all points should be plotted as a dot plot. This comment applies to many qPCR figures throughout the supplement. In S7 Figure 1, "one representative experiment" out of two performed is shown. This strongly suggests that the two replicates are noisy, and a cynical reader might suspect that the authors are trying to hide the variance. This also applies to S5 Fig 3. Particularly in the context of a validation study, it is imperative to present all data clearly and objectively, especially when these are the specific data that are being used to refute the claim.

      S6: The figure 1 of S6 shows all the points. Collectively, this represents 6 replications using 3 drivers of the claim ‘over-expression of GNBP3 efficiently activate the Toll pathway’. The observation, we are now reporting in S6, was already mentioned in Buchon et al 2009 (PNAS). To address reviewer’s concern, we have removed the standard deviation. Finally, our conclusion is rather soft ‘Overexpression of GNBP3 either ubiquitously or in the fat body does not effectively activate the Toll pathway’. At most, we find similar to (El Chamy et al., 2008) that overexpression may produce ‘weak but detectable’ activation of Toll’.

      S7: We could not address this point. The point stands, there is no condition where overexpression of native Grass corresponds with higher Drosomycin expression

      Other comments:

      In S26, the authors suggest that much of the observed melanization arises from excessive tissue damage associated with abdominal injection contrasted to the lesser damage associated with thoracic injection. I believe there may be a methodological difference here. The Methods of S27 are not entirely clear, but it appears that the validation experiment was done with a pinprick, whereas the original Mabary and Schneider study was done with injection via a pulled capillary. My lab group (and I personally) have extensive experience with both techniques. In our hands, pinpricks to the abdomen do indeed cause substantial injury, and the physically less pliable thorax is more robust to pinpricks. However, capillary injections to the abdomen do virtually no tissue damage - very probably less than thoracic injections - and result in substantially higher survivals of infection even than thoracic injections. Thus, the present manuscript may infer substantial tissue damage in the original study because they are employing a different technique.

      The reviewer is correct that injection and pinprick injury do not induce the same type of injury and there are differences across labs. We still believe that our approach is valuable. The point is that we confirmed a role of eiger in melanization but not due to its expression in the fat body. It is important to underline that our ReproSci is a conceptual replication project and that we never directly challenge the original observation but rather the robustness of the claim. Injection with a pulled capillary was attempted — in our hands, this caused extensive trauma and killed over 80% of flies it was attempted on. The pinprick on the other hand caused very little trauma. The first sentence of the Results/discussion section states this point.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      It is questionable whether all the studies relevant to the field of assessment have been identified, starting with the own publications from the lead authors. Indeed, Buchon et al, Genes & Development, 2009, Buchon et al., Cell Host&Microbe, 2009, Buchon et al., BMC Biology, 2010 have not been included in the 400 articles, even though one of them is cited when discussing the role of Duox in the intestinal host defense. Other missing articles that fulfill the criteria set by the authors include, but may not be limited to, Chung et al. JBC, 2011, Nehme et al., PLoS One, 2011, Cronin et al., Science, 2009, Limmer et al. 2011.

      In our selection, we did not choose articles dealing with intestinal homeostasis and stem cells as well as microbiota/symbionts (Buchon 2009a,b and 2010 Cronin 2009). We also did not analyze articles centered on virulence factor (Limmer 2011). I agree that we missed Chung et al. JBC, 2011 and Nehme et al., PLoS One, 2011 that were published in 2011. Table S1 provide all the information on the article we selected and the ones we removed from the first search.

      One area of the field that would have benefited from further insights of ReproSci is that of innate immunity memory or priming (Pham et al., PLoS Pathogens, 2007, has been included in the 400 articles). That being said, the scope of this article is already considerable, and this is just a suggestion for future scrutiny.

      The reviewer should recognize that this study (Pham et al.) is inherently complex to reproduce. The field of innate immune priming has also matured considerably since the first publications. Importantly, the set of articles containing “non-validated claims” does not fully overlap with the category of studies that might be considered as weak or problematic.

      A major issue in science is the exaggeration of claims, which our approach does not capture. As a result, some articles that are strongly promoted yet make relatively trivial claims— often a source of frustration within the community—may still be classified as valid under our framework. This represents an important limitation of our approach.

      For the Supplements, it would be better to show all the data points, especially with respect to RTqPCR data. The nature of the error bars (SD, SE) is never indicated except for one exception (Figure 5, S28). When introducing or using novel lines affecting gene expression, such as RNAi lines or KO mutants, there are often no indications as to how these lines have been validated.

      This is especially critical for negative results.

      Errors bars: The errors bars were standard deviation. Sorry for this lacks of clarity. This is now indicated in the supplement. Experiments were done in multiple laboratories requiring complex coordination. For this reason, changing all the graphs was too complicated and could not be done for all the figures in the revised version. However data points are shown in many figures of the original draft and all the new figures of the revised version.

      For RNAi validation: Concerning the RNAi validation:

      (a) Sphinx ½: We have extended our work on Sphinx using a newly generated double

      mutant that remove both Sphinx1 and 2. Thus our conclusion does not rely anymore only the use of RNAi.

      (b) S12: Hep RNAi : We are using standard Hep-RNAi and BskDN fly tools that have been validated in many studies.

      Articles validating the HepRNAi (BDSC35210) can be found on this link. This line has also been validated in Figure 1 of the revised version of Supplement S12.

      Articles validating the BskDN (BDSC6409) can be found on this link.

      Of note, the Bloomington number of Hep RNAi was miss-annotated and has been corrected in the revised version.

      (a) S16. Dscam: The Trip RNAi lines has been used in other articles (ex. Bui et al., “Adjacent neuronal fascicle guides motoneuron dendritic branching 2024 (eNeuro)).

      (b) S23. Duox. We are using two RNAi lines including the original RNAi construct used in the article we assessed (Ha et al., 2005).

      (c) Eiger: we are using two distinct UAS-RNAi constructs that have been validated (#108814, reference here, #45253 reference here).

      Loss-of-function mutations:

      For previously described mutants: we used some previously described mutants available in stock centers or from other labs. These include Spheroide<sup>D104</sup>, wntD mutants Irc<sup>MB11278</sup>, NOS<sup>Δall</sup> and Gr28b. See references in the supplement. We have always checked the genotypes of these mutants.

      For newly generated mutants

      spirit<sup>DR32</sup> see Figure 1 in S2

      edin<sup>KO</sup>: we have added a new figure describing the mutant in S14 D

      ΔSphinx1/2 we have added a figure describing the mutant in S4

      DNaseII<sup>sk4</sup>: the exact frameshift mutation is indicated in S11

      SR-CI<sup>SK6</sup> and Δ(Sr-CI,Sr-CIII): we have added a figure describing the mutant in S18

      Hemese<sup>JP187</sup> and HemeseJP<sup>828</sup> we have added a figure describing the mutant in S21

      Listericin<sup>Δ1</sup> and Listericin<sup>Δ2</sup> mutation are described in Figure 1 in S15

      We have now included in the revised supplement a table with all the new tools generated in the framework of the ReproSci project (Supplementary Table 4).

      The only uncharacterized mutant is PGRP-LE<sup>Δ53</sup>, a gift from François Rouyer (Gif-sur-Yvette). But we also did our experiments with an established mutant: PGRP-LE<sup>112</sup>.

      Is the repeated use of "in vitro" to refer to cell culture studies appropriate? In vitro usually refers to experiments performed in the absence of any living organism or cell, e.g., biochemical reactions in a test tube.

      Accordingly, we have replaced in vitro by in cell culture when appropriate

      (A) MAIN TEXT

      (1) Introduction:

      PGRP-LC: Ramet et al, Nature 2002 reference is missing.

      "[...]epithelial repair through stem cell proliferation" is a typical disease tolerance mechanism and therefore unlikely to "[...]contribute to DETERRING ingested pathogens". In addition, is "detterring" really the appropriate word?

      The changes have been made.

      (2) Results:

      GNBP1: "and find no evidence" would read better as "and found no evidence". In addition, for GNBP3, the authors may also want to cite Mishima et al. (JBC, 2009) and possibly one on silkworm ßGRP (Takehasi et al., PNAS, 2009).

      The changes have been made.

      Wnt D: "Dif" and not "dif"=diffuse irregular facets

      The changes have been made.

      cGLR-STING pathway (Cai et al., 2022): subsequent studies indicated that cGLR ligands are RNA molecules, not DNA. Thus, whether such receptors would be able to detect naked DNA remains a remote possibility.

      We agree and have amended the text accordingly

      DSCAM1: the statement "not amenable to genetic studies" might be modulated into "not easily amenable to genetic studies" as exemplified by Dong et al. PLoS Biol, 2025 (which the authors may now add to their reference list as this article was published after submission of the current work) and all the literature on DSCAM and the Drosophila nervous system.

      We agree and have amended the text accordingly

      Psidin: "multiple papers suggest...". References are not given.

      We have amended the text and reported to the supplement. Some references have been added.

      NOS: "this study reports" should be "this study reported"; otherwise, the reader falsely believes that the authors refer to the Reprosci article. NOS expression: what about data from subsequent RNAseq studies and data from FlyCell Atlas?

      We agree with the reviewer and used the past time. For simplicity, we did not discuss Nos expression pattern.

      Eiger: the Kodra et al. reference appears to be missing in the reference list.

      The Kodra reference has been added.

      (3) Discussion:

      Third source of irreproducible claims: besides off-target effects, a limitation of the RNAi approach is that one can never be sure that a null phenotype is obtained. Thus, when obtaining negative results, it may be caused by a hypomorphic effect.

      This additional point has been added with an example that illustrates the point “Besides off-target effects, a limitation of the RNAi approach is that one can never be sure that it mimics a full null phenotype. As an example, the partial silencing of the serine protease gene Grass may explain why its role in the antifungal response was not detected using in vivo RNAi, but was revealed through the use of a null mutation (El Chamy et al., 2008; Kambris et al., 2006b)”.

      (4) Reference list:

      Cuttell et al, Gordon et al, 2005, and Melcarne et al, 2019 are duplicated.

      Thank you for noticing it. Change has been made.

      (5) Supplementary materials:

      Table S2 and S3 appear to have been interchanged.

      This has been corrected.

      Ouyang et al: BioRXiv should be indicated.

      This has been corrected.

      (B) INDIVIDUAL SUPPLEMENTS:

      (1) S1: enzymatic activity of GNBP1.

      The number of independent experiments does not appear to be mentioned. With respect to the western blot shown in Figure 2A, it seems that the intensity of the band corresponding to activated ModSP is lower in lane 1 than in other lanes. The suggestion is to scan multiple blots to quantify the activation of this protein in different conditions. Do the authors know the nature of the high mobility band that appears solely when S. aureus peptidoglycan is added?

      Regarding the lower intensity of the activated ModSP band in lane 1, a similar phenomenon has been reported in An evolutionarily conserved serine protease network mediates melanization and Toll activation in Drosophila (Fig. S2), where ModSP autoactivation was observed following incubation with PGRP-SA, GNBP1, and peptidoglycans. In current experimental design, the primary objective was to determine whether preincubation of peptidoglycans with GNBP1 further enhances ModSP activation. Therefore, our analysis focused on comparisons across different incubation time points rather than direct comparison with lane 1. Within this context, the lower intensity of the activated ModSP band in lane 1 is expected and does not affect the interpretation of the results

      In response to the suggestion of scanning multiple blots for quantification, we note that no clear enhancement of ModSP autoactivation was observed across different incubation times. We also explored alternative incubation conditions, but none resulted in a detectable increase in activation. Thus, additional quantification would not change the overall conclusion.

      (2) S2: Spirit

      It would have been nice to display the spirit mRNA levels in the KO and KD mutants. Is the catalytic domain removed by the deletion and can the authors exclude a potential expression of a truncated Spirit from a cryptic translation initiation site upon leaky Gal4 expression of the transgene, hence the need for RTqPCR data using primers that map 3' to the transposon insertion?

      We are using a deletion that remove all the Spirit isoforms that all start with the same ATG which was removed in the mutant, so it's very unlikely. There is an HSP70T = Terminator after the Gal4, which should exclude an initiation of translation after Gal4. However, we have verified the expected mutation by PCR.

      Figure 2: Crystal cells appear to be present in spirit larvae. They, however, appear to be smaller, which may be difficult to measure. Quantification of the number of crystal cells is necessary.

      We have removed this part in the revised version (Figure 2C and associated text) because it does not concern the assessed claims in Kambris et al et., 2006 that Spirit regulates the Toll pathway.

      Figure 3: It is not clear if pooled data are presented for survival experiments.

      Yes survivals show pooled data. We have updated figure legend to make this clearer.

      (3) S4: Sphinx 1/2

      In the absence of testing null mutant flies, the conclusion may be too strong. Can the authors totally exclude the expression of these proteases in a few cells? If they function as apical proteases, a minimal expression may be sufficient to trigger a proteolytic cascade.

      To address the reviewer’s comments, we generated a deletion removing both sphinx 1 and sphinx 2 and analyzed Toll pathway activity in the absence of these two serine proteases. We find that flies lacking sphinx 1 and sphinx 2 exhibit wild-type induction of Drosomycin following M. luteus infection, as well as normal survival upon E. faecalis challenge. These new data provide strong evidence supporting our claim that, in contrast to our previous report (Kambris et al., 2006), Sphinx 1 and Sphinx 2 do not regulate the Toll pathway. Accordingly, we have replaced the earlier RNAi-based results with data obtained from loss-of-function mutants.

      (4) S5: wntD

      Figure 1, if any, appears to be missing.

      Thank you for noticing this. This is now corrected Figure 2=>Figure 1 and Figure 3=> Figure

      Fig. 3C-C': please, homogenize the color code with other panels (yw in blue and not suddenly in orange)

      We have homogenized the color code in the revised version.

      (5) S6-S7: Activation of Toll by overexpression of GNBP3 or protease genes The point is not framed appropriately: the overexpression studies were not intended to determine whether the overexpression of these genes activates the Toll pathway to levels of activation encountered during infection, but as tools for epistatic analysis, and in the case of S8, to identify novel protease genes that might be involved in Toll pathway activation. The results of the epistatic analysis are not disputed and, in some cases, have been validated by independent approaches (e.g., by hemolymph transfer experiments), and the hits of the protease screen have been validated by other laboratories, namely grass and SPE. In Figure S5B of Gottar et al, Cell, 2006, a level of only 30% of immunized was achieved, whereas it was about 70% in Figure 3A. Thus, the level of induction by overexpression of GNBP3 is variable but nevertheless sufficient for epistatic analysis both for Gottar et al. and for El Chamy et al., Nat. Immunol, 2008. Furthermore, levels of activation sufficient for epistatic analysis of Toll pathway activation or stimulation of the melanization proteolytic activation cascade upon the overexpression of either GNBP3 or GNBP1 together with PGRP-SA have been reached (Gobert et al., 2003; Gottar et al. 2006; El Chamy et al, 2008; Matskevich et al., Eur. J. Immunol., 2010). Thus, the overexpression of GNBP3 functions for genetic analysis purposes in two independent teams, that however, are working in the same research Unit. While one cannot exclude that enough peptidoglycan metabolites, e.g., TCT, are provided by the microbiota, it cannot be excluded that ß-(1-3)glucans might originate from the food or mycobiota, which may be distinct from that in the Reprosci laboratory. This illustrates the difficulty of controlling all parameters.

      We fully agree that the notion that GNBP3 functions upstream of serine protease is validated. The point is that we cannot reproduce the observation that overexpression of GNBP3 trigger a strong Toll activation sufficient for epistatic analysis as shown in Gottar et al., 2006. The point is that ReproSci does not challenged any of the major claims of Gottar et al. 2006 but only a minor claim. The magnitude of gene induction relative to the unchallenged condition is an important consideration in the field of Drosophila immunity and can be misleading. For example, a gene described as being induced fivefold may appear significant, whereas the same gene can be induced up to 1,000-fold following infection. Therefore, absolute expression level compared to challenged level, rather than fold changes alone, should be carefully considered when interpreting immune gene activation.

      We have done our studies with two different constructs. The observation that overexpression of a gene activate an immune pathway is by itself a result suggesting a concentration-dependent mode of activation. For instance, overexpression of ModSP is sufficient to activate the Toll pathway (Buchon 2009). This was not the case for GNBP3, even at low level. We cannot exclude that this could be the case in a specific background but at least not all background. Over-expression of GNBP3 is used in 3 panels of Gottar 2006 and this was a significant piece of data. On my side, my lab has lost significant amount of time to reproduce this without success.

      Now we could be wrong in our assessment but we let the author of this study to show it.

      To take in consideration Reviewer’s comment, we are softened our conclusions : ‘Overexpression of GNBP3 either ubiquitously or in the fat body does not effectively activate the Toll pathway’. At most, we find similar to (El Chamy et al., 2008) that overexpression may produce ‘weak but detectable’ activation of Toll’.

      References:

      Alphabetical order is not respected (Matskevich before Kim), and the Mishima reference is not optimal: it should be the JBC article in the same year that documents also the biochemistry of binding to ß-glucans.

      We have done the changes in the revised version

      (6) S8: PGRP-LE not in hemolymph

      Fink et al., Mucosal Immunol. 2016 used the NP1-Gal4, which is not expressed in enteroendocrine cells, as stated in the text, but in enterocytes (and possibly the nervous system).

      For controls, is the wild-type control the w[iso] Drosdel background?

      Please provide the supplier of the GFP antibody.

      We have addressed all the points in the revised version.

      (7) S9: PGRP-LE and melanization

      Figure 1D-E: A quantification would bolster the claim.

      We agree that quantification of Figure 1D-E would reinforce the claims but we believe that our data are sufficient to state that PGRP-LE does not block the cuticular melanization upon septic injury (which is also consistent with an intracellular role). We have softened our conclusion.

      (8) S10: PGRP-LE and bacillus

      Please provide a description of the Bacillus subtilis strain.

      This is a strain that derived from the Jean Lambert collection of Strasbourg and used in Lemaitre B PNAS 1997 (J.Millet and A. Klier, Pasteur Institute of Paris). We have checked the strain and confirm that it was indeed a B. subtilis strain that we name B subtillis FS.

      It is not clear from the Mat & Meth whether the 2-3 independent replicates per genotype represent biological replicates in one experiment or correspond to several independent experiments. Are the pooled data displayed?

      This information was on the methods. It has been copied to the figure caption.

      (9) S11: DNAse II and regulation of AMP genes

      The exact larval stage is not provided in S11, nor in the original study.

      The experiment was done on wandering third-instar larvae as indicated in the material and methods

      The number of flies for survival experiments is rather low, but this is not a major issue given the outcome of the experiment.

      We agree with the reviewer.

      What is the concentration of the injected DNA? As the solution was likely viscous, was the DNA sheared?

      We have used a concentration of DNA of: 200 ng/ul, which is now indicated in the revised version of the Supplement. DNA was no sheared.

      Figure 1A&D: A positive control of immunization would have been nice. 1D: At which time point was Diptericin expression measured by RTqPCR?

      Unchallenged flies were used in Figure 1A while in Figure 1D Diptericin was measured 6 h after challenged. We agree that a bacterial challenge control would have been nice, but clearly the level of Diptericin in 1A corresponds to levels observed in unchallenged flies. Of note, we have tried several different concentrations, of more or less long "sizes" of DNA (short or very long fragments), and also different DNA sources (E. coli or Drosophila) but we did not see any effect on the activation of the Imd pathway.

      DNAseII-deficient larvae have wild-type hemocyte numbers. His sub-title is not accurate as Figure 3 actually reports an INCREASED number of hemocytes in the DNase II mutant.

      The reviewer is correct and we have adjusted the text.

      (10) S12: JNK pathway and AMP gene expression

      Hep RNAi lines and possibly also the Bsk-DN line should be validated by monitoring puckered mRNA levels after a stress that activates the JNK pathway. The absence of this control weakens the Reprosci conclusions.

      As stated above, we are using standard Hep-RNAi and BskDN fly tools that have been validated in many studies.

      Articles validating the HepRNAi (BDSC35210) can be found on this link. We have also validated the RNAi in new Figure 1 of Supplement S12.

      Articles validating the BskDN (BDSC6409) can be found on this link

      The Bloomington number of Hep RNAi was miss-annotated and has been corrected in the revised version

      (11) S13: Caspar

      There is clearly a trend for improved survival of the Caspar mutant in Figure 1A. Please, show the pooled data and appropriate statistical analysis. The legend to 1A mentions one overexpression strain that is not displayed and has likely not been performed because loft experiments were performed at 25{degree sign}C, whereas OE experiments should be performed at 29{degree sign}C, hence in separate experiments.

      There was a mistake in the original figure legend when we mentioned the impact of overexpression of caspar on survival without showing the data (no effect was observed). The text has been removed in the revised version because it is not related to the claims we assessed from the Caspar article (Kim et al.,2006). To addressed reviewer’s comments, we now present the pooled data in Figure 1 of the revised Supplement S13. The conclusion is that we do not observe any increase host survival in caspar mutant related to wild-type consistent with our observation that the Imd pathway is not strikingly over-activated in absence of infection in caspar loss-of-function mutants.

      Why was the c729-Gal4 driver chosen? Has it been validated as a bona fide fat body driver?

      The use of c729-Gal4 was suggested by, and borrowed from, the laboratory of Prof. Gaiti Hasan, who had characterized and used it in adult fat body experiments (Subramanian M et al., 2013, Dis. Mod. & Mech). The BDSC number for the corresponding stock is BDSC_6983. Based on Flybase data, it is also expressed in somatic cells of male/female reproductive systems in the adult.

      The RTqPCR experiments are not overwhelmingly convincing for a lack of data points: pooled data should be shown, inasmuch as there is a significant difference upon Caspar OE 6h after Ecc15 challenge.

      We now show in the revised version of the Supplement S13 the pooled data from different experiments with individual points shown.

      In conclusion and although our results are variable, they do not reproduce the results produced in the original article by (Kim et al., 2006) According to our results, we observe:

      (1) no increase Dpt expression in absence of challenge both in caspar deficient larvae and adults.

      (2) A possible inhibition of Dpt upon over-expression caspar at 6h in adult.

      - A possible increased Dpt expression in caspar loss of function mutant larvae upon challenge.

      The later may suggest an inhibition role upon overexpression of caspar that required further analysis. The text of the supplement has been amended to take all those points in consideration.

      (12) S15: listericin

      Introduction: The LLO (also referred to as hly) L. monocytogenes mutant does not prevent the entry of Listeria inside cells. The pore-forming toxin listeriolysin is required for pathogen escape from the phagosome.

      There is no reference to LLO in the introduction of the S15 listericin section.

      Has the STAT-92E RNAi line been validated? It is difficult to draw a definitive conclusion on the absence of the role of the JAK-STAT pathway in adults using an RNAi transgene because it may only imperfectly silence the expression of the target gene. "Contrary to Goto et al.2010, in our hands reduction of JAK-STAT activity through RNAi [...] in adult flies": Goto et al. apparently tested the JAK-STAT pathway only in S2 cells. This statement should therefore be modulated accordingly.

      We have validated the STAT92 RNA in the revised version by confirming that Turandot gene expression is reduced in this mutant (Supplement 15 Figure 2 C-D). We have also validated the PGRP-LE<sup>112</sup> null mutant (Supplement 15 Figure 1C).

      We have adjusted the conclusion: “Contrary to (Goto et al., 2010), we find that Listericin expression is not specifically dependent on PGRP-LE, and is not dependent on JAK-STAT signaling in flies. Of note, this could be the case in S2 cells where the initial experiments were done.

      Antibacterial effects of listericin: It would be cautious not to rely solely on survival experiments, but also to monitor the bacterial titer to draw a definitive conclusion (assay used by Goto et al.). A control overexpressing GFP or a non-relevant peptide would have been welcome to control for potential metabolic effects that would decrease the effect of the overexpression. More importantly, Goto et al. used a Cg-Gal4 driver that is also expressed in hemocytes, which is likely not the case for the Lpp driver. Is it known if the c564 driver is also expressed in hemocytes and to the same level as the Cg-Gal4 driver?

      We have used two fat body drivers to overexpress Listerin, Lpp and C564, the latter being expressed in hemocytes indeed. We agree that bacterial counting would provide a sensitive assay but in absence of any protective effect of Listericin overexpression, we do not expect any major titer change in L. monocytogenes growth. To reinforce our conclusion, we have generated Listericin null mutations (Fig 4C) and we have shown that they are not more susceptible than the wild-type to L. monocytogenes.

      (13) S16: DSCAM1

      The authors use an RNAi construct to knock down DSCAM1 expression. Which part of the transcripts is targeted? Did the authors verify that silencing was effective and would affect all DSCAM transcripts?

      The DScam RNAI (BDSC #38945) that we are using has been used in other articles (link) and is validated in Kamiyama et al., Dev cell (Figure S4).

      Data points should be shown in the figure.

      Unfortunately, we could not address this point to the difficulty to reach the collaborator who provided the data.

      Their conclusions would be strengthened by directly testing opsonization using the assay developed by Haller et al., EMBO Reports, 2018. Also, to derive the phagocytic index, the authors must have counted the number of hemocytes retrieved from bled larvae? Was there a decrease when DSCAM1 was silenced in hemocytes? The use of a hml-Gal4-Gal80ts driver would have allowed to bypass the issue of developmental effects.

      We expect an opsonin to be abundant in the hemolymph but we did not find any secreted form of dScam in our proteomics analyses (Rommelaere 2024). 20 years after the publication of this landmark article in Science, the absence of any confirmation is puzzling and we are reluctant to do any additional experiment taking into consideration that phagocytosis assays are often variable.

      (14) S18: SR-CI

      The major issue with this supplement has been dealt with in the Public Review: no phagocytic receptor function was claimed in the Ramet et al, 2001 study.

      We fully agree with the reviewer and with Mika Rämet and Monty Krieger (personal communication), and we apologize for this misunderstanding. In fact, Rämet et al. (2001) did not present data demonstrating a role for Sr-CI in phagocytosis per se in his article, but rather showed that this receptor is involved in bacterial binding. Our confusion arose from a subtitle in the Results section of their article (“SR-CI Binds Both Gram-Positive and Gram-Negative Bacteria and Is Necessary for Optimal Phagocytosis by S2 Cells”) and the article title that claim that Sr-CI is a pattern recognition receptor, which does not reflect the content of the article.

      To clarify this point, we have revisited the original claim. Consistent with Rämet et al. (2001), we now observe a defect in hemocyte binding to bacteria in Sr-CI mutants. Thus, we validate the claim. Because Sr-CI is often assumed to function as a phagocytic receptor, we have also retained the experiments showing that it is not essential for the phagocytosis of E. coli or S. aureus. All experiments have been repeated during the revision process using a null single mutation and a double mutant removing both Sr-CI and Sr-CIII.

      Introduction: Is it really adequate to mention a phagocytic receptor for a ligand, dsRNA, that gets endocytosed?

      In the introduction, we summarized what is known on the Sr-CI, including its implication in the uptake of dsRNA. As suggested by the reviewer, we used the term endocytosis to refer to the ability to uptake dsRNA.

      Methods: Have the authors excluded the potential off-target effect of CRISPR-Cas9 in other scavenger receptor genes? Monitoring their expression levels would also allow the detection of any compensatory effect in the null mutant by overexpression of other scavenger receptors.

      We are now using two mutant lines: one carrying a frameshift mutation (SK6) that specifically affects Sr-CI, and another with a deletion removing both Sr-CI and Sr-CIII. We have carefully validated both mutations by genomic sequencing. As our results are now consistent with the original findings of Rämet et al. (2001), we believe that the analyses presented in the Supplementary Information are genetically well supported.

      Results: Figure 1 is really confusing with so much variability in the data, which raises doubts about the reliability of the method. The reduction of the phagocytic index in B is not "mild". Again, one would like to see the individual data points and to know what the error bars are. For 1G, has any statistical analysis been performed? Finally, Panels A to G lack homogeneity in their presentation. Also, why are the absolute values of the y-axis varying so much from panel to panel (A-B vs C-D; E vs. F)?

      We have repeated our experiments using a new set of mutants, both generated in the isogenic DrosDel background. In the revised version, we include additional experiments assessing the contribution of Sr-CI to hemocyte binding to bacteria. Consistent with the original report by Rämet et al. (2001), we observe similar results. We have revised the text accordingly and moderated our claims. In addition, we performed further biological replicates and now provide appropriate statistical analyses.

      (15) S19: Undertaker

      Undertaker has been identified through a deficiency screen that restricted the genomic zone of interest to eight genes. RNAi was then used to identify the candidate gene as being Undertaker. While an off-target effect of RNAi cannot be excluded, it cannot account for the results of the deficiency screen (junctophilin is on the second chromosome, whereas undertaker is on the third). The deficiency phenotype could be rescued by an Undertaker transgene. While overexpression can indeed provide a rescuing activity due to high levels of ectopic expression, why would it do so in the context of an 82F deficiency, unless this deficiency carries a second site mutation, which is a rather remote possibility.

      Given that the deficiency line deletes at least 14 genes in a cluster, several of which are involved in growth and development, we assume that another gene(s) within the span of this deficiency is responsible for the effect on efferocytosis, or that some other mutation in the uncontrolled genetic background is responsible. The impact of Df(3R)3-4 on efferocytosis remains to be investigated.

      The authors claim that Undertaker is not expressed at the right embryonic stage and hardly in S2 cells, which is correct according to large-scale data. However, Cuttell et al. successfully stained S2 cells with an antibody raised against retinophilin/undertaker by the investigators who studied the role of this gene in the eye (Mecklenburg et al., 2007). Should we trust more largescale datasets based on transcriptomics or a specially developed tool? (Both junctophilin and undertaker are at the limit of detection of the proteomic data available on FlyBase; equivalent signals in hemocytes were measured in FlyCellAtlas). Thus, the argument of the absence of expression is not definitive.

      We agree on this but the expression pattern is an additional element that reinforce our conclusion. This is not the key element that relies on the use of loss-of-function mutation. Another element is the absence of follow-up study in the last 18 years.

      The new phagocytosis data set generated by Reprosci shows an absence of impact of the undertaker loft mutation in larval hemocytes. Whether these data can be extrapolated to S2 cells, embryonic or adult hemocytes, remains debatable, as are the explanations put forth by Reprosci in their conclusion to explain by a possible off-target effect of RNAi on junctophilin. It would be interesting to determine the phenotype of junctophilin mutants in the ex vivo larval hemocyte assay.

      We have analyzed the role of Undertaker using third instar larvae in an ex vivo assay and did not find any role in efferocytosis. I think that all our data and analysis of the literature is consistent with our statement that’ that undertaker is unlikely to have a role in phagocytosis’. Now, we can never exclude that Undertake may play a subtle role in this process. The role of Draper has been observed in larval hemocyte that represent macrophage of flies. We are using a null mutation in undertaker preventing the existence of off-targets. We have nuanced our conclusion in the article and add a sentence in the conclusion of the supplement: ‘We cannot however exclude that Undertaker play a role at a specific stage of development that we did not assess.’

      (16) S20: Psidin

      This supplement is duplicated

      The duplicated supplement has been removed.

      Phagocytosis assay: the authors use E. coli-GFP. How can they discriminate between internalization and simple binding at the surface of hemocytes? It would have been more appropriate to use a phalloidin, stained to another color rather than green. The suggestion here is to first use FITC-labeled bacteria, followed by Trypan blue treatment to quench the fluorescence of noninternalized bacteria. Second, pHrodo bacteria could be used to monitor the acidification of the phagosome in wt and psidin hemocytes.

      We agree with the reviewer that this would be better. Because our observations are consistent with the data reported in this original article, we did not feel inclined to extend our analysis.

      (17) S21: Hemese

      The pie charts in Figure 1 would benefit from a statistical analysis. Why do the encapsulated eggs appear to be much larger in the hemese mutant? Could it be that more lamellocytes are recruited and make a thicker capsule? Should Figure 1C be imperatively quantified?

      To extent our analysis, we generated two new Hemese null mutants, Hemese<sup>JP187</sup> and Hemese<sup>JP828</sup>, carrying deletions in the central region of the gene. Using these lines, we show that wild-type and <sup>Hemese</sup> mutant larvae display comparable levels of lamellocytes and similar numbers of melanized capsules following wasp infestation. We further quantified lamellocyte differentiation and included appropriate statistical analyses. We have removed the previous results obtained with the Hemese<sup>SK2</sup> mutant, which yielded similar observations. By reproducing our previous findings with independent mutant lines and by providing quantitative analyses, we strengthen our conclusion that Hemese does not act as a negative regulator of lamellocyte differentiation upon wasp infestation.

      (18) S22 IRC

      IRC is actually not a catalase but a heme peroxidase. For the experiments on C. albicans, can the authors exclude that the IRC flies succumb because they are more sensitive to ethanol than wt or spz flies (sucrose is fermented by C. albicans): a control would be to use glycerol (nonfermentable) instead of sucrose solution.

      We thank the reviewer and Carolina Barillas (personal communication) to inform us that IRC is not a catalase but an heme peroxidase. This is now included in the article and the supplement. It is clear that the name IRC for immune regulated catalase is misleading. We cannot exclude that the IRC flies succumb because they are more sensitive to ethanol than wt or spz flies but we did not test this interesting idea during the revision.

      Do IRC mutants succumb to the ingestion of killed bacteria?

      No, they get stuck in fly food and die.

      (19) S23 DUOX

      Introduction: When citing Kumar et al., the authors might also want to cite Bai et al. on the Bactrocera dorsalis peritrophic matrix.

      This reference has been added

      Results:

      Figure 1: any statistical analysis? Data points are not shown for the lef panel, and error bars are not defined.

      We have added in the revised version ‘When using the Mann-Whitney U test, we still observed a statistically significant difference in CFU counts at 6 hpi in Figure 2B, as well as at both 6 hpi and 24 hpi in Figure 2F. However, the magnitude of these differences is relatively small’. Error bars have been defined in the general revision of the supplements (see above).

      Figure 2A shows only a limited reduction in Duox expression at the transcriptional level. "successfully" might be a bit of an overstatement.

      We have removed the term ‘successfully’.

      Figure 2E is too small.

      We have increased the size of Figure 2E.

      The authors might want to discuss the role of Duox in enterocytes destined to die as described by Amchelavsky et al., Cell Reports, 2020.

      Good point, we have discussed this reference in the revised version.

      The Sajjadian reference is incomplete.

      The reference has been completed

      (20) S24: NOS

      Maybe the work from the Royet laboratory could be cited along with that of Neyen et al. and Zaidmann-Remy et al. in the Introduction.

      Good points. We have added two references related to the work of the Royet lab (Bosco-Drayon et al., 2012; Charroux et al., 2017).

      It is not clear from Rabinovich et al. (2016) which line should be the relevant wild-type control. Why use w[1118] in Figure 1 and Ore-R in Figure 2? A more definitive conclusion could be reached upon isogenization or testing a second null mutant in homozygous and transheterozygous conditions?

      We agree that ideally, we should have used isogenic wild-type control but in absence of any effect of NOS mutants, we consider that the use of w[1118] and Oregon wild-type control is acceptable, considering that they behave similarly in the assay we have used.

      (21) S25 eiger survival

      Survival experiments: Are pooled data shown? Have the authors monitored the health status of their fly lines? In some of the survivals with late phenotypes, e.g., egr mutants and E. faecalis, this may be an issue, inasmuch as noninfected or mock-infected controls are not shown (have they been performed?).

      The survival analysis showed the pooled of 40 flies and were often done with two sexes. They also include many controls. We cannot never exclude minor effects at late time points, but the critical message is that we cannot reproduced the previously published results.

      The survival graphs are difficult to analyze: the authors should definitely avoid light colors such as yellow that do not show up well in a white background.

      As stated above, these experiments were done by many scientists in different lab and it was difficult to homogenize the data. Therefore, we did not modify our graphs although we agree with the reviewers. We believe that line patterns and contrast differences between groups guarantee that the readers can still assess the data.

      (22) S27: eiger humoral response

      Introduction: Have the authors also checked the Flysickseq data from the Buchon lab?

      There is no induction of eiger in Flysick. This information along with the reference Troha et al., have been added to S27.

      Methods: Have the RNAi lines been validated, and how? Is one more efficient at silencing than the other? This set of data would complement Figure 1 with RTqPCR experiments.

      The two RNAi lines we are using have already been used in many studies assessing the function of eiger ((#108814, reference here, #45253 reference here)

      Figure 3 colors in survival graphs: see S25.

      We did not modify our graphs although we agree with the reviewers. By increasing the magnification, the readers can still assess the data. As stated above, these experiments were done by many scientists in different labs and it was difficult to homogenize the data.

      Would it have been worth to also test the transheterozygous Gr28b mutants to avoid any issue of second-site mutations?

      We could have extended the genetics approach but, given that both us and another group (Sang) found no effect on feeding in an independent mutant, and extremely high feeding in the claimed 'anorexic' mutant, this would not be relevant to the claim. Future study may tell us if Gr28b has clearly a feeding phenotype.

      Reviewer #2 (Recommendations for the authors):

      (1) Adjust the discussion to better contextualize subjectivity: Because the choice of claims and papers inevitably involves subjective decisions, consider expanding the discussion to acknowledge this limitation more explicitly and explain how the companion metascience manuscript complements this work.

      We have added a section at the end of the discussion to discuss the limitation of our study and we establish more link to the companion article.

      (2) Refine language and avoid binary judgments: Terms such as "correct," "incorrect," or similar definitive formulations should be softened. Emphasizing uncertainty and openness to future revision will better reflect the iterative nature of scientific inquiry.

      We are softening our language in several of our assessment to avoid binary judgement.

      (3) Highlight reproducible findings as well: While the focus on irreproducible or challenged claims is understandable, it may be helpful to balance this by more clearly acknowledging wellsupported claims or areas of strong reproducibility to reinforce the positive impact of robust findings.

      We have added two sentences at the end of the introduction and at the beginning of the discussion that most claims are reproducible and that we have focused here on nonreproducible claim.

      (4) Clarify how the community can engage with the dataset: Because you provide extensive supplementary material and a large online resource, consider adding more explicit guidance on how researchers can contribute comments, evidence, or corrections, and how these contributions will be integrated.

      This point is already addressed in the revised sentence: “We hope that the community-accessible website will encourage researchers to share their perspectives and contribute data from diverse sources, thereby improving objectivity.” In addition, we have proactively engaged with principal investigators to motivate them to contribute to this effort by sharing unpublished results and information. However, it remains unclear to what extent scientists are genuinely interested in reproducibility, as has been noted in other studies on the topic. For example, articles that challenge previous findings are often under-cited, and the presence of contradictory evidence does not necessarily prevent researchers from continuing to cite the original claims. This is clearly a challenge of reproducibility study. Comments, evidence and corrections will be integrated in the ReproSci website. We have already updated this database when revising this article and will continue to do it.

      (5) Resolve the date-range inconsistency: The Introduction mentions analysis of papers from 1959-2011, whereas the Methods section cites 1940-2011. This discrepancy should be corrected for consistency.

      We have solved this discrepancy by correcting the method section. This should be 1959-2011. Thank you for spotting this mistake.

      Reviewer #4 (Recommendations for the authors):

      (1) The "disclaimer" subsection should be incorporated into the Introduction, as it is central to the premise of the study.

      The disclaimer has been moved at the end of the introduction and one sentence has been added in the abstract.

      (2) The inconsistency of graphical representation and statistical analysis of survival and gene expression data across different supplements is distracting and makes the project feel cobbled together. A consistent and unified framework for analysis and presentation would feel more cohesive and rigorous.

      The experiments were conducted across multiple laboratories and required substantial coordination. As a result, modifying the graphs at this stage would be technically complex and would require monumental effort for a tiny return. Therefore, we regret that we were unable to implement this change. The most important is that data and analyses are presented transparently, allowing readers to evaluate and interpret the results independently.

      (3) The purported roles of eiger and Gr28b in immunity have nothing to do with each other, aside from both having been published by David Schneider's group. I would suggest not combining them into a single section unless there is to be a 'miscellaneous' section that contains work by multiple groups.

      We have done two separate sections.

      (4) It would be easier to comment on specific passages in the manuscript if line numbers had been included.

      Sorry for this. We have included number of lines in the revised version.

      (5) The use of the word "elegant" to describe melanization reactions on page 3 is a bit odd and feels out of place.

      It has been removed

      (6) The sentence "We conclude that PGRP-LE is an exclusively intracellular sensor, with a prominent role regulating the gut immune response (Bosco-Drayon et al., 2012; Neyen et al., 2012)" should be edited to read "as reported in (citations)".

      We have edited the sentence.

      (7) The sentence "Experiments performed for ReproSci and review of the literature suggest that JNK is unlikely to have a strong direct or systematic role in the regulation of Drosophila AMPs in vivo, and is not required in the adult fat body for AMP expression in response to infection (Supplementary S12)" lacks detail. I realize that the experiments are described in S12, but I would suggest a brief summary in the main text of the article as well.

      We have provided more information in the article.

      (8) The phrasing of "While many of the challenged claims discussed in this paper are known to be controversial by experts, or have fallen quietly out of current research interests, some are still a source of confusion. This is particularly true for young scientists new to the field of Drosophila immunity or scientists with primary interests outside of Drosophila immunity that use the field as a reference." could be edited for clarity. A more direct phrasing could help, such as "Even in the absence of published refutation, many of the challenged claims were already considered controversial by experts in the field. Others have quietly fallen out of the general current research interest. These may nevertheless still be a source of confusion for young scientists new to the field of Drosophila immunity or scientists with primary interests outside of Drosophila immunity that use the field as a reference."

      We have changed the sentence accordingly.

      (9) On Discussion page 15, the comma should be removed from "In this article we have not discussed a number of claims, that had no clear follow-up studies and remain unchallenged."

      The coma has been removed.

      (10) In Methods, the authors "acknowledge that our verification experiments could also be erroneous". It would be appropriate to also include such a disclaimer in the Introduction and/or Discussion.

      The disclaimer has been moved at the end of the introduction and one sentence has been added in the abstract.

    1. Author response:

      The following is the authors’ response to the original reviews.

      eLife Assessment:

      This important study presents an impressive large-scale effort to assess the reproducibility of published findings in the field of Drosophila immunity. The authors analyse 400 papers published between 1959 and 2011, and assess how many of the claims in these papers have been tested in subsequent publications. In a companion article they report the results of experiments to test a subset of the claims that, according to the literature, have not been tested. The present article also explores if various factors related to authors, institutions and journals influence reproducibility in this field. The evidence supporting the claims is solid, but there is considerable scope for strengthening and extending the analysis. The limitations inherent to evaluating reproducibility based on the published literature should also be acknowledged.

      We have included in the abstract the limitation of evaluating replicability based on the published literature

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      The authors set out on the ambitious task of establishing the reproducibility of claims from the Drosophila immunity literature. Starting out from a corpus of 400 articles from 1959 and 2011, the authors sought to determine whether their claims were confirmed or contradicted by previous or subsequent publications. Additionally, they actively sought to replicate a subset of the claims for which no previous replications were available (although this set was not representative of the whole sample, as the authors focused on suspicious and/or easily testable claims). The focus of the article is on inferential reproducibility; thus, methods don't necessarily map exactly to the original ones.

      The authors present a large-scale analysis of the individual replication findings, which are presented in a companion article (Westlake et al., 2025. DOI 10.1101/2025.07.07.663442). In their retrospective analysis of reproducibility, the authors find that 61% of the original claims were verified by the literature, 7.5% were partialy verified, and only 6.8% were challenged, with 23.8% having no replication available. This is in stark contrast with the result of their prospective replications, in which only 16% of claims were successfully reproduced. The authors proceed to investigate correlates of replicability, with the most consistent finding being that findings stemming from higher-ranked universities (and possibly from very high impact journals) were more likely to be challenged.

      Strengths:

      (1) The work presents a large-scale, in-depth analysis of a particular field of science that includes authors with deep domain expertise of the field. This is a rare endeavour to establish the reproducibility of a particular subfield of science, and I'd argue that we need many more of these in different areas.

      (2) The project was built on a collaborative basis (https://ReproSci.epfl.ch/), using an online database (https://ReproSci.epfl.ch/), which was used to organize the annotations and comments of the community about the claims. The website remains online and can be a valuable resource to the Drosophila immunity community.

      (3) Data and code are shared in the authors' GitHub repository, with a Jupyter notebook available to reproduce the results.

      We thank the reviewer for their positive comments.

      Main concerns:

      (1) Although the authors claim that "Drosophila immunity claims are mostly replicable", this conclusion is strictly based on the retrospective analysis - in which around 84% of the claims for which a published verification attempt was found. This is in very stark contrast with the findings that the authors replicate prospectively, of which only 16% are verified. Although this large discrepancy may be explained by the fact that the authors focused on unchallenged and suspicious claims (which seems to be their preferred explanation), an alternative hypothesis is that there is a large amount of confirmation bias in the Drosophila immunity literature, either because attempts to replicate previous findings tend to reach similar results due to researcher bias, or because results that validate previous findings are more likely to be published.

      Both explanations are plausible (and, not being an expert in the field, I'd have a hard time estimating their relative probability), and in the absence of prospective replication of a systematic sample of claims - which could determine whether the replication rate for a random sample of claims is as high as that observed in the literature -, both should be considered in the manuscript.

      I still believe that most of ‘verified’ claims are indeed solid, consistent with the feeling of increased knowledge in the Drosophila immunity. Of note, when I started in the field in the early 90, nearly all the articles in Drosophila developmental biology, the dominant field at that time, were solid. I agree that this may represent a past period. Still, perceived irreproducibility is high because affecting claims published in high-impact articles. To address the reviewer’s comments, we have included the possibility of confirmation bias in the discussion of the article.

      (2) The fact that the analysis of factors correlating with reproducibility includes both prospective and retrospective replications also leads to the possibility of confusion bias in this analysis. If most of the challenged claims come from the authors' prospective replications, while most of the verified ones come from those that were replicated by the literature, it becomes unclear whether the identified factors are correlated with actual reproducibility of the claims or with the likelihood that a given claim will be tested by other authors and that this replication will be published.

      We agree that the ReproSci is a human biased endeavor and may be subjected to bias, notably the one mentioned. Some verified claims might be considered as challenged and some challenged claims as verified. But this is likely not affecting most of our results. Our papers have been posted on a public archive and that the community could scrutinize our data (most authors have checked their claims!). Based on community feedback, we have had to change the status of three claims only: one verified claim became challenged, one challenged claim became unchallenged and one unchallenged became verified. We therefore did not expect major changes in our conclusions. We have provided an estimation of irreproducibility ranging from 10-20% and we believe this is a rather safe interval. This is still significant. The fact that the ReproSci project is a human endeavor, and therefore subject to inherent limitations, is already emphasized in the last section of the discussion.

      (3) The methods are very brief for a project of this size, and many of the aspects in determining whether claims were conceptually replicated and how replications were set up are missing.

      Some of these - such as the PubMed search string for the publications and a better description of the annotation process - are described in the companion article, but this could be more explicitly stated. Others, however, remain obscure. Statements such as "Claims were cross-checked with evidence from previous, contemporary and subsequent publications and assigned a verification category" summarize a very complex process for which more detail should be given - in particular because what constitutes inferential reproducibility is not a self-evident concept. And although I appreciate that what constitutes a replication is ultimately a case-by-case decision, a general description of the guidelines used by the authors to determine this should be provided. As these processes were done by one author and reviewed by another, it would also be useful to know the agreement rates between them to have a general sense of how reproducible the annotation process might be.

      The same gap in methods descriptions holds for the prospective replications. How were labs selected, how were experimental protocols developed, and how was the validity of the experiments as a conceptual replication assessed? I understand that providing the methods for each individual replication is beyond the scope of the article, but a general description of how they were developed would be important.

      We have extended the first section of the Result to mention that an extended Material and Methods can be found in the complementary article Westlake et al., eLife 2026 and on the ReproSci website indicated the resources described in the companion articles. Disagreement between the two authors were limited and mostly dealt with textual interpretation (the definition of the major claims, which can affect if they are verified or not). As mentioned above, our articles are now public since more 6 months and we got little request to change the status of a claim (only 3 over more than 1000). Of note many claims from some ancient articles are part of the common knowledge, are verified routinely by many labs in the field, and therefore were easy to categorize.

      We also added a sentence to also underline that the scientific value of an article does not fully correlate with its status. A number of problematic articles filled with exaggeration or confused claims were still categorized as verified. Thus, we screen for replicability but they are many other publication issues we could not capture in our study. This point is now mentioned in the discussion.

      (4) As far as I could tell, the large-scale analysis of the replication results was not preregistered, and many decisions seem somewhat ad hoc. In particular, the categorization of journals (e.g. low impact, high impact, "trophy") and universities (e.g. top 50, 51-100, 101+) relies on arbitrary thresholds, and it is unclear how much the results are dependent on these decisions, as no sensitivity analyses are provided.

      Particularly, for analyses that correlate reproducibility with continuous variable (such as year of publication, impact factor or university ranking, I'd strongly favor using these variables as continuous variables in the analysis (e.g. using logistic regression) rather than performing pairwise comparisons between categories determined by arbitrary cutoffs. This would not only reduce the impact of arbitrary thresholds in the analysis, but would also increase statistical power in the univariate analyses (as the whole sample can be used in at once) and reduce the number of parameters in the multivariate model (as they will be included as a single variable rather than multiple dummy variables when there are more than two categories).

      We did not pre-registered our study, which is quite different from other reproducibility projects. We did not know at the start how the project would unfold. Of note, I believe that ‘cleaning’ an extensive field by experts was by itself an achievement and represent another way to assess replicability, with its own limitation.

      We agree that the cut-off can be seen as arbitrary. However, publication year has been modeled as a continuous variable through a spline (to allow for non-linearity) in the multivariate analysis. For journal and institutional ranking, we would like to defend and keep the categorical specifications in the main text for two reasons:

      - Institution ranking: For institutional ranking, the largest institutional category is “Not Ranked” which we cannot assign a rank and ranks institutions individually only through the top 100. Below that it publishes bands (101-150, 151-200, 201-300, 301400, 401-500) of variable width, which are not straightforward to use continuously without making strong assumptions (e.g midpoint) unsupported by the data.

      - Prestige: As mentioned by another reviewer there are career consequences attached to Nature, Science and Cell that are different from other journal, and the effect of moving from a journal from an IF 3 to 8 is different than from 30 to 35. We provide a sensitivity analysis in the supplementary information where we refit the multivariate model with log-transformed impact factor continuous predictor. We obtain very similar results than these in the main text, with the exception that the impact factor of the journal becomes significant. We describe and discuss this results in the supplementary information (section S5), while justifying why we keep the categorical model in the main text.

      We are grateful to the reviewer for prompting these additions, which we agree strengthen the paper.

      The text added in the SI states:

      “As a sensitivity analysis, we refitted the multivariable hierarchical logistic model by replacing journal-impact-factor categories with log₂-transformed continuous impact factor, while retaining all other covariates and random intercepts from the primary analysis. University ranking was retained as a categorical variable because the 2010 Shanghai Academic Ranking reports individual ranks only for institutions ranked 1– 100 and otherwise reports rank bands (101–150, 151–200, 201–300, 301–400, and 401–500); moreover, 441 of 1,006 claims (43.8%) were from unranked institutions, which constitute a distinct group.

      Each doubling of journal impact factor was associated with 1.51-fold higher odds that a claim was challenged (OR 1.51, 94% HDI 1.13–2.08). At the mean impact factors of the low-impact and trophy-journal tiers (4.4 and 61, respectively; approximately 3.8 doublings), the continuous model implies a trophy-versus-low-impact odds ratio of approximately 4.8. By contrast, the primary model directly estimated the trophy-versus-low-impact odds ratio as 1.75 (94% HDI 0.59–4.91). Although this wide interval includes 4.8, the point estimates differ between the two models. We interpret the larger implied trophy-journal effect in the continuous model cautiously because it assumes that the log-linear slope estimated predominantly from the many journals with lower impact factors (around 2–12) applies unchanged to the sparsely represented trophy journals (62 claims across Science, Nature, and Cell). We therefore retained the categorical journal analysis as the primary analysis because it directly estimates the trophy-journal comparison using claims published in those journals. Estimates for all other covariates were broadly similar to those in the primary model. In particular, the association with Top 50 university affiliation remained evident (OR 4.04, 94% HDI 1.57–10.08, compared with OR 3.68, 94% HDI 1.50–9.28 in the primary model)”.

      [This response is referred later as “Response to categorical variable encoding”]

      (5) The multivariate model used to investigate predictors of replicability includes unchallenged claims along with verified ones in the outcome, which seems like an odd decision. If the intention is to analyze which factors are correlated with reproducibility, it would make more sense to remove the unchallenged findings, as these are likely uninformative in this sense. In fact, based on the authors' own replications of unchallenged findings, they may be more likely to belong the "challenged" category than to the "unchallenged" one if they were to be verified.

      We thank the reviewer for raising this comment, we agree that the classification of the unchallenged claims as not challenged is difficult given their nature. We refitted the multivariable analysis excluding unchallenged claims, with a classification of Challenged and Unchallenged (Verified, Partially Verified, Mixed). The results are shown in the supplementary section S4 and are extremely similar to the main model.

      The text added in the SI states:

      “We fit the multivariate model from the main text while excluding unchallenged claims from the analysis. The methods are similar and the convergence and diagnosis checks are good and not reported here for brevity. The model simultaneously adjusts for author demographics, laboratory attributes and journal or institutional prestige and predict a binary outcome for each claim: challenged or not challenged (including Verified, Partially Verified, Mixed). The re-analysis included 659 claims, of which 60 (9.1%) were challenged. The non-challenged reference group comprised of Verified (n=525), Partially Verified (n=64), Mixed (n=10). The Adjusted odds ratios and 94% highest-density intervals are reported in Figure S4. The results are very similar to the analysis with the unchallenged claims in the main text, with only university ranking (Top 50) being a significant predictor (OR 3.34 (1.28–9.01) vs the main text OR 3.68 (94% HDI 1.50– 9.28). The other variable with the biggest changes shows only modest differences:

      - High-impact journal OR 1.12 (vs 1.31)

      - Trophy journal OR 1.47 (vs 1.75)

      - Post-doc OR 1.44 (vs 1.16) and their intervals still include 1. Note that the excluding unchallenged decision condition on follow-up, which is not random and might be influenced by our key variable (journal tier, institutional ranking) and bias results for this model.”

      However, we did not replace the main model of the article by this particular model because when you chose only claim that are either verified or challenged (so you exclude unchallenged), the condition that made these claims included in this analysis could be influenced by a cofactor, so our odds ratios might be wrong.

      [This response is referred later as “Response to unchallenged exclusion”]

      Reviewer #2 (Public review):

      Summary:

      Lemaitre et al. conducted an analysis of 400 publications in the Drosophila immunity field (1959-2011), performing both univariable and multivariable analyses to identify factors that correlate with or influence the irreproducibility of scientific claims. Some of the findings are unexpected, for instance, neither the career stage of the PI nor that of the first author appears to matter that much, while others, such as the influence of institutional prestige or publication in "trophy journals," are more predictable. The results provide valuable insight into patterns of irreproducibility in academia and may help inform policies to improve research reproducibility in the field.

      Strengths:

      This study is based on a large, manually curated dataset, complemented by a companion paper (Westlake et al., 2025. DOI 10.1101/2025.07.07.663442) that provides additional details on experimentally documented cases. The statistical methods are appropriate, and the findings are both important and informative. The results are clearly presented and supported by accessible documentation through the ReproSci project.

      We thank the reviewer for their assessment.

      Weaknesses:

      The analysis is limited to a specific field (immunity) and model system (Drosophila). Since biological context may influence reproducibility -- for example, depending on whether mechanisms are more hardwired or variable -- and the model system itself may contribute to these effects (as the authors note), it remains unclear to what extent these findings generalize to other fields or organisms. The authors could expand the discussion to address the potential scope and limitations of the study's generalizability.

      We have added a limitation section at the end of the manuscript to discuss these points. We wrote:

      “Finally, the findings we report may be specific to a particular field, model organism, and time period, and may be strongly influenced by factors idiosyncratic to their development. Because this analysis is limited to a single field (immunity) and model system (Drosophila), it remains unclear to what extent these findings generalize to other fields, organisms, or more recent studies.”

      However, we believe that our study adds on the discussion on reproducibility by providing another approach. Our study also aligns with the feeling that knowledge of Drosophila innate immunity has increased so much in the last decades, and that science is still quite robust in many fields.

      Reviewer #3 (Public review):

      Summary:

      The authors of this paper were trying to identify how reproducible, or not, their subfield (Drosophila immunity) was since its inception over 50 years ago. This required identifying not only the papers, but the specific claims made in the paper, assessing if these claims were followed up in the literature, and if so whether the subsequent papers supported or refuted the original claim. In addition to this large manually curated effort, the authors further investigated some claims that were left unchallenged in the literature by conducting replications themselves. This provided a rich corpus of the subfield that could be investigated into what characteristics influence reproducibility.

      Strengths:

      A major strength of this study is the focus on a subfield, the detailing of identifying the main, major, and minor claims - which is a very challenging manual task - and then cataloging not only their assessment of if these claims were followed up in the literature, but also what characteristics might be contributing to reproducibility, which also included more manual effort to supplement the data that they were able to extract from the published papers. While this provides a rich dataset for analysis, there is a major weakness with this approach, which is not unique to this study.

      Weaknesses:

      The main weakness is relying heavily on the published literature as the source for if a claim was determined to be verified or not. There are many documented issues with this stemming from every field of research - such as publication bias, selective reporting, all the way to fraud. It's understandable why the authors took this approach - it is the only way to get at a breadth of the literature - however the flaw with this approach is it takes the literature as a solid ground truth, which it is not. At the same time, it is not reasonable to expect the authors to have conducted independent replications for all of the 400 papers they identified.

      However, there is a big difference trying to assess the reproducibility of the literature by using the literature as the 'ground truth' vs doing this independently like other large-scale replication projects have attempted to do. This means the interpretation of the data is a bit challenging.

      We acknowledge that our analysis necessarily relies on the published literature; however, two important points should be considered. First, we assessed replicability more than a decade after the original studies, allowing us to evaluate whether their claims have withstood subsequent scrutiny. Second, the evaluation draws on the authors’ strong expertise in the field. Accordingly, the validity of published claims was not accepted uncritically but subjected to informed expert assessment. This is exemplified by the case of the proposed microbicidal role of Duox, which we classified as challenged despite the original article accumulating more than 600 citations.

      Overall, our replicability analysis, like similar efforts, relies not only on literature but also on expert judgment. Of course it has inherent limitations, which are now more clearly articulated in the discussion.

      Below are suggestions for the authors and readers to consider:

      (1) I understand why the authors prefer to mention claims as their primary means of reporting what they found, but it is nested within paper, and that makes it very hard to understand how to interpret these results at times. I also cannot understand at the high-level the relationship between claims and papers. The methods suggest there are 3-4 major claims per paper, but at 400 papers and 1,006 claims, this averages to ~2.5 claims per paper. Can the authors consider describing this relationship better (e.g., distribution of claims and papers) and/or considering presenting the data two ways (primary figures as claims and complimentary supplementary figures with papers as the unit). This will help the reader interpret the data both ways without confusion. I am also curious how the results look when presented both ways (e.g., does shifting to the paper as the unit of analysis shift the figures and interpretation?). This is especially true since the first and last author analysis shows there is varying distribution of papers and claims by authors (and thus the relationship between these is important for the reader).

      Articles can contain claims that we found replicable and other that we did not. Thus, we believe than an evaluation by claim is more precise. The extraction of the different claims relies on the reading of the article, but is a human enterprise. There are clearly some unavoidable biases at this step. Of note, the articles analyzed in this study are very different one from another (size, novelty, amount of data…).

      However, we agree that the analysis at the article level is interesting, and we followed the reviewer suggestion and provided in Supplementary Section S6 a sensitivity analysis of using article-level effects for the multivariate analysis. We note that because only 43 articles (12.5%) contained at least one challenged claim, this analysis is less robust than the claim analysis. The text added in the SI states:

      “Two claims in the same paper might not be independent, so we might want to incorporate an article random effect to the primary Bayesian formulation. However, due to the low number of claim per article (mostly one to four) and only 43 articles (12.5%) contained at least one challenged claim (and most articles contains only one to four claims), we could not manage to fit this model properly (we observe MCMC divergences). As a work-around sensitivity analysis, we repeated the analysis with the article as the unit. Each of 345 articles with complete covariate data (representing 869 major claims, 60 of the 69 challenged claims in the full dataset; the remaining 9 fell in articles excluded for missing covariates) contributed as outcome the proportion of its major claims classified as challenged. The model was a (frequentist) binomial-link fractional-response generalized linear model with HC3 standard errors (the intervals reported here are 94% confidence intervals rather than posterior credible intervals).

      Each article contributed equally regardless of its number of claims. The Top-50 institutional effect remained significant under both analysis (OR 5.15, 94% CI 2.18– 12.15; versus a claim-level OR 3.68, 94% HDI 1.50–9.28). In this new model Trophy journals also showed had higher odds of challenged claims than low-impact journals (OR 2.90, 94% CI 1.24–6.78 vs a claim-level OR 1.75, 94% HDI 0.59–4.91). This impact was not significant in the primary model but became significant at using article-level analysis. Other estimates are consistent in direction and magnitude with the primary claim-level model. Model diagnostics were satisfactory.”

      Moreover, we added Figure S6 which display visually the relationship between the claims and the article.

      [This response is referred later as “Response to claim vs article level analysis”]

      (2) As mentioned above, I think the biggest weakness is that the authors are taking the literature at face value when assigning if a claim was validated or challenged vs gathering new independent evidence. This means the paper leans more on papers, making it more like a citation analysis vs an independent effort like other large-scale replication projects. I highly recommend the authors state this in their limitations section.

      We have now explicitly acknowledged this limitation in a dedicated section at the end of the revised manuscript. However, as noted above, we do not take the literature at face value. Notably, some of the claims we identify as challenged originate from highly cited articles, which could lead a naïve reader to assume their validity.

      Ultimately, this replicabilty project remains a human, expert-driven effort aimed at determining which claims withstand scrutiny within a field. The broader community was invited to engage with and respond to these assessments and we did get some feedbacks. Importantly, claims were not evaluated in isolation but in the context of the entire body of knowledge, and all evaluations were made transparent and explicitly justified in the ReproSci database.

      On top of that, I have questions that I could not figure out (though I acknowledge I did not dig super deep into the data to try). The main comment I have is How was verified (and challenged) determined? It seems from the methods it was determined by "Claims were cross-checked with evidence from previous, contemporary and subsequent publications and assigned a verification category". If this is true, and all claims were done this way - are verified claims double counted then? (e.g., an original claim is found by a future claim to be verified - and thus that future claim is also considered to be verified because of the original claim).

      When two articles reported the same main claim and this claim was judged as “verified,” each instance was counted in the analysis. However, when validation came from studies published after 2011, the claim was counted only once. Thus, our study specifically evaluates the replicability of claims originating from a defined period (pre-2011).

      We note that, in principle, repeated publication of the same finding across many articles could artificially inflate estimates of replicability. However, such cases appeared to be rare in practice, and studies reporting similar claims typically provided complementary evidence—for example, elucidating gene function through either genetic or biochemical approaches.

      Related, did the authors look at the strength of validation or challenged claims? That is, if there is a relationship mapping the authors did for original claims and follow-up claims, I would imagine some claims have deeper (i.e., more) claims that followed up on them vs others. This might be interested to look at as well.

      We did not perform a systematic mapping between original claims and subsequent follow-up studies. While this is an important and interesting aspect, it was considered beyond the scope of the present work. The current study already represents a substantial investment of time and effort, and the resulting database provides a valuable resource for future analyses. In particular, it could support a dedicated bibliometric study at a later stage.

      (3) I recommend the authors add sample sizes when not present (e.g., Fig 4C).

      The cited panel appears to correspond to Figure 5C in the revised numbering, as the current Figure 4 contains only panels A and B. We systematically checked the denominators of all figures and revised the captions to report the numbers of claims, authors or laboratories represented, together with the reasons for exclusions. We also added the numbers of authors and claims directly within the author-level scatter plots, with the observational unit explicitly identified.

      I also find that the sample sizes are a bit confusing, and I recommend the authors check them and add more explanation when not complete, like they did for Fig 4A. For example, Fig 7B equals to 178 labs (how did more than 156 labs get determined here?), and yet the total number of claims is 996 (opposed to 1,006).

      There are 156 labs total, 23 labs contributed publications during both junior and senior stages, and 11 claims lacked a junior/senior classification. This has been explicited in the caption.

      Another example, is why does Fig 8B not have all 156 labs accounted for?

      The panel does not include all 156 laboratories because we could obtain information about first author training for only 146 PI and laboratories while prior first-author status was unavailable or indeterminate for ten PI. This has been added to the caption.

      (Related to Fig 8B, I caution on reporting a p value and drawing strong conclusions from this very small sample size - 22 authors).

      The 22 authors are not the total sample size; they constitute the subgroup of PIs who had previously published a first-author paper on Drosophila immunity in another laboratory. In the submitted panel, they were compared with 117 PIs without this training history, giving 139 classified laboratories and 774 claims.

      As a last example, Fig 8C has al 156 labs and 1,006 claims - is that expected? I guess it means authors who published before 1995 (as shown in Figure 8A continued to publish after 1995?) in that case, it's all authors? But the text says when they 'set up their lab' after 1995, but how can that be?

      Thank you for identifying this inconsistency. Figure 8C intentionally includes the full cohort of 156 PIs and all 1,006 claims. Panel C compares research styles and does not impose a restriction based on year of entry into the field or year of claim publication. Thus, PIs who entered the field before 1995 are included together with all claims attributed to them; the panel is not restricted to claims published after 1995.

      The statement that only PIs who established their laboratories after 1995 were included was an erroneous carryover from an earlier version of the analysis. We removed this restriction from the Results and revised the caption to state that exploratory PIs (n = 91) contributed 366 claims, whereas continuity PIs (n = 65) contributed 640 claims.

      We also replaced references to the date when PIs “established their laboratory” with “year of entry into the field,” defined as the year of their first Drosophila-immunity publication as either first or last author. During the same check, we revised Panel B to include all 146 PIs eligible for the pre-PI training comparison, contributing 793 claims.

      (4) Finally, I think it would help if the authors expanded on the limitations generally and potential alternative explanations and/or driving factors. For example, the line "though likely underestimated' is indicated in the discussion about the low rate of challenged claims, it might be useful to call out how publication bias is likely the driver here and thus it needs to be carefully considered in the interpretation of this. Related, I caution the authors on overinterpreting their suggestive evidence. The abstract for example, states claims of what was found in their analysis, when these are suggestive at best, which the authors acknowledge in the paper. But since most people start with the abstract, I worry this is indicating stronger evidence than what the authors actually have.

      We have added a dedicated section on limitations at the end of the Discussion to explicitly acknowledge key constraints, and we also address these points throughout the Discussion where relevant. In addition, these limitations are now in the abstract.

      The authors should be applauded for the monumental effort they put into this project, which does a wonderful job of having experts within a subfield engage their community to understand the connectiveness of the literature and attempt to understand how reliable specific results are and what factors might contribute to them. This project provides a nice blueprint for others to build from as well as leverage the data generated from this subfield, and thus should have an impact in the broader discussion on reproducibility and reliability of research evidence.

      Thank you for this positive assessment!

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      Comments and recommendations are provided in the order that they appear in the manuscript.

      Introduction:

      - In the second paragraph of the introduction, I don't think all the references refer to "molecular life sciences" (e.g. one of them is from ecology and evolution, for example). I'd also argue that Macleod et al. 2014 refers to risk of bias rather than to reproducibility per se.

      We have corrected this in the revised version.

      - The author use both "reproducibility" and "replicability", apparently as synonyms, but as definitions for these words vary across sources (e.g. https://arxiv.org/abs/1802.03311, https://www.nationalacademies.org/our-work/reproducibility-and-replicability-in-science, https://osf.io/br9sp/) it may be worth stating their definitions upfront.

      Thank you for the references. We agree that the literature contains multiple, sometimes conflicting definitions of these terms, which can lead to confusion. In response to the reviewer’s comment, we have clarified our terminology. Specifically, we now use the term “conceptual replicability” in the abstract and consistently refer to “replicability” and “irreplicability” throughout the manuscript. We hope this revised terminology improves clarity.

      - Why are analysis described as "exploratory" and "multivariate"? If it has not been preregistered, shouldn't the multivariate analysis be considered exploratory as well?

      Thanks, we agree. The word “exploratory” is confusing as we use it for its structural meaning and not its epistemological meaning. We have replaced it throughout by “descriptive”, as to not imply that the multivariate analysis is preregistered by contrast.

      Results:

      Methodology and claim assessment

      - The methods for the selection, annotation and classification of studies are described very cursorily here, and the Methods section doesn't add that much, but I'll keep these observations to the methods. Still, it's worth mentioning that it's hard to know how reproducible the annotation and classification process is from the information provided.

      We have provided more information on the method section on the way to annotate and class claims. Of note, there is more information on the methods on the associated publication Westlake et al., 2025 and on the ReproSci website.

      - "Then, experimental work was performed in several laboratories...". Once again, a much better description of how replications were set up and performed is needed.

      We have provided information on the number of laboratories (nine) involved in the reproduction of 45 major claims. The laboratories involved in replication are listed in the author list. All the files associated with experimental replication can be found in the supplementary materials of Westlake et al 2025 or the ReproSci website.

      - "These claims subjected to experimental validation were selected according to criteria such as appearing suspicious due to the absence of direct follow up or being straightforward to test experimentally". This is rather vague, but if no explicit criteria were set upfront this may be inevitable. Still, it would be useful to know who made this decision.

      A first list of claims to be replicated was made by Hannah Westlake and Bruno Lemaitre. The claims that were selected to be replicated were tested by the labs and experimental workers that had the expertise required to test them. The choice of the claims to be tested was not random. Claims that were suspicious are claims that were already tested in the host laboratory without success, claims whose validity are debated at meeting, claims from highranked journal with no follow-up. This is now indicated in the method of the revised version.

      Drosophila immunity claims are mostly reproducible

      - The percentages given in the initial description of the results pool the results of the retrospective analysis of the literature and the prospective replications performed. As mentioned in the Public Review, I think these are rather distinct ways to assess reproducibility, and would recommend that these two analyses are described separately.

      We agree with the reviewer but we believe that we have already well separated the results before and after experimental work in the revised version. This is clearly shown in Table 1. Our text says ‘Importantly, 6.8% of claims (69 out of 1006) were challenged. Among these, 44.9% (31 out of 69) were contested by published articles including 7.2% by the same authors, and 55.1% (38 out of 69) were challenged experimentally as part of the ReproSci project.’

      - "These results may reflect the robust scientific standards and methodological rigor of Drosophila research...". Once again, as mentioned in the Public Review, I think publication bias is a plausible explanation, so this should be mentioned as an alternative.

      We have mentioned publication bias in the revised version in the section on limitation. But an important point to underline is that this analysis did not take publication results as face fact. This is a critical analysis by experts in the field. As already mentioned, some claims like ‘Duox produces microbicidal ROS” ‘NO is a signaling molecule…’that have been mentioned in multiple articles were considered as challenged.

      A second point is that it is likely that publications in some fields are more replicable than in other. Actually, we did not discuss ‘reproducibility issues’ when I started in the field 30 year ago because this was not perceived as an issue. It is normal that reproducibility rate varies according to fields. Nevertheless, we do find important claims with high visibility that are not replicable in our sample. Thus, our findings nuance the ‘reproducibility crisis narrative’ but we still believe that there is concern with reproducibility in life science. Last point, the criterium we have used in our study did not map all the problematic papers, notably some claims might be fundamentally verified but exaggerated in the original paper.

      - It would be useful to break down the "partially verified" category somewhere. Illustrative examples of what is meant by "insightful data were accompanied by incomplete interpretations" or "incomplete data were paired with insightful interpretations" would be useful as well.

      All the claims are listed in the public database with an explanation as to why they got affected to a category. The categories mixed and partially verified refer to claims that are more complex to categorize.

      Here are are two examples from the ReproSci website:

      Claim: Relish Rel mutants are very susceptible to bacterial and fungal infection. Partially verified

      Assessment: Relish mutants are primarily susceptible to Gram-negative bacterial infections, and do not typically have increased susceptibility to Gram-positive bacteria and fungi which are primarily rebuffed by the Toll pathway, although Imd signaling may provide a minor contribution to defense against these. The high susceptibility of Relish mutant to fungi observed in this article is likely due to the presence of the ebony marker (Lemaitre et al., 1996) [here only one part of the statement has been verified]

      Claim: PGRP-SC1a is required for Lys-type peptidoglycan recognition and Toll activation. Mixed

      Assessment: A possible role for PGRP-SCs in Toll activity has been strongly debated. Challenged by (Bischoff et al., 2006) who found no effect of PGRP-SC RNAi on activation of Toll (Drs expression) in adult flies (although note that their data show a minor reduction of Drs expression in flies in response to E. faecalis). Supported by (Costechareyre et al., 2016) who used single -SC1 and -SC2 mutants to show that Toll activation (Drs expression) was reduced in -SC1 but particularly -SC2 mutants (~50%) in response to E. faecalis (although survival was not affected). The supplementary data of (Paredes et al., 2011) similarly show that Drs expression was reduced (50%) in response to M. luteus septic infection in PGRP-SCdelta flies (PGRP-SC1A/B -SC2 triple mutant), but concluded that this was due to a secondary effect of Imd overactivation. Note that the phenotype found by (Garver et al., 2006) was much stronger (complete ablation of Drs expression), which is not consistent with any subsequent results and argues for a secondary mutation in this line, although this is not consistent with the successful rescue of Drs expression by transgenic replacement of PGRP-SC1a. Downregulation of Toll in these mutants could be explained if the Toll pathway requires amidase activity of PGRP-SC for immunogenicity (e.g. the sugar backbone without stem peptides is a stronger elicitor than whole peptidoglycan), whereas similar cleavage reduces recognition by the Imd pathway (consistent with the demonstrated requirement of stem peptides for full stimulation of the Imd pathway (Chang et al., 2005; Stenbak et al., 2004)). See annotation for (Mellroth et al., 2003). [here the claim is mostly challenged but there are observations that go in the same directions]

      As shown by these examples, category assessment was complex process and relied on human expertise. However, there was very little contestation from the community after the submission of our articles and the opening of the ReproSci website.

      A significant fraction of unchallenged claims is non-reproducible

      - Excluding the 45 unchallenged major claims that were experimentally tested, we categorized the remaining 240 unchallenged claims into three groups". No information is provided on that classification process (either here or in the methods). Who made these assessments (which seem quite subjective and dependent on field expertise), and how do you know if such judgments are reproducible across different evaluators?

      This categorization was done by Hannah Westlake and reviewed by Bruno Lemaitre with few disagreements. This is now indicated in the revised version. The category ‘unchallenged logically consistent” and ‘‘unchallenged logically consistent’ refer to claims that although not directly verified are corroborated or in with current literature. See ReproSci for justifications.

      Example from ReproSci website:

      Claim: The minimal structure needed to activate the Toll pathway is a muropeptide dimer.

      Assesment: Unchallenged logically consistent This is consistent with (Park et al., 2007) who show that on a linearized strand of peptidoglycan, the minimal motif is at least 3 dimers. But it is expected that a non-linearized dimer linked by the peptide bridge could serve as the minimal motif by clustering peptidoglycan.

      Claim: eater null flies are susceptible to oral infection with Serratia marcescens Unchallenged logically consistent Inconsistent with the observation that Eater mutants successfully phagocytose Serratia marcescens (Bretscher et al., 2015). This may indicate that another factor affected by eater mutation is required for defense against S. marcescens, such as formation of lamellopodia and filopodia or adhesion of hemocytes to the body wall, or that Eater contributes to binding of Gram-negative bacteria but does not trigger phagocytosis in response to them as it does for Gram-positive bacteria.

      Higher representation of challenged claims in trophy journals and from top universities

      - Both impact factor and the Shanghai university ranking are continuous variables, but the authors opt to use them as categorical variables in the analysis (i.e. "low-impact", "highimpact", "trophy"; "Top 50", "51-100", "101+"). While there may be legitimate reasons to do this if they feel that these categories are a better descriptor of the underlying reality (e.g. perhaps Cell, Science and Nature are indeed in a category by themselves), it is an unusual decision that leads the comparison to ignore the distinctions between journals/universities within a category. Moreover, it also opens up the opportunity to analysis bias as categories can be set up in many different ways. Thus, if the analysis was not preregistered, I'd recommend that analyses using impact factor and ranking as quantitative variables are added as sensitivity analyses, as these seem to me to be the most natural/less ad hoc way to look at the issue.

      See “Response to categorical variable encoding” above.

      - As mentioned in the Public Review, the analysis here pools the results from the retrospective analysis based on the literature and the prospective one based on the performed replications. Although this may be justified from a sample size perspective (as the number of challenged claims is not that high), it would be useful to perform this analysis separately on the two sets of results as well, as different trends may be noticed. There are many biases that might come into play here (e.g. results from top institutions being more or less likely to have challenged/unchallenged claims published) and looking at the results separately could help in tearing apart these hypotheses.

      The ReproSci project analyzes all the papers of a community during a period of time. As such, the total number of claims is limited and we believe that pooling the data was justified. We provide as sensitivity analysis in Supplement S7, a multivariate model with claims in their pre-experimental classification state:

      “As a sensitivity analysis, we refitted the multivariable hierarchical logistic model using only the claim classifications available before experimental validation by the ReproSci project, as the choice of which claims to further validate could have been influenced by covariate (impact factor, university status). The 45 claims tested prospectively were therefore restored to their original “Unchallenged” classification, while all covariates and author-level random intercepts were retained from the primary analysis. The complete-case analysis included 869 claims, of which 28 (3.2%) were challenged. No predictor had a 94% highest-density interval excluding 1, including publication in trophy journals (OR 1.11, 94% HDI 0.33–3.77) and affiliation with a Top50 institution (OR 1.44, 94% HDI 0.48–3.94). Thus, the associations observed in the pooled analysis were not evident when using classifications based exclusively on the retrospective literature review, although estimates were imprecise because of the small number of challenged claims”

      The irreproducibility rate has increased over time as the field has grown in popularity

      - Again, why not use year as a continuous variable rather than using 5-year windows (as this would effectively include more information)? I think the categorization here is less ad hoc than in the journal/university case, but it is still an unusual decision. More important than this, however, is the fact that pairwise comparisons between periods is probably not an appropriate strategy to look for a time trend, as it excludes all information not related to the pair in each analysis. I'd strongly suggest substituting this for a straightforward regression with publication year as a continuous variable.

      We thank the reviewer for this important suggestion. We agree that categorizing publication year into five-year periods may obscure temporal trends.

      We therefore modelled publication year continuously using a spline in the multivariable analysis, thereby retaining the full temporal information while allowing for non-linearity. A straightforward linear regression would impose a linear trend, which may not adequately capture changes over time. We retained the five-year groupings solely for visualization.

      - "The subsequent increase in unchallenged claims may reflect the rapid conceptual expansion of the field, which likely outpaced the growth in the number of researchers". Do we have data on the growth in the number of researchers in the field? If so, it might be interesting to cite this.

      We do not have the number of researchers to assess the growth of the field, however we can see in Figure 8A an increase in the number of laboratories (as identified by last author name) after 1995. This together with the increase in the number of articles (Figure 3A) clearly show the expansion on of the field.

      - Isn't a "rise in unchallenged claims" over time expected by chance, as older findings will have more time to have been verified by someone else? I understand that the 14-year window probably mitigates this effect, but it still probably exists in some degree and should be mentioned.

      The reviewer is correct that the % unchallenged claims should increase over time, but this does not explain the very low number of unchallenged claims between 1992-2001.

      First-author patterns of irreproducibility

      - With 69 challenged claims and 289 first authors, it would be impossible to achieve "perfect equality" (e.g. a Gini index of 0.88). To verify how far the observed coefficient deviates from chance, it would be useful to obtain (perhaps via simulations) the Gini coefficient expected by chance given the number of challenged claims/authors, and perhaps derive a p value as well (e.g. the proportion of random permutations in which the index exceeds the observed value).

      Very good observation, thank you, we provide this analysis for both first and last author, in the main text and in a supplementary table.

      Added first author text:

      “The distribution of challenged claims among first authors was highly unequal with a Gini coefficient of 0.881 (inequality index ranging from 0 -perfect equality- to 1 extreme inequality-, Figure 4B): the top 10% of first authors accounted for 73.9% of challenged claims, and the top 20% accounted for all challenged claims. This inequality exceeded that expected by chance (reassigning randomly the 69 challenged labels across individual claims, while preserving each author’s number of claims, p = 0.000001). It also remained greater than expected when claims from the same paper were kept together (p = 0.015; Supplementary Table Sx). The concentration of challenged claims among first authors cannot be explained solely by differences in the number of claims or by clustering within papers.”

      Added last author text:

      “Challenged claims were also unevenly distributed among leading authors (Gini coefficient = 0.856): the top 10% accounted for 71.0% of challenged claims and the top 20% accounted for 94.2%. The observed inequality exceeded that expected when challenged labels were reassigned across individual claims (p = 0.00081), but not when claims from the same paper were kept together (p = 0.127; Supplementary Table S9). The apparent concentration among leading authors could be explained by multiple challenged claims arising from the same papers.”

      Added method text:

      “We compared the observed Gini coefficients with two permutation analyses, each based on 1,000,000 permutations. First, we randomly reassigned the challenged labels across individual claims while keeping every claim attached to its original author. This preserved the number of claims contributed by each author. Second, we kept the challenged-claim pattern of each paper together and reassigned these patterns among papers containing the same number of claims. This additionally accounted for the possibility that claims from the same paper were challenged because of a shared problem. For each permutation, we recalculated the Gini coefficient across authors and calculated the p-value as the proportion of simulated coefficients that equalled or exceeded the observed coefficient. Full results are reported in Supplementary.”

      - Claims in a single paper may not be fully independent from each other (as both could be irreproducible due to the same error), so it could be worth adding the article as a random variable here.

      See answer above: [“Response to claim vs article level analysis”]

      - In Fig. 4B, what defines the order of the dots between 0 and 250 (i.e. authors that have no challenged claims)? Is this merely arbitrary? This should be stated more clearly.

      Thank you, the order was arbitrary, it has now been fixed by using a secondary sorting (verified claim proportion), and Authors tied on challenged-claim proportion are ordered by verified-claim proportion has been added the legend.

      - In Fig. 5C, there are clearly less dots than there are authors. This is likely due to superposition (i.e. there are probably multiple circles with 1 article and 0% verified claims). Nevertheless, it means that the graph conveys an erroneous message. As the x axis is a discrete variable, it may be worth turning it into five categories (e.g. 1 to 5) and adding some jitter to each of them in order to let the reader know how many dots are in each category/%.

      Thank you, this was indeed due to superposition. After trying to add a jitter, the graph was still confusing, so we changed the representation to show circle whose size depends on the number of authors. The graph now conveys the size of each block properly.

      Lead-author patterns of irreproducibility

      - The same comment concerning the Gini index made for the first authors also holds here.

      We added a text, see answer above.

      - In Fig. 6B, the same comment made for figure 4B also holds.

      Thank you, the order was arbitrary, it has now been fixed by using a secondary sorting (verified claim proportion), and Authors tied on challenged-claim proportion are ordered by verified-claim proportion has been added the legend.

      - The division between "senior" and "junior" PIs is rather ad hoc here. Once more, why not use "years from first last-author publication" as a continuous variable as a more neutral way to analyze this (as done in Fig. 8)? Also note that it is not clear whether "published a lastauthor article at least five years prior to the considered publication" means any article or one about Drosophila immunity (as in Fig. 8A), and which database was used to examine this (PubMed? Other?).

      Senior and junior researchers were classified based on whether they had published a last-author article five years or more using Pubmed (for seniors). We did not specify articles in Drosophila immunity when considering seniority but only having a last author article five year before the publication.

      - In Fig. 7C, the same comment made for Fig. 5C also holds, although the solution here is less obvious as there are more possible numbers for "number of articles".

      Thank you. As in Fig. 5C, superposition obscured multiple authors occupying the same coordinates. We therefore revised Fig. 7C so that authors with the same number of articles and proportion of challenged claims are represented by a single circle. Circle size and the number shown inside indicate how many authors are represented.

      - As far as I could tell, the data on Fig. 8A refers to when authors published their first first/last author papers on Drosophila immunity (which makes it different from Fig. 7, which refers to any article, but I could be mistaken). If this is the case, I'm not sure it's correct to talk about "the period when principal investigators established their laboratories" as mentioned in the text, as (a) they could have published a first author paper in somebody else's lab or (b) they could have started a lab and only later published a paper on Drosophila immunity. "Year of entry in the field" as in the figure legend seems more appropriate.

      We have changed for ‘year of entry in the field’ as suggested by the reviewer

      - In the same figure, the 1995 cutoff seems completely arbitrary. Why not analyze this as a regression with year of entry as a continuous variable?

      The 1995 boundary is historical as it marks the expansion of Drosophila immunity from a marginal subject into a popular field. The expansion of the field at this specific time was probably driven by a combination of factors: major advances in Drosophila genetics and genomic resources and growing knowledge of antimicrobial peptides in the early 1990, a strong interest on innate immunity that drew attention on the power of Drosophila to answer key questions in this new area. These developments attracted new researchers to insect immunity, and the later discoveries of the IMD and Toll pathways in 1995 and 1996 gave the field an additional (and probably even stronger) boost. Our corpus holds 29 articles for 1959– 1994 (0.8 per year) against 371 for 1995–2011 (21.8 per year), and only 13 of the 156 PIs entered before 1995. The comparison is therefore a cohort contrast more than a contrast or search for a cutting point. Moreover, a regression would impose a linear relationship between the different years, which we believe is too constrained on regard of the observed data.

      - "We hypothesized that these authors, having gained prior hands-on experience on Drosophila immunity, would be less prone to publishing irreproducible claims.". This is a possibility, but given that most of the sample is retrospective, it's also possible that the field is more prone to publicly challenging findings from newcomers.

      Since we do not observe major difference in replicability between senior and junior PI, we still believe that training as first author in a traditional immunity laboratory compared to no training is significant.

      Irreproducibility according to research styles

      - The objective definition of "continuity" and "exploratory" PIs should be stated here for this to be interpretable (note that this is not clear in the Methods either).

      We have better defined how we separate "continuity" and "exploratory" PIs in the methods and in the result section.

      Multivariable analysis of predictors of claim irreproducibility

      - As mentioned in the Public Review, does it make sense to include "unchallenged" along with "verified" in the outcome? If the objective is to reduce the analysis to a "verified/not verified" claim, wouldn't it make more sense to remove the unchallenged findings (as these are likely uninformative, and based on the authors' own replications may be more related to the "challenged" category than to the "unchallenged" one?

      See above, “Response to unchallenged exclusion”

      - As stated previously, why not include journal impact factor, university ranking, year of first paper and year of first Drosophila immunity paper, as continuous variables rather than categorical ones (which would effectively lead to a model with less parameters when there are more than 2 categories). Particularly, there is more information to be gained from adding a single variable than from performing individual comparisons between categories when these have a natural order.

      See above, “Response to categorical variable encoding”

      Discussion:

      - As "conceptual reproducibility" is somewhat of a vague concept, it seems important to discuss (both in the Methods and Discussion) how this was operationalized. Although it's obvious some decisions of what constitutes a direct replication will vary on a case-by-case basis, general guidelines on how these criteria were set are needed.

      We have defined in the methods used to categorize article claims as well as the link with the other companion article. In the ReproSci database, all the assessment are justified allowing to see how we classified claims.

      - "Contrary to the more dramatic narratives...". Here, it is important to emphasize the key differences between this and the cited references: (a) the fact that the majority of the replicability of the sample was found on the basis of a retrospective sample and (b) the fact that the study is dealing with conceptual rather than direct replications. Also, the possibility of confirmation bias should be mentioned as an alternative hypothesis in the last sentence of this paragraph.

      This is a good point and we have highlighted that methodological differences between our study and other studies could explain differences in replicability rates.

      - "findings that, despite being published, have never been independently tested". A more accurate description may be "have never been independently confirmed or refuted in the published literature", as many (and perhaps most - see Baker 2016) replication attempts may go unpublished, as the following sentences themselves indicate.

      We have changed the text according to the reviewer’s suggestion.

      - The description of how findings came to be regarded as "suspicious" here is interesting - and an important part of how the sample was determined. In this sense, I'd consider this as part of the methods. Even though defining what makes something "suspicious" may not be completely systematic, a general description of the method that led the researchers to arrive at this list (e.g. the process that seems to be hinted at in this paragraph) deserves a thorough description.

      The description of how findings came to be regarded as "suspicious" is now detailed in the methods.

      - "Our results suggest the status of a claim being "unchallenged" is not a reliable proxy for its validity". I agree, but this is statement is in direct contradiction with the authors' decision to include unchallenged claims along with validated ones in the binary outcome of the multivariate model.

      See above, “Response to unchallenged exclusion”

      - "Trophy journals are more likely to publish articles with challenged claims than high or lowimpact, although the difference was not significant." Again, a single analysis using a continuous measure of impact should provide more statistical evidence than the pairwise comparisons.

      See above, “Response to categorical variable encoding”

      - "However, this higher rate of follow-up work cannot fully explain by itself the higher proportion of challenged claims in trophy journals." Why not, exactly? I don't remember seeing an objective analysis of it.

      If we remove the unchallenged claims, we still observe higher rate of irreplicability in trophy journal: 15.85% in trophy journal versus 9% in high-impact and 8.1% in low-impact. So we believe that the higher rate of irreplicability in trophy journals cannot be explained by a lower level of unchallenged.

      - The very large paragraph on pages 21-22 could be split into two, one about journals and the other about universities.

      This has been done.

      - "Our data align with the broader narrative of increasing rates of non-reproducible science.". Does it? The time trend did not seem very clear to me (and I would argue that it was not analyzed properly).

      As indicated in the text, we observed an increase in the rate of irreplicable claims over time; however, this trend did not reach statistical significance. We are confident in the robustness of our analysis and therefore did not pursue this question further. While our findings align with concerns about non-replicable science, they also offer a more nuanced perspective, showing that in some fields, replicability remains significantly high.

      - "A similar but more acute pattern was observed during the SARS-CoV-2 pandemic." References should be provided here.

      We have added this reference to suggest that articles published on SARS-CoV-2 pandemic are overall less reliable than others: An alarming retraction rate for scientific publications on Coronavirus Disease 2019 (COVID-19) Nicole Shu Ling Yeo-The https://doi.org/10.1080/08989621.2020.1782203

      - Some of the trends discussed here (e.g. time, continuity vs. exploratory style are not supported (even as a trend) by the multivariate model, and this caveat should be mentioned. An odds ratio of 0.89 with a very wide confidence interval may be too weak in terms of evidence strength to merit a whole paragraph in the introduction discussing it.

      We did not mention the question of time horizon or the distinction between continuity and exploratory research styles in the Introduction; however, we believe these issues merit consideration in the Discussion. In particular, the contrast between continuity-driven and exploratory approaches is noteworthy. Although we found no significant difference in the rate of challenged claims between these approaches, there was a significant difference in the rate of unchallenged claims, which are subsequently more likely to be challenged. This finding is important in the current funding landscape, where many agencies prioritize short-term, exploratory projects. Such incentives may inadvertently contribute to issues of irreproducibility.

      - There are many other limitations beyond those mentioned, in particular the fact that much of the analysis is retrospective and based on a potentially biased literature. The fact that the analysis does not seem to be preregistered and is dependent on a lot of ad hoc decisions also merits discussion. This should definitely be explored in more detail in the Limitations section.

      These limitations are now discussed in the limitation section at the end of the discussion. We agree on the fact that our analysis was not preregistered and that some of our conclusions are raised after analyzing the data. This article is part of a more global project including the databases with all the information. However, full objectivity when analyzing literature is not unachievable, and these critics are inherent to all reproducibility projects.

      Methods:

      Selected articles, annotation and experimental validation:

      - "In brief, a list of 400 publications published before 2011 was generated using a curated search string on the publicly available PubMed database.". Please state that the search string is available in the companion article (e.g. https://doi.org/10.1101/2025.07.07.663442) or include it here.

      This is now stated.

      - "Selected primary articles were annotated by a single researcher".

      By "annotation", do the authors mean the extraction of claims? This is not self-evident. Also, what does the "review" process entails? Do the authors have any data on agreement?

      We do not have data on agreement but overall, there were few discrepancies. We agree that the way to section article in separate claims could affect the conclusion in a number of cases. All the data are public and we did not have any request from the community. The fact that this project depends from arbitrage from the two annotators is mentioned in the limitations.

      - "Claims were cross-checked with evidence from previous, contemporary and subsequent publications and assigned a verification category."

      How was this process performed? This seems to be quite complex and there's hardly any information about it. And once again, do the authors have any data on how reproducible this process would be when performed by different people?

      All the data, notably claim assessment and justifications, are available on the website. Findings cross-checking the claim could be identified by knowledge of the authors, checking articles that quotes the articles. This was an enormous amount of work with human arbitrage. We expected more feedback from the community. The reaction of the community will be described in a companion article later.

      - The authors mentioned that annotations and verifications were made available for comments on the community, but how were these comments incorporated if different opinions were voiced? Can the authors provide data on how frequent these comments were, and how often they were incorporated?

      All data is available on the website, where members of the community can publicly comment on our assessments. The authors can see these comments on the ReproSci website

      Table 1:

      - Again, the three "partially verified" categories in Table 1 seem to refer to very different situations and it would be interesting to break these down somewhere.

      We agree that categories ‘mixed’ and ‘partially verified’ are complex. They represent situations where a decision was not easy. We prefer not to break down those categories in multiple sub-categories.

      First and last author classification:

      - What does "status of first author" mean?

      Status means their position: technician, PhD student, Post-doc, PI….

      - "PIs were manually classified as..." - there seems to be something missing in this sentence (e.g. "as senior or junior on the basis of whether they have...")

      We have added PIs: PIs were manually classified as senior or junior PIs on the basis on having published an article in Pubmed as last author more than five year ago.

      - The distinction between continuity and exploratory is not explained in objective terms. Is there any objective definition of what it means to "continue to work in the field". Publishing a paper in the last X years? And what counts as a "transient" incursion?

      We have better explained in the methods this distinction.

      Statistical analysis:

      - Can the authors define exactly what they mean by "weakly informative priors"?

      Weakly informative prior are Bayesian prior distribution that are meant to be vague as to let the data dominate the results (vs the prior belief of the scientist). They can be seen as very close to flat priors, which are not used here because they cause numerical convergence issues.

      - The authors mention a lot of variables included in the multivariable analysis, but little information is provided on the categorization. What are "low, high and trophy journals"? What university rankings are used?

      We used Shanghai Ranking’s 2010 Academic Ranking of World Universities as our ranking of university. Our binning of ranking in categories make the analysis less susceptible to changes in ranking system. We selected the Shanghai ranking as it primarily evaluates research output and awards (where Times also evaluate teaching, and QS also employer reputation), which we believe represent better the variable than may affect irreplaceability. For the categorization, please see answer above: “Response to categorical variable encoding”

      - "Exact formulas (...) are available in the public repository". What repository do authors mean? The project website? The GitHub repository? Please specify and provide a direct link if possible.

      We added a link to the main text (it was only in the supplementary document). The Supplementary document contains information on how to reproduce the results.

      Reviewer #2 (Recommendations for the authors):

      Specific comments:

      Some methodological details related to the main conclusions of the paper are missing.

      We have extended the methodological section and also better link this article to the companion article.

      - Impact factor: It is unclear which year(s) of journal impact factors were used. Trophy journals are defined as those with an impact factor >50 (Science, Nature, and Cell), but according to Figure 2B, there are only three such journals. Are "trophy journals" limited to these three, or are others included that meet the >50 impact factor threshold?

      These are the 2022 impact factor, we made that clear in the main text. Moreover, only 3 journals in our datasets had an impact factor >50: Nature, Cell, and Science (so the Trophy Journal category is limited to these 3, but not by definition). This is explicit in Table S1: List of journals with impact factor and claim assessment.

      - University ranking: Similarly, please clarify which year(s) of university ranking data were used. Since rankings vary depending on the system (e.g., QS, Times, Shanghai), were the conclusions consistent across multiple ranking sources?

      We used Shanghai Ranking’s 2010 Academic Ranking of World Universities as our ranking of university. Our binning of ranking in categories make the analysis less susceptible to changes in ranking system. We selected the Shanghai ranking as it primarily evaluate research output and awards (where Times also evaluate teaching, and QS also employer reputation), which we believe represent better the variable than may affect irreplaceability.

      Reviewer #3 (Recommendations for the authors):

      Table S4 - for leading author there is a variable of 'historical lab after 1998 continuity' - should that be 1995?

      Correct, we changed this label to Trained in Historical laboratory (Comparison restricted to claims published after 1995) to make it more explicit.

    1. Author response:

      We thank the reviewers for their careful reading of the manuscript and for their insightful comments. Several suggestions relate to a lack of clarity in our presentation, and others propose analyses that will strengthen the impact and robustness of the work. We outline our planned revisions below.

      Reviewer 1:

      We are grateful to the reviewer for appreciating the significance of our work for the treatment of mitochondrial disorders and its future implications in the development of genetic tools and protein design.

      (1) Multiple testing

      Figure 3A–C, Figure 3—figure supplements 1, 2, 4 and 5, Figure 6G and Figure 7F used one-way ANOVA with Tukey's post-hoc test, in which correction is intrinsic; the p-values shown are already adjusted. Our legends did not state this, and we will include this information in the revised manuscript.

      We will apply Benjamini-Hochberg correction across all 400 comparisons, and as individual cells are likely underpowered, will also test aliphatic-to-threonine substitution at the level of residue classes, analogous to the directional analysis in Figure 4.

      (2) Experimental versus predicted structures

      We thank the reviewer for pointing this out. Our description here was not adequately clear. All structural alignments and compositional analyses used AlphaFold2 models; experimental structure availability was used only as an inclusion criterion for the compartment comparisons. We chose predicted models because experimental structures are frequently incomplete, which would bias residue composition. We will state this more prominently and add the source of the structure to the relevant legends.

      (3) Hydrophobicity scale

      We used Kyte-Doolittle for comparability with the prior literature on TMH hydrophobicity in relocated mitochondrial genes, and because it is additive by construction, which the mean-hydrophobicity analyses require. The Hessa scale is defined for insertion of a complete segment and carries substantial position dependence (PMID: 15674282). It is used in Figure 8G because that analysis plots single-residue transfer free energies, which is the scale's intended use and which Kyte-Doolittle, being a hydropathy index does not provide. We will state this rationale in the Methods and in the Figure 8G legend.

      (4) Bootstrap support in the ATP6 tree

      We agree that the low-support nodes warrant discussion, and we should have addressed it in the original text. These nodes (43, 55, 40) concern relationships among Porifera, Ctenophora and Cnidaria, which remain contested in analyses of far larger datasets (PMID: 41686647). The inference of independent relocation does not depend on them: the apicomplexan, chlorophyte and ctenophore sequences are separated by backbone nodes with 100% support. We thank the reviewer for noting that the distinct MTSs in each clade provide independent support, and we will state this explicitly along with an acknowledgement that values below 70 indicate unresolved relationships.

      (5) Core versus peripheral definition

      We sincerely thank the reviewer for pointing this out as our text was unclear regarding this. This was set using the ER TMHs, which provide the largest and best-powered set, and applied unchanged to all other groups. The window was chosen to give comparable numbers of positions in each bin, and so that core positions remain membrane-embedded despite helix tilt and uncertainty in the inferred helix midpoint, both of which are greatest near the termini. We will make the rationale explicit and add a robustness analysis at alternative window sizes, as recommended by the reviewer.

      (6) Literature

      We thank the reviewer for these references and agree they should be discussed. We will incorporate the role of Ser and Thr -containing motifs in TM helix association into the discussion of the biophysical properties of these residues. We will review relevant literature regarding hydrophobicity preferences of the TIM translocon in the context of competition between Sec61 and TIM/TOM insertion, together with the differences between insertion of proteins encoded in the mitochondrial and nuclear genomes. Further, we will also make a version of Figure 8G using the Bothelo and the Kyte-Doolittle scale.

      Reviewer 2:

      We sincerely appreciate the reviewer for their insightful comments, and for suggesting experiments to further strengthen the manuscript.

      (1) Assembly and function of allotopically expressed ATP6

      We agree that mitochondrial localization does not establish functional allotopic expression, and will revise the text so this is unambiguous in our manuscript. Our figures 6 and 7 test whether reduced TMH hydrophobicity allows a mitochondrially encoded protein to reach mitochondria when expressed from the nucleus. Assembly into complex V requires further constraints — correct topology, coordinated assembly with the c-ring, and stoichiometry with nuclear-encoded subunits — for which ATS may not be sufficient.

      Following the reviewer's thoughtful suggestion, we will perform Blue Native PAGE to test whether the imported subunit is incorporated into ATP synthase and to compare the T1, T2 and T3 constructs. We will also add a Discussion section on topology as a distinct barrier and acknowledge the previous efforts at ATP6 allotopic expression.  As the reviewer anticipates, we expect that it can be challenging for the current constructs to be fully functional, but we will test this experimentally following the BN-PAGE assays. If we do not get successful incorporation, we will discuss this in the text as to what caveats may have caused this.

      (2) Expression level confound

      We appreciate with the reviewer’s concern regarding this panel. For context, we would like to point out that the conditions originally shown were chosen so that the comparison runs against our conclusion: the most hydrophobic constructs were expressed at low levels and the ATS constructs at high levels, so expression would be expected to work against the observed difference rather than produce it. We recognize that this rationale was not apparent from the figure.

      To address this concern further, we have the remaining conditions in hand and will show all four constructs at both expression levels, as requested.

      Reviewer 3:

      We are very grateful to the reviewer for their thorough review of the manuscript and for providing constructive feedback.

      (1) Statistical support for threonine enrichment

      We take this point. The strength of statistical support varies across these comparisons, and we will report the p-values with the outliers removed, together with the corrections described under Reviewer 1 point 1. We note that the comparisons are constrained by the number of proteins available there are 13 mtDNA-encoded human IMM proteins, and the E. coli-human comparisons are limited to pairs with detectable homology.

      (2) Enrichment of threonine relative to other residues

      We will report the absolute residue compositions for the E. coli and human sets in a supplementary figure, and examine the relative enrichment of threonine, asparagine and proline more closely.

      (3) Threonine content in Figure 3

      The values in Figure 3C are Tukey-adjusted, and all pairwise comparisons are shown in Figure 3—figure supplement 1. The reviewer is correct that only the Golgi comparison reaches significance. Figure 2 compares each human TMH to its aligned E. coli counterpart, so each protein serves as its own control; Figure 3 compares means across unrelated proteins, where between-protein variation is large relative to the compositional difference. We will make this distinction clearer in the text.

      (4) Hydrophobicity of mtDNA-encoded TMHs in Figure 3

      The reviewer is correct that mtDNA-encoded IMM TMHs do not differ significantly in hydrophobicity from secretory-pathway TMHs. The compartment comparisons test proteins of shared nuclear origin with different destinations; the mtDNA-encoded group is shown for reference, as it differs in both genomic origin and biogenesis route. We will revise the text to specify which mitochondrial class the differences apply to.

      (5) Direction of the Figure 3C and Figure 4G comparisons

      We thank the reviewer for bringing this up. Our current text did not make it clear that these comparisons involved different organisms. The mtDNA-encoded proteins in Figure 4 are drawn largely from jakobids with large mitochondrial genomes, which retain extensive IMM biogenesis machinery and may face weaker constraints on TMH composition. Those in Figure 3C are the 13 human mitochondrially encoded proteins, which do face these constraints and are correspondingly threonine-rich. The apparent difference in direction reflects this rather than an inconsistency in the underlying trend, and we will make it explicit in the text.

      (6) Contribution of ATS to hydrophobicity reduction

      We are grateful to the reviewer for their insightful reading of potential evolutionary solutions to the targeting problem. We agree that ATS accounts for part rather than all of the reduction, and that the role of other hydrophobicity-reducing substitutions should be better defined. We will quantify the share attributable to aliphatic-to-threonine substitution, and for the ATP6 examples, report how much of the reduction remains when the threonine substitutions are reverted.

      (7) ALIVF grouping

      The reviewer is right for noting that phenylalanine does not show substitution towards threonine in the way the other aliphatic residues do in Figure 2H. Phenylalanine is nonetheless depleted in human mitochondrial TMHs alongside isoleucine, valine and alanine (Figure 2C), so the grouping is consistent at the level of composition even though the substitution routes differ. We will also discuss aliphatic-to-valine substitutions, which are largely hydrophobicity-neutral and so do not contribute to the reduction in the same way.

      (8) Literature

      We thank the reviewer for pointing out early attempts at understanding mitochondrial protein biogenesis and allotopic expression. We will incorporate these references into our discussion, specifically in the context of considering factors which could favor TIM/TOM over Sec61 insertion.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1:

      Summary:

      Jeay-Bizot and colleagues investigate the neural correlates of the preparation of, and commitment to, a self-initiated motor action. In their introduction, they differentiate between theoretical proposals relating to the timing of such neural correlates relative to the time of a recorded motor action (e.g., a keypress). These are categorised into 'early' and 'late' timing accounts. The authors advocate for 'late' accounts based on several arguments that align well with contemporary models of decision-making in other domains (for example, evidence accumulation models applied to perceptual decisions). They also clearly describe prevalent methodological issues related to the measurement of event-related potentials (ERPs) and time-frequency power to gauge the timing of the commitment to making a motor action. These methodological insights are communicated clearly and denote potentially important limitations on the inferences that can be drawn from a large body of existing work.

      To attempt to account for such methodological concerns, the authors devise an innovative experiment that includes an experimental condition whereby participants make a motor action (a right-hand keypress) to make an image disappear. They also include a condition whereby the stimulus presentation program automatically proceeds at a set time that is matched to the response timing in a previous trial. In this latter condition, no motor action is required by the participant. The authors then attempt to determine the times at which they can differentiate between these two conditions (motor action vs no motor action) based on EEG and MEG data, using event-related potential analyses, time-frequency analyses, and multivariate classifiers. They also apply analysis techniques based on comparing M/EEG amplitudes at different time windows (as used in previous work) to compare these results to those of their key analyses.

      When using multivariate classifiers to discriminate between conditions, they observed very high classification performance at around -100ms from the time of the motor response or computer-initiated image transition, but lower classification performance and a lack of statistically significant effects across analyses for earlier time points. Based on this, they make the key claim that measured M/EEG responses at the earlier time points (i.e., earlier than around -100ms from the motor action) do not reliably correlate with the execution of a motor action (as opposed to no such action being prepared or made). This is argued to favour 'late' accounts of motor action commitment, aligning with the well-made theoretical arguments in favour of these accounts in the introduction. Although the exact time window related to 'late' accounts is not concretely specified, an effect that occurs around -100ms from response onset is assumed here to fall within that window.

      Importantly, this claim relies on accepting the null hypothesis of zero effect for the time points preceding around -100ms based on a somewhat small sample of n=15 and some additional analyses of individual participant datasets. Although the authors argue that their classifiers are sensitive to detecting relevant effects, and the study appears well-powered to detect the (likely to be large magnitude) M/EEG signal differences occurring around the time of the response or computer-initiated image transition, there is no guarantee that the study is adequately sensitive to detect earlier differences in M/EEG signals. These earlier effects are likely to be more subtle and exhibit lower signal-to-noise ratios, but would still be relevant to the 'early' vs 'late' debate framed in the manuscript. This, along with some observed patterns in the data, may substantially reduce the confidence one may have in the key claim about the onset timing of M/EEG signal differences.

      We thank the reviewer for this thorough summary and for providing the opportunity to clarify our claims in light of the concerns identified by this review. Our key claim we make is not that there are no early signals. Rather it is that the well-known and reliable signals (e.g. the RP) that could be construed as evidence for early commitments do not have the characteristics of early commitment signals (i.e. they are not predictive). Based on our main results (Figure 3) we can classify the presence of those early signals using traditional approaches rather well (time-based approach), but when we control for autocorrelation in the data (task-based approach), this classification performance goes away – indicating that those particular signals might not contain movement or intention specific information. Further, we do have evidence that our paradigm was sensitive enough to detect small differences between the two conditions as is evidenced in Appendix 1, Figure 12 with above chance AUC right after trial start, a period during which participants likely recall the trial type (Active vs. passive). We have now added individual peak AUC to the figure to illustrate that our approach was sensitive to these differences (See Figure S12).

      We do however fully agree that absence of evidence is not evidence of absence. We have therefore effected the following changes to mitigate misinterpretations of our results: Abstract: “…it was not useful in predicting movement.” “ “Our results substantially constrain the interpretation that early EEG antecedents, including the RP, reflect a commitment to act, instead indicating that EEG-detectable evidence consistent with such a commitment emerges closer to movement onset, in line with the timing of conscious intention and the capacity for late movement inhibition.

      Introduction:

      “We show that, once appropriate controls are introduced, there is little evidence that cortical EEG contains reliable predictive information much earlier than ~100 ms before movement. Those results better align with late-decision accounts, which posit that the final neural commitment to initiate movement arises very close to the time of movement onset, in the context of self-initiated movements that are not pre-planned.”

      “[…] and at odds with the presence of predictive early signals indicative of a commitment to move – from the vantage point of cortical activity.”

      Discussion:

      “Instead, the data better align with the more recent late-decision accounts”

      “We show here that the data, once properly controlled for, do not support this early neural commitment.”

      “Importantly, the significance of these findings lies not in whether premovement neural activity exists, but in what that activity can legitimately be interpreted to reflect. Our results suggest that although early ramping activity precedes self-initiated movement, this ramping activity may not reflect a true commitment to initiate movement. Instead, they may reflect broader preparatory neural dynamics that bias action likelihood without determining action outcome. Importantly, our findings do not establish whether the relationship between premovement activity, intention, and action is causal or merely correlational. Rather, they constrain interpretations that equate the presence of early neural antecedents with evidence that a specific voluntary decision has already been unconsciously determined one or more seconds before movement onset.”

      Figure S12

      Added individual peak AUCs post slide appearance

      Caption: “Individual peaks after the appearance of the slide are displayed as black circular dots in the figure.”

      Notably, there is some indication of above-chance (above 0.5 AUC) classification performance at time points earlier than -100ms from the response, as visible in Figure 3A for the task-based EEG analyses (EEG OC dataset, blue line). While this was not statistically significantly above chance for their n=15 sample, these results do not appear to be clear evidence in favour of a zero-effect null-hypothesis. In Figures 2A-B, there are also visible differences in the ERPs across conditions, from around the time that motor action-related components have been previously observed (around -500ms from the response). The plotted standard errors in the data are large enough to indicate that the study may not have been adequately powered to differentiate between the conditions.

      We agree with the reviewer that our data does not support the strong claim that there are no early signals. In particular, we agree that the absence of statistically significant decoding does not demonstrate the absence of any underlying signal, especially for potentially subtle effects. However, our central claim is more specific. We do not argue that no early signals exist, rather, we argue that signals previously taken to be evidence of early commitment to move (like the RP) do not exhibit the characteristics expected of a cortical EEG signature of commitment: namely being predictive.

      The slow ramping that we observed, despite its early onset, was not reliably predictive of upcoming movement. It is precisely the contrast between the early presence of ERPs without reliable early decoding that supports our main claim that those signals do not reflect commitment-like processes.

      Classifiers specifically designed to pick up the clearly observable slow ramping activity (e.g. basic-slope LDA in Figure 5) or trained on a large search space of features (e.g. Haar-Adaboost) failed to produce strong or reliable early decoding.

      Importantly, Haar-AdaBoost was not restricted to slow ramping activity or the RP. Its feature space included spatial, temporal, and time-frequency information, allowing it to detect other potentially informative EEG features beyond slow ramping activity, including changes in spectral power. Our key claim is not that no early neural signals exist. Rather, we found little reliable early predictive information across a broad range of EEG features. Our classifiers were sensitive to slow ramping activity (like the RP), spatial patterns, and changes in spectral power, yet robust discrimination emerged only close to movement onset. Thus, any earlier commitment signal would need either to differ from the RP and the other features accessible to our analyses, or to be largely invisible to scalp EEG and MEG. We have revised the abstract and selected sections to clarify that our findings concern early predictive information detectable by our classifiers in EEG more broadly, including but not limited to the RP. These revisions do not rule out an early neural commitment represented in signals inaccessible to EEG or MEG or to our classifiers.

      Abstract:

      “Although early ramping activity was present, our classifiers found little reliable predictive information in the EEG until about 100 ms before movement, when classification accuracy rose abruptly.”

      “Our results substantially constrain the interpretation that early EEG antecedents, including the RP, reflect a commitment to act, instead indicating that EEG-detectable evidence consistent with such a commitment emerges closer to movement onset, in line with the timing of conscious intention and the capacity for late movement inhibition.”

      Introduction:

      “Here, we introduce a paradigm that tests whether early antecedents detectable in EEG—including the RP, but not limited to slow ramping activity—distinguish epochs culminating in self-initiated movement from well-matched epochs not culminating in movement, thereby assessing whether early EEG activity contains reliable outcome-specific information consistent with a commitment to act.”

      “Thus, the analysis was not restricted to the RP nor to other slow potentials, but could exploit temporal, spatial, and spectral differences throughout the EEG signal.”

      Results:

      “Our results show that the slow buildup observed in movement-locked averages was not reliably predictive under more carefully controlled conditions (i.e. when classified against a control condition using the task-based approach). More broadly, classifiers sensitive to diverse temporal, spatial, and spectral features found little reliable early predictive information in the EEG.”

      Discussion:

      “Our results cannot rule out the possibility of an early neural commitment that is undetectable in EEG or MEG. Rather, neither the RP nor slow ramping nor other early EEG/MEG features accessible to our classifiers exhibited reliable commitment-like predictability. Any earlier commitment signal would therefore need to be distinct from the RP and either largely invisible to EEG/MEG or too weak, distributed, or otherwise inaccessible for the present decoding methods to recover.”

      Further, we agree that our study may be underpowered to detect extremely small early effects. However, several observations suggest that any such effects are weak and unlikely to reflect a robust commitment. First, the slight early above-chance decoding visible in Figure 3A is primarily driven by a small number of participants and disappears following outlier exclusion (Figure S7). Second, even when present, early decoding remained extremely weak (approximately AUC ≈ 0.52–0.55), far below the level expected from a stable neural commitment to a specific action outcome. Third, when examining the earliest time points at which single trials became consistently and continuously classifiable until movement onset (EDT analysis), decoding emerged only very close to movement onset (~100 ms on average, with the most extreme participant remaining below ~200 ms). This pattern was additionally replicated in the now-expanded Libet dataset (N = 8; Figure S4), despite early onset of low-decoding performance at the group level, single trials EDTs or non-outlier group onsets were also very close to movement onset.

      Importantly, these conclusions were robust across multiple classifier architectures, parameter choices, and preprocessing pipelines. We additionally reprocessed the EEG data using a 0.05–80 Hz band-pass filter, a 58–62 Hz notch filter, and down-sampling to 512 Hz, following the reviewer’s recommendations (below). Although this preprocessing marginally increased early above-chance decoding, the effect again depended primarily on a single outlier participant (participant 6), and single-trial EDTs remained below ~200 ms even for the outliers (Figure S14). Excluding this participant eliminated the apparent early decoding.

      We therefore agree that early signals may exist. However, our findings suggest that the classical premovement ramping previously interpreted as evidence for an early decision does not behave like a commitment signal. At best, the early decoding observed in outliers could reflect weak biases or task compliance rather than early commitments to a specific course of action. Our conclusions do not depend on proving the complete absence of early information. Rather, they depend on showing that the early signals traditionally invoked in support of early-decision accounts lack the reliability and predictive strength that would be expected if a neural commitment to act were represented by a stable EEG signal.

      In addition to the changes presented earlier, we have made the following changes to the manuscript to accommodate the above:

      Introduction:

      “Although very weak sustained above-chance classification was observed at early time points (Figure 3), these effects were driven by outliers (Figure S7). Crucially, this above-chance classification does not provide evidence for a commitment to initiate movement. Instead, it indicates that upcoming movements can be weakly discriminated from a matched control condition only in a small subset of participants and trials. Moreover, classifiers trained exclusively on slow ramping activity performed comparably—but not better—during the pre-movement period (Figure 5).”

      Results:

      “…we could decode only slightly better than chance…”

      “…could only be classified reliably very close to movement onset…”

      “Indeed, once outliers were excluded, classification remained at chance until very close to movement onset (Figure S7).”

      “This single-trial EDT suggests that commitment, defined as sticking to a course of action, arises only late in time, close to movement onset.”

      “This single-trial EDT suggests that commitment, defined as sticking to a course of action, arises only late in time, close to movement onset.”

      “Additionally, while ramping activity is observable in multiple participants (Figure S3) it disappears when a high-pass filter with a 0.1 Hz cutoff is applied (Figure S14). This suggests that the effect may be driven by very slow fluctuations, slower than typical anticipatory signals, and may therefore reflect non-neural or artifactual processes.”

      Discussion:

      “, when using a classifier based solely on these slow ramping signals (basic slope LDA), performance also hovered around chance levels before movement, indicating that early ramping activity is not predictive of upcoming movements (Figure 5).”

      “Some readers may note a slight above-chance performance in early time windows (Fig. 3). However, this effect was driven by outliers (Fig. S7). Even when present, such weak performance (e.g., AUC ≈ 0.53) falls far short of what would be expected from a reliable neural signature of commitment. Moreover, analyses of EDTs derived from correct classifications at the single-trial level show that correct predictions emerge and are sustained only very close to movement onset. This indicates that the underlying predictive signal itself arises only late. Together, these results suggest that the signal supporting early classification is not commitment-like.”

      “In our primary analyses, we deliberately avoided filtering to preserve even the slowest fluctuations in the signal. However, this choice may have allowed low-frequency noise to remain, potentially obscuring smaller effects. To address this possibility, we re-analyzed the data using a 0.05–80 Hz band-pass filter, applied a band-stop filter to attenuate line noise, and down-sampled the data to 512 Hz (rather than 500 Hz, to minimize loss of frequency information). The filtered analysis (Fig. S14) revealed broadly similar patterns, with two notable differences: the slow drift in the passive ERP was no longer present, and group-level AUC onsets (both by-eye and 90\% criteria) appeared earlier. However, these early onsets were driven by a single outlier (participant 6; figure S14). When considering mean EDTs at the participant level, or when excluding this outlier, onset estimates remained late (figure S14) and consistent with our main findings (Figure 3).”

      New figure in the appendix Figure S14

      New figure with filtered data

      Caption: “Decoding performance and MRCPs from filtered EEG data. EEG data were sampled at 512 Hz to avoid loss of frequency content during downsampling. Line noise was attenuated using a 58–62 Hz band-stop filter, and signals were further filtered using a 0.05–80 Hz one-pass zero-phase FIR filter (FieldTrip, firws) to reduce artifactual activity. (A) Grand-average movement-related cortical potentials (MRCPs) at electrode C3 for active (blue) and passive (red) trials, aligned to slide transition (t = 0; dotted gray line). Shaded areas indicate the standard error of the mean. MRCP onsets are marked by dashed gray lines. (B) Grand-average time course of validation AUC (10-fold cross-validation) for the task-based decoding approach (blue line). The x-axis reflects the leading edge of the sliding window relative to slide transition (t = 0; dotted gray line). Shaded areas indicate the standard error of the mean. AUC onsets are marked by dashed gray lines. Despite early apparent onsets at the group level (AUC onset-by-eye and 90% method > 1 s before movement), classification performance remains near chance and does not exceed ~0.55 until close to movement onset. At the participant level, both AUC onsets and single-trial EDTs average -0.09 s. Excluding participant 6 shifts group-level AUC onset estimates to -0.44 s (by eye) and -0.32 s (90% onset method), indicating that early onsets are driven by outliers.”

      Although the authors acknowledge this limitation in the discussion section of their manuscript, their counter-argument is that the classifiers could reliably differentiate between conditions at time points very close to the motor response, and in the time-based analyses where substantive confounds are likely to be present, as demonstrated in a set of analyses. Based on this data, the authors imply that the study is sufficiently powered to detect effects across the range of time points used in the analyses. While it's commendable that these extra analyses were run, they do not provide convincing evidence that the study is necessarily sensitive to detecting more subtle effects that may occur at earlier time points. In other words, the ability of classifiers (or other analysis methods) to detect what are likely to be very prominent, large effects around the time of the motor response does not guarantee that such analyses will detect smaller magnitude effects at other time points.

      In summary, the authors develop some very important lines of argument for why existing work may have misestimated the timing of neural signals that precede motor actions. This in itself is an important contribution to the field. However, their attempt to better estimate the timing of such signals is limited by a reliance on accepting the null hypothesis based on non-statistically significant results, and arguably a limited degree of sensitivity to detect subtle but meaningful effects.

      Strengths:

      This manuscript provides compelling reasons why existing studies may have misestimated the timing of the neural correlates of motor action preparation and execution. They provide additional analyses as evidence of the relevant confounds and provide simulations to back up their claims. This will be important to consider for many in the field. They also endeavoured to collect large numbers of trials per participant to also examine effects in individuals, which is commendable and arguably better aligned with contemporary theory (which pertains to how individuals make decisions to act, rather than groups of people).

      The innovative control condition in their experiment may also be very useful for providing complementary evidence that can better characterise the neural correlates of motor action preparation and commitment. The method for matching image durations across active and passive conditions is particularly well thought-out and provides a nice control for a range of potential confounding factors.

      Weaknesses:

      There is a mismatch between the stated theoretical phenomenon of interest (commitment to making a motor action) and what is actually tested in the study (differences in neural responses when an action is prepared and made compared to when no action is required). The assumed link between these concepts could be made more explicit for readers, particularly because it is argued in the manuscript that neural correlates of motor action preparation are not necessarily correlates of motor action commitment.

      We thank the reviewer for highlighting this important conceptual distinction. When proposing a matched control condition, the primary requirement was that the two conditions differ in the presence versus absence of a commitment to act. We argue that our two conditions (active vs. passive) satisfy this criterion. In the active condition, participants are instructed to execute a self-initiated motor action to advance from one slide to the next. In the passive condition, participants are not preparing or committing to any action during the slideshow.

      We agree, however, that the two conditions are not matched in all other respects. Most notably, as pointed out by the reviewer, they also differ in the presence versus absence of movement itself as well as of accompanying movement preparation. As such, any differences observed between the conditions could in principle reflect motor-related processes, intention-related processes, or both. Importantly however, this ambiguity does not weaken our main conclusion. If early commitment-related signals were present and robust, they should still contribute to reliable discrimination between conditions. Yet despite the presence of visible premovement ramping activity in the averaged ERPs, classification remained weak and unreliable until very close to movement onset.

      We have made the following changes to the manuscript accordingly:

      Introduction:

      “While the two conditions differ in the presence or absence of movement, they also differ in the presence or absence of an intention to move. As such, any early differences, if present, could reflect either motor-related or intention-related processes. However, this ambiguity is not a concern here, as we only observe differences at later time points.”

      Discussion:

      “A recent study (Derchi et al., 2023) contrasted volitional blinks with spontaneous blinks, thereby keeping the occurrence of movement constant while varying the presence of intention. Such an approach would avoid the movement-versus-no-movement contrast inherent to our paradigm. Importantly however, matching motor outcomes across conditions would likely make classification substantially more difficult, since motor-related information could no longer contribute to decoding performance.”

      As mentioned in the summary, the main issue is the strong reliance on accepting the null hypothesis of no differences between motor action and computer initiation conditions based on a lack of statistically significant results from the modest (n=15) sample. Although a larger sample will increase measurement precision at the group level, there are some EEG data processing changes that could increase the signal-to-noise ratio of the analysed data and produce more precise estimates of effects, which may improve the ability to detect more subtle effects, or at least provide more confidence in the claims of null effects.

      See our responses above regarding accepting the null. Also, we included an additional 5 participants to the Libet task (See updated Figure S4) to slightly improve our sample size. Although as previously stated in our manuscript, the number of trials matter more than the number of participants for a decoding study and with 1400 trials representing about 4 hours of data collection, should such early signals exist yet remain undetectable even with extensive trial counts and multiple decoding approaches, our results would suggest that EEG and MEG may have limited utility for studying them.

      We have emphasized this point in our revised version of the manuscript:

      Discussion:

      “Some of our participants contributed up to 1400 trials, totaling up to 4 hours of data collection over 2 to 4 sessions in the EEG or MEG. Should such early signals exist yet remain undetectable even with extensive trial counts and multiple decoding approaches, our results would suggest that EEG and MEG may have limited utility for studying them.”

      “[…] in eight additional participants and we found more or less identical results […]”

      Figure S4:

      Figure was updated to reflect an additional 5 participants

      Caption updated to “AUC and ERP of Libet-task participants. Machine learning and ERP results for eight participants that we ran with a spontaneous movement initiation task based on Libet et al. (1983). (A) Readiness potential at Cz for the eight participants. In blue are the averages of the press trials and in red the averages of the no-press trials. Time 0 is the time of the trial end (dotted black line). Shaded areas are the standard errors of the mean. RP onsets using the 3 methods on press trials are reported and accordingly labeled (dashed grey lines) (B) Validation AUC for the eight participants using the task-based approach. Time 0 is the time of slide transition (dotted gray line). The AUC is aligned to the leading edge of the sliding window. Shaded areas are the standard errors of the AUC. AUC onsets using the three onset detection methods are reported and labeled accordingly (dashed grey lines). Our slideshow paradigm, while providing a more ecologically valid task, is agnostic as to the spontaneity of the participants’ movement decisions. To ensure that our task would generalize to more standard paradigms in the field of self-initiated action, we performed our analyses on data from a spontaneous voluntary movement paradigm based on (Libet et al., 1983). Here we collected eight further participants (4 female, 4 males, age M=24, 1 left-handed, 7 right-handed). They performed 350 trials of a task similar to the task performed by participants at OC except for the fact that there were no pictures, simply a fixation cross. Furthermore, the instructions for the manual trials were for participants to wait for a minimum of 3 seconds then start monitoring inwards for an urge to move. Whenever they detected such urge they were instructed to press as abruptly and spontaneously as possible, ending the trial. In the automatic trials, participants were instructed to do the same (monitor introspectively for an urge), except that they should not act on the urge if/when they felt it, but rather to wait for the next urge passively, and repeat such process until the trial ended automatically. This paradigm is much closer to the seminal studies on self-initiated actions (Libet et al., 1983; Kornhuber & Deecke., 1965). Here movements are performed spontaneously, and the matched condition (automatic) is identical in most regards apart from it not containing or terminating in a movement. All preprocessing and data analysis applied were the same. We found no strong qualitative difference with our main result (Figures 2A and 3A), suggesting that our task would generalize to other types of self-initiated actions.”

      First, it is stated in the EEG acquisition and preprocessing section that the 64-channel Biosemi EEG data were recorded with a common average reference applied. Unless some non-standard acquisition software was used (of which we are not aware exists), Biosemi systems do not actually apply this reference at recording (it is for display purposes only, but often mistaken to be the actual reference applied). As stated in the Biosemi online documentation, a reference should be subsequently applied offline; otherwise, there is a substantial decrease in the signal-to-noise ratio of the EEG data, and a large portion of ambient alternating current noise is retained in the recordings. This can be easily fixed by applying a referencing scheme (e.g., the common average reference) offline as one of the first steps of data processing. If this was, in fact, done offline, it should be clearly communicated in the manuscript.

      We did perform common average reference during the data preprocessing (lines 200-204 Slideshow2025/preprocess.m at main · lucasjeaybizot/Slideshow2025 · GitHub). We however clarified this description in the methods to clarify that this was performed offline:

      Methods:

      “We recorded EEG using a 64-channel BioSemi system keeping electrode offsets below 10 mV.”

      The CAR was moved down for clarity.

      “Data was re-referenced to the common average offline.”

      In addition, the data is downsampled using a non-integer divisor of the original sampling rate (a 2,048 Hz dataset is downsampled to 500 Hz rather than 512 Hz). Downsampling using a non-integer divisor is not recommended and can lead to substantial artefacts in raw data as a result, as personally observed by this Reviewer in Biosemi data.

      We had initially downsampled to 500 Hz to keep our analyses consistent from PF to OC. However, this is a very valid point, we have therefore re-analyzed the data using a downsampling to 512 Hz. Results did not change qualitatively nor quantitatively. Descriptions can now be found in the new supplementary Figure S14 and as referenced in the main manuscript (see changes below).

      Discussion:

      “In our primary analyses, we deliberately avoided filtering to preserve even the slowest fluctuations in the signal. However, this choice may have allowed low-frequency noise to remain, potentially obscuring smaller effects. To address this possibility, we re-analyzed the data using a 0.05–80 Hz band-pass filter, applied a band-stop filter to attenuate line noise, and downsampled the data to 512 Hz (rather than 500 Hz, to minimize loss of frequency information). The filtered analysis (Fig. S14) revealed broadly similar patterns, with two notable differences: the slow drift in the passive ERP was no longer present, and group-level AUC onsets (both by-eye and 90% criteria) appeared earlier. However, these early onsets were driven by a single outlier (participant 6; figure S14). When considering mean EDTs at the participant level, or when excluding this outlier, onset estimates remained late (figure S14) and consistent with our main findings (Figure 3).”

      Finally, although a 30 Hz low-pass filter is applied for visualisation purposes of ERPs, no such filter is applied prior to analyses, and no method is used to account for alternating current noise that is likely to be in the data. As noted above, much of the alternating current noise will be retained when an offline reference is not applied, and this is likely to further degrade the quality of the data and reduce one's ability to identify subtle patterns in EEG signals. Changes in data processing to address these issues would likely lead to more precise estimates of EEG signals (and by extension differences across conditions).

      In order to assess whether line noise or the absence of filtering in our main analyses could explain the absence of strong early decoding, we re-processed our data with a low pass filter at 80 Hz, a high pass filter at 0.01 Hz and a notch filter from 58 to 62 Hz. We further downsampled our data from 2048 Hz to 512 Hz to maximally retain spectral features. We then ran this preprocessed data through our algorithm. These changes are all comprised in new figure S14 and described above (see response to previous comment).

      With regard to possible effects extending hundreds of milliseconds before the response, it would be helpful for the authors to more precisely clarify the time windows associated with 'early' and 'late' theories in this case.

      We agree this is a very important clarification for the readers and as it stands is only implied in the literature. We now formalized it as follows, an early signal is a signal that would precede the time participants become aware of their intentions to move. In the case of self-initiated action, a recent meta-analysis suggests the lower bound of the 95% predictability intervals lands at -257 ms (Braun et al., 2021).

      We have made the following modifications to the manuscript to reflect this definition:

      Introduction:

      “According to early-decision accounts, decisions (i.e., commitments to a course of action) occur early at the neural level, before participants typically report becoming aware of them. The lower bound of meta-analytic estimates of awareness, at ~250 ms before movement onset (Braun et al., 2021), can be used as a pragmatic threshold to classify neural signals as “early” (more than 250 ms before movement onset) or “late” (less than 250 ms before movement onset).”

      “[…] well in advance, prior to the typical range during which participants report becoming aware of having decided (Braun et al., 2021).”

      “[…] in time to movement onset, during the typical range during which participants report becoming aware of having decided (Braun et al., 2021).”

      Discussion:

      “Early-decision accounts posit that there is an early neural commitment to a decision that occurs prior to the subjective awareness of the decision.”

      The EEG data that would be required to support 'early' theories is also not made sufficiently clear. For example, even quite early neural correlates of motor actions in this task (e.g., around -500ms from the response, or earlier) could still be taken as evidence for the 'late' theories if these correlates simply reflect the accumulation of evidence toward making a decision and associated motor action, as implied by the Leaky Stochastic Accumulator model described by the authors. In other words, even observations of neural correlates of motor action preparation that occur much earlier than the response would not constitute clear evidence against the 'late' account if this neural activity represents an antecedent to a decision and action (rather than commitment to the action), as the authors point out in the introduction.

      We thank the reviewers for pointing out a set of two very pivotal assumptions in our work: early models predict that there are early commitment signals and that those signals both, (1) precede the subjective experience of the decision and, (2) are highly specific to the decisions’ outcome.

      Assumption (1) rests on a set of findings that participants report being first aware of their decision up until very close to movement onset (Libet et al., 1983) which, according to a recent meta-analysis occurs up to around ~250 ms before movement onset (Braun et al., 2021). It is additionally supported by a large corpus of literature on movement inhibition: participants can inhibit their movement up until within ~225 ms from executing them (Vergbruggen et al, 2019). A similar time is also reported specifically for self-paced arbitrary movements (Schultze-Kraft et al., 2016). As such we take it that early-decision accounts, to satisfy (1), predict the early signal to be present more than ~250 ms before movement onset.

      Assumption (2) relates to the conceptualization of decisions. Early-decision accounts posit that decisions are made early. A decision can be viewed as an act of settling on a plan of action. That is, unless new information interferes, the plan of action that was settled on by the act of deciding will be carried out. Maintaining this settled plan of action until it is carried out implies that once a decision has occurred, its accompanying plan of action must be maintained somewhere in the brain. In other words, there should be a brain signal that could in theory be used to predict with high accuracy an upcoming action. While ‘high accuracy’ is a vague concept, another prediction is that it should be equally useful over time to predict the decision, in other words, once a trial begins being correctly classified, it should remain so until movement onset.

      In our paradigm, evidence for early theories would therefore be EDTs (Figure 3B) that occur more than 250 ms before the slide transition.

      We have added the following section to clarify this in our manuscript:

      Discussion:

      “Evidence for early accounts would require EDTs that occur earlier than the ~250 ms lower boundary of meta-analytic estimates of the subjective awareness of the decision (Braun et al., 2021). In our data, no participants' EDTs (Figure 3B) occurred earlier than 250 ms before slide transition. While AUC onsets computed on the group data did occur earlier than 250 ms (Figure 3A), this was driven by outliers (Figure S7) and not present at the individual level.”

      In addition, there is some discrepancy regarding the data that is used by the classifiers to differentiate between the conditions in the EEG data and the claims about the timing of neural responses that differentiate between conditions. Unless we reviewers are mistaken, the Sliding Window section of the methods states that the AUC scores in Figure 3 are based on windows of EEG data that extend from the plotted time point until 0.5 seconds into the past. In other words, an AUC value at -100ms from the response is based on classifiers applied to data ranging from -600 to -100 milliseconds relative to the response. In this case, the range of data used by the classifiers extends much earlier than the time points indicated by Figure 3, and it is difficult to know whether the data at these earlier time points may have contributed (even in subtle ways) to the success of the classifiers. This may undermine the claim that neural responses only become differentiable from around -100ms from response onset. The spans of these windows used for classification could be made more explicit in Figure 3, and classification windows that are narrower could be included in a subset of analyses to ensure that classifiers only using data in a narrow window around the response show the high degree of classification performance in the dataset. If we are mistaken, then perhaps these details could be clarified in the method and results sections.

      The reviewer correctly describes the plotted data. However, it is important to note that because of two reasons (1 and 2 below), the concern of the onset of the AUC of the leading edge of the sliding window not reflecting the onset of the outcome-specific brain activity, can be substantially reduced. (1) The analysis we conducted is a sliding window, which means that an onset detected at -100 ms is above chance performance when classifying data taken from -600 to -100 ms but no such classification for the previous window from -620 to -120 ms. While this could mean that the entire window of activity was necessary for classification, it also suggests that only when incorporating data from the -120 ms to -100 ms window can the classifier perform above chance. (2) We used Haar features of different sub-window length combined with AdaBoost. AdaBoost selects the most informative features given the data, under this circumstance an increase in performance occurring only when including data from -120 ms to 100 ms indicates that data from that window was necessary for this increase in performance.

      Additionally, to ensure more precision we now tested window of 250 ms and 100 ms (updated figure S11), the results of which align with what we previously report.

      Discussion:

      “Another potential concern is that predictive performance observed in wide sliding windows (e.g., -600 to -100 ms) could reflect information present as early as the beginning of the window. However, this interpretation is inconsistent with the temporal profile of decoding performance. For example, if the -620 to -120 ms window is non-predictive whereas the -600 to -100 ms window becomes predictive, the most parsimonious interpretation is that predictive information emerges near the newly included time points close to -100 ms, rather than being present throughout the entire window. This interpretation is further supported by the comparable performance observed across different window widths (figure S11), suggesting that the classifier was able to localize informative features within broader windows.”

      Figure S11

      Figure was updated to include analysis run with 250 ms window and 100 ms window Figure caption: “Evaluation of the sliding window widths. (A) Average validation AUC of Haar-Adaboost of the three participants of the PF EEG dataset using a sliding window (light blue) or growing window approach (pink) with the task-based approach. Time 0 is the time of slide transition (dotted gray line). The AUC is aligned to the leading edge of the sliding window. Shaded area is the standard error of the mean. A growing window analysis is similar to the sliding window analysis except that at each iteration, instead of sliding the window, the window width is increased by 0.02 s. This means that for an epoch beginning 3 s before movement, the window of analysis for the leading edge aligned to the slide transition would be 3 s wide from -3 s to 0 s (while for the sliding window method it would be 0.5 s wide from -0.5 s to 0 s). While it enables the capture of more patterns, it is a computation heavy analysis. To ensure that we were not missing out on some substantial longer-term patterns with sliding window, we ran a growing window on our PF EEG data. We found no improvement of using growing window over sliding window. (B) Average validation AUC of Haar-AdaBoost on the main OC EEG dataset using sliding windows of 100 ms (light blue), 250 ms (medium blue), and 500 ms (dark blue). Shaded areas represent the standard error of the mean. While clear classification differences emerged following movement onset, no substantial differences were observed prior to movement onset. This indicates that the 500 ms window was not too large to obscure finer temporal patterns. Furthermore, these results suggest that Haar-AdaBoost can identify localized informative features within larger windows, supporting the interpretation that the leading edge of the sliding window approximates the earliest time point at which predictive information becomes available.”

      Reviewer #2:

      Summary:

      The authors set out to investigate how well the onset of a self-initiated movement could be predicted at different times prior to action onset. To do so, they collected EEG and MEG data across 15 human participants who watched natural landscape images on a screen. These participants performed active self-initiated movements or observed passive actions to have a new image appear. By comparing the neural activity prior to active and time-matched passive actions, the authors found that even though a build-up of neural activity is visible close to 1s prior to action, action onset could only be reliably predicted around 100ms prior to action. These results confirm what was already suggested in previous literature: the commitment to action is only clear from the late stages in the visible neural ramp-up to action onset.

      Strengths:

      (1) The paper presents a well-thought-out methodology to assess the predictive value of neural activity prior to a self-initiated movement and passively observed action, while keeping all other experimental factors identical. This methodology can be applied outside the specific scope of this paper as well, in efforts to assess the correspondence of a neural signature with an observed behavior.

      (2) The results are a strong confirmation of what was suggested less clearly in previous research (Trevena & Miller, 2010, Consciousness & Cognition; Schmidt et al., 2016, Neuroscience & Biobehavioral Reviews; Travers et al., 2020, NeuroImage).

      Weaknesses:

      (1) Although the authors conducted a solid confirmatory study, the importance of this confirmation is less clear to me. How do the current results change our interpretation of the relation between conscious intention and neural preparation for action? Do these results affect our interpretation of free will? Why does it matter at all whether we see neural preparatory activity prior to the report of a conscious intention to act, or prior to action observation? This study does not clarify the relationship between the observed neural phenomenon, the action or the experienced intention. It does not explain whether this relation is causal, correlational or something else.

      We thank the reviewer for their review. While it was previously suggested that the commitment to action comes late (Schultze-Kraft et al. 2016) and mechanisms were proposed to explain the early ramp-up in light of this late commitment (Schurger et al., 2012; Schmidt et al., 2016). Our main contribution is not merely confirmatory. Rather, our study introduces a matched control condition together with a classifier-based framework specifically designed to test whether early premovement activity is sufficiently predictive to qualify as a commitment-like signal.

      Trevena & Miller 2010 differ largely from our approach, their control condition being matched for ‘decision’ but differing only in motor output. Their results are therefore still consistent with the RP being a decision-following signal. In contrast, our paradigm directly tests whether the early ramping activity reliably distinguishes epochs culminating in self-initiated movement from well-matched epochs not culminating in movement. Travers et al. 2020, while more directly testing the question of the specificity of the RP to self-initiated actions, provided ambiguous and contradictory interpretations, stating both that “[RP-like events] occur to the same degree in control data” and that “these events do not support the hypothesis that Readiness Potentials happen in the absence of action” with results allowing for multiple interpretations. Our study addresses this ambiguity directly by testing whether these early signals contain reliable outcome-specific information predictive of an upcoming action.

      More broadly, while our findings are relevant to debates surrounding free will, our primary goal is neuroscientific rather than philosophical. Specifically, we address whether the signals traditionally interpreted as evidence for early decisions actually possess the properties expected of an early commitment signal. Our findings suggest that they do not.

      Our data therefore invites a reinterpretation of the signals previously taken to challenge views of free will that require decisions to be made consciously. Specifically, the slow ramping signals traditionally interpreted as markers of decisions occurring very early in the brain do not exhibit the characteristics expected of a commitment-like signal. Rather than reflecting a stable and outcome-specific commitment to act, these early ramping signals may instead reflect broader preparatory dynamics that bias action likelihood without determining action outcome.

      Our findings do not establish whether the relationship between premovement neural activity, intention, and action is causal or merely correlational. Addressing that question would require causal interventions beyond the scope of the present study. However, if early premovement activity were causally related to a settled commitment to act, one would expect it to contain strong and reliable predictive information regarding the upcoming action outcome. Our results do not support this account.

      To clarify these points further, we have revised the manuscript accordingly and added the following text to the Introduction and Discussion sections.

      Intoduction:

      “Previous work showed that these early ramping signals were not specific to the outcome of a motor decision (Trevena & Miller, 2010). However, because their analyses remained time-locked to decision outcomes, they could not directly test whether the observed slow buildup specifically reflected a commitment-like process. Related work further suggested that RP-like patterns can emerge elsewhere in ongoing neural activity as features of spontaneous low-frequency fluctuations (Travers et al., 2020). Here, we introduce a paradigm that explicitly tests whether these early ramping signals distinguish epochs culminating in self-initiated movement, where a motor intention is present, from well-matched epochs not culminating in movement, where no motor intentions were present, thereby assessing whether they reliably reflect a commitment to act.”

      Discussion:

      “Our data therefore invites a reinterpretation of the signals previously taken to challenge views of free will that require decisions to be made consciously. Specifically, the slow ramping signals traditionally interpreted as markers of decisions occurring very early in the brain do not exhibit the characteristics expected of a commitment-like signal. Rather than reflecting a stable and outcome-specific commitment to act, this early antecedent ramp-like buildup may instead reflect broader preparatory dynamics that bias action likelihood without determining action outcome.”

      (2) Whereas Derchi et al. (2023, Scientific Reports) were able to keep the entire experimental context similar across intended and unintended conditions, Jeay-Bizot et al. have one big difference between their passive and active conditions: the presence of a movement. Therefore, the present results explain the presence or absence of a movement rather than the presence or absence of an intention to act.

      We thank the reviewer for pointing us to this very relevant and elegant paradigm introduced in Derchi et al., 2023. We agree that our active and passive conditions are not matched for movement itself, and therefore that any differences observed between these conditions could in principle reflect motor-related processes, intention-related processes, or both.

      However, our primary goal was not to isolate a pure neural correlate of intention independent of movement, but rather to test whether the early premovement signals traditionally interpreted as markers of commitment contain reliable outcome-specific information predictive of an upcoming action. In that respect, the presence of an additional movement-related difference between conditions would be expected to increase, rather than decrease, decodability. Consequently, if reliable early commitment-like signals were present, they should still have contributed to reliable early classification performance in our paradigm.

      More closely matching the motor output across conditions, as in Derchi et al. (2023), would likely make classification substantially more difficult by removing movement-related information from the decoding problem altogether. Importantly, despite movement differing between our two conditions, reliable decoding still emerged only very close to movement onset.

      In addition to our modifications made with respect to a similar comment by reviewer #1 (see above), we have added the following paragraph:

      Discussion:

      “Our goal was not to isolate intention, but to test whether the signals traditionally interpreted as commitment signals actually possess commitment-like predictive properties. A recent study (Derchi et al., 2023) contrasted volitional eyeblinks with spontaneous eyeblinks, thereby keeping the occurrence of movement constant while varying the presence of intention. Such an approach would avoid the movement-versus-no-movement contrast inherent to our paradigm. However, matching motor outcomes across conditions would likely make classification substantially more difficult, since motor-related information could no longer contribute to decoding performance. More importantly, our paradigm is focused on the neural antecedents that are specific to whether or not a movement is initiated. This is a fundamentally different question from Derchi et al, which is focused on whether or not an intention is present. The two questions are complementary, however, and taken together, our study and the Derchi study contribute significantly to our understanding of spontaneous voluntary action.”

    1. Author response:

      The following is the authors’ response to the previous reviews.

      Joint Public Reviews:

      (1) The manuscript states that simulation-based calibration showed the amortized posterior estimator was unreliable (85-88), but these results are not shown. The manuscript explicitly states that simulation-based calibration demonstrated substantial failures of the amortized posterior estimator, yet the corresponding analyses are not presented. Since these results motivate the transition to sequential NPE and are central to assessing inference reliability, they should be reported quantitatively, either in the main text or supplementary material.

      We agree and have therefore added the simulation-based calibration result as a supplementary figure.

      (2) The authors present two independently trained estimators and show strong agreement between them. This is a useful robustness analysis. However, the rebuttal occasionally presents this as addressing concerns regarding cross-validation and generalization. The new analysis does not constitute cross-validation in the usual sense and does not directly assess generalization to held-out targets or posterior accuracy.

      I recommend that the authors explicitly describe Figure 4 as a reproducibility analysis and avoid presenting it as a substitute for validation.

      We are sorry for causing confusion with our response in the rebuttal. But we hope that the manuscript text is clearer than our rebuttal. We refer to the results as a “replication of the posterior estimator”. Regarding cross-validation, Figure 1 D shows additional simulations of posterior parameters that were not part of the training dataset.

      (3) Posterior correlations are useful for generating hypotheses about compensatory mechanisms, but they should not be interpreted as direct evidence of compensation. The compensatory interpretation should instead be supported by the perturbation analyses (e.g., Figure 6), which provide mechanistic validation.

      The manuscript consistently treats posterior correlations and conditional posterior shifts as direct evidence of compensatory mechanisms. These are consistent with compensatory mechanisms, but they do not by themselves establish that the corresponding biological parameters causally compensate for the perturbation. I recommend clarifying this distinction and emphasizing that the conditional posterior analyses generate hypotheses regarding compensation, which are then partially supported by the perturbation experiments shown later in the manuscript.

      The language throughout the manuscript should therefore be softened.

      We agree and have added hedging phrases to communicate the caveats of the results. For example, we now refer to “putative compensatory mechanisms” and adjusted the language in many other parts of the manuscript to highlight that our results provide estimates of mechanisms rather than the mechanisms themselves.

      (4) The manuscript repeatedly suggests that the inferred conditional distributions may be useful for identifying precise interventions or guiding personalized treatments (examples include lines 24-29, lines 217-223, lines 242-246, lines 277-282, lines 283-286). These claims go beyond what is directly demonstrated.

      The study does not evaluate treatment outcomes, patient-specific inference, intervention efficacy, or clinical decision-making. Rather, it demonstrates differences in inferred parameter distributions within a computational model. While these results are valuable and may generate clinically relevant hypotheses, they do not yet establish predictive utility for treatment selection or precision medicine. I therefore recommend substantially softening these translational claims and emphasizing that the current findings generate hypotheses that could be tested experimentally in future work.

      You are correct. We are currently working to use our approach on patient data, but the present manuscript does not test the translational potential of the method and therefore some of our previous claims are unsupported. We have therefore deleted references to clinical potential in large parts of the manuscript and add qualifying phrases where we kept discussions of translational potential.

      (5) The revised manuscript still mixes presentation of findings with interpretation.

      For example, lines 217-226 largely continue to describe findings from Figure 6 and would fit better in the Results section. The Discussion would be strengthened by focusing more exclusively on biological implications, limitations, and future directions.

      A similar issue appears later in the discussion comparing posterior correlations and conditional distributions. Much of this section effectively reinterprets Figures 2 and 3 rather than discussing broader implications.

      We agree that the main function of the discussion is to put results into a broader context. But we also believe that repeating results at different levels of detail, different wording, and different interpretation can be to the benefit of some readers. We have therefore left the discussion largely intact except for the changes relating to above points 3 & 4.

      (6) The discussion around lines 271-282 overstates what can be concluded from the inferred posteriors.

      The statement that correlations "discover broadly applicable mechanisms" whereas conditionals "identify specific mechanisms" is stronger than the presented evidence supports. Likewise, the conclusion that conditional distributions are more useful for precision treatments is speculative and not directly demonstrated.

      I recommend reformulating these statements as interpretations or hypotheses rather than conclusions.

      We have deleted the reference to personalized treatment and refer to the mechanisms as “hypotheses” in other parts of the discussion.

      (7) Around line 84, the manuscript introduces q(theta|x) without clearly defining θ, x, or q. Readers unfamiliar with SBI may struggle to follow the notation. All quantities should be defined when first introduced.

      We have added definitions of theta and x. We hope that q is sufficiently defined when we call it the “posterior estimate”.

      (8) The manuscript equates larger KS distances between conditional posteriors with greater compensatory potential. While KS distance provides a useful measure of posterior redistribution, it is not obvious that it should be interpreted as a measure of biological efficacy.

      We hope that the changes described above make it clear that we view the KS distance as an estimate of putative compensatory mechanisms in the simulator, rather than direct measures of biological efficacy.

      (9) The manuscript would benefit from a discussion of parameter identifiability. The inference problem maps 32 model parameters to 7 summary statistics, implying substantial nonidentifiability. While complete identifiability analysis is likely beyond the scope of the current work, this limitation should be discussed explicitly.

      Non-identifiability is indeed an important aspect of simulation-based inference. We allude to it in the introduction where we mention degeneracy. But since we do not present results directly quantifying non-identifiability, we believe an explicit discussion goes beyond the scope of our manuscript.

      All in all, the revised manuscript is significantly improved and addresses several concerns raised in the previous review. However, important issues remain as discussed above.

      We thank you for the comments that led to the improved revision and for your constructive feedback on this revised version.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      A fundamental technique for the identification of peptide-specific CD8 T cells is the use of fluorophore-conjugated and peptide loaded MHC tetramers. Classically, refolding of specific peptides with MHC monomers can be labour intensive, and not optimal for screening large numbers of different peptides. Hence, UV-exchanged tetramers have been developed to upscale this, however, still has some associated challenges such as UV-mediated damage to peptide complexes. Here, Pothast, C.R. et al demonstrate the efficacy of using temperature exchanged tetramers for the prevalent alleles HLA-A*03:01, A*11:01, B*07:02, and C*07:02. Building upon their previous work with HLA-A*02:01, H-2Kb, and HLA-E. They first demonstrate the complex stability of tetramers with different affinity peptides at high temperature, showing complex destabilisation can be rescued with higher affinity peptides. This is followed by an optimisation of peptide exchange temperatures, tailored for each allele. The authors then demonstrate successful binding to clonal T cell lines, and then a step further with viral peptides against PBMCs from individuals with confirmed infection history. For the latter they compare to conventional tetramers and demonstrate comparable signal.

      Due to the prevalence of these 4 alleles, the ease-of-handling, and short time requirements, these tetramers are likely to show high utility.

      Strengths:

      The manuscript is well-written and the results are solid, although more detail may add clarity to some of the results, in particular Figures 1 and 2. Other than the points reported below, the study uses accurate controls to demonstrate the specificity of the tetramers, and the data are convincing.

      Overall, the interpretation of the results is accurate, and the discussion is thorough. Additional comments may be included to cover potential tetramer batch variability and differences in the stability of different alleles. Specifically, whether certain alleles require higher-affinity peptides to be stable, compared to others.

      Weaknesses:

      The authors demonstrate the equivalence of temperature-exchanged tetramers to conventional ones, however, as they are an advancement on UV-exchange, it would be useful to show data on how their stability, exchange efficacy, and binding to T cell lines compare to UV-based tetramers. It would be supportive to show that temperature does not impact fluorophore intensity as well.

      Reviewer #2 (Public review):

      Summary:

      The majority of CD8+ T cell responses rely on the proper presentation of antigens through stable MHC-I (but not requiring a stable immunological synapse). This work highlights a new approach to build an array of stable peptide MHC-I using temperature exchange, which can be used to identify antigen-specific CD8+ T cells.

      Strengths:

      In this work, the authors have proposed an alternative method to reload the peptide MHC-I molecule. Their temperature-exchange approach is distinct from current reloadable peptide MHC technologies involving photolabile peptide, empty MHC-I (Nat Commun 11, 1314 (2020). https://doi.org/10.1038/s41467-020-14862-4), tapasin/TAPBPR chaperone-assisted (eLife 7:e40126.), enzyme exchangeable (WO2020226570) and small alcohol (Curr Res Immunol. 2022 Aug 18;3:167-174. doi: 10.1016/j.crimmu.2022.08.002) approaches.

      Weaknesses:

      However, the proposed temperature-exchange approach does not substantially improve the quality of antigen-specific T cells that can be identified using the photolabile peptide MHC-I molecules.

      The time saved using the temperature-exchange protocol may not be a pull factor as the photolabile peptide MHC-I approach is not unreasonably laborious.

      Reviewer #3 (Public review):

      Summary:

      The study by Pothast and colleagues outlines an extension of their previously described temperature-based MHC-I peptide exchange method on 4 common HLA alleles, to enable the generation of peptide/MCH-I tetramers for characterization of antigen-specific T cells by flow cytometry.

      Strengths:

      This work outlines a protocol for generating MHC-I tetramers on 4 common HLA allotypes, which can then be applied to monitor T cell responses by flow cytometry studies. The work provides conditional ligands for exchange on each HLA and demonstrates proof of concept studies using clonotypic T cells and CD8+ PBMCs.

      The results support that the temperature-exchanged tetramers can perform similarly to conventional tetramers in some settings.

      Weaknesses:

      Given that there are several proposed methodologies addressing the same task (including UV-mediated, disulfide-bond based stabilization of empty MHC-I conformers, and chaperone-based methods), the relevance of the proposed temperature-mediated technology is questionable.

      More specifically, important limitations of the study include:

      (1) A lack of quantification of exchanged molecules relative to molecules that retain the original placeholder peptides, or completely empty molecules present in the same sample.

      (2) A lack of validation that peptide exchange has occurred in the absence of a reporter T cell line appears to be a significant limitation of the methodology for antigen / T cell discovery.

      (3) The sub-optimal exchange efficiency relative to conventional prepared pMHC-I molecules, shown in Figure 4, is a significant limitation of the approach.

      (4) There are no data to support that exchange proceeds through the generation of empty molecules during the temperature cycle, or by peptide binding on empty molecules that are already present in the sample. Understanding the mechanism of exchange is important for the necessary improvements to the methodology.

      (5) It is possible that the temperature cycle causes protein aggregation or other irreversible changes to the sample - this should be explicitly quantified and addressed in the paper, since misfolded MHC-I molecules can lead to high levels of background staining.

      (6) These potential limitations should limit detection of low-affinity/low-avidity interactions between TCRs and their cognate pMHC antigens - this should be addressed explicitly in a model antigen setting.

      (7) The approach appears to be limited to the HLAs showing high thermal stability, which have been explored in this study. However, a large fraction of HLAs show sub-optimal thermal stabilities. It seems that explicit validation of peptide exchange would be required for any new HLA allele introduced into this process.

      (8) Whether the approach can be used to load suboptimal peptides with lower thermal stabilities that are emerging immunotherapy targets is not addressed in the present study.

      Because of these limitations, the present manuscript does not conclusively support the claim that temperature-based exchange can be used as a robust methodology to generate pMHC-I tetramers with desired peptide specificities.

      As a result, the scope of applications using these suboptimal exchanged pHLA tetramers is limited, and should be addressed with further improvements of the methodology, including better characterization of exchange efficiency, demonstration of functionality across a broader range of HLA allotypes with varying thermal stability profiles, and validation with clinically relevant low-affinity peptides that would strengthen the potential utility of this approach in immunotherapy development and basic T cell biology research.

      We are submittng a revised version that addresses the major points raised. We believe that the manuscript in its present form clearly communicates the development of a robust and versatile temperature-based peptide exchange platform applicable across multiple HLA class I alleles, with relevance for both fundamental and clinical immunology. While we appreciate the constructive feedback provided, we feel that the core findings and conclusions are already well supported and suitable for publication.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      The main recommendation here is to include a stability and staining comparison to UV-exchanged tetramers, as this will directly address why temperature-exchanged tetramers are superior. It could also be discussed that research groups may have better access to temperature-regulating equipment than UV. Other minor corrections may include:

      We thank the reviewer for this suggestion. We have previously demonstrated that HLA‑A*02:01 and H‑2Kb remain stable as frozen monomers, and similarly showed the stability of thermal peptide exchange for HLA‑E, both at the monomer stage and after multimerization into thermal‑exchange HLA‑E tetramers. In addition, we have directly compared these reagents with conventional tetramers (see Figure 5). Conventional monomers and tetramers are routinely stored at −80 °C for several months without loss of staining performance, and we applied the same storage conditions to thermal‑exchange HLA‑E tetramers. Consistent with conventional tetramers, thermal‑exchange tetramers maintained their ability to stain TCR‑expressing cells for up to six months, with optimal staining preserved at both −20 °C and −80 °C. These findings have been published previously and are discussed in the current manuscript.

      We would like to emphasize that we do not conclude that thermal peptide exchange is superior to existing technologies. Our intention is to demonstrate that this approach is feasible and to present its advantages and limitations, which are discussed in detail in the manuscript.

      In the discussion we have included a sentence about the accessibility of heat exchange in relation to the equipment needed for UV exchange.

      “Moreover, the broader availability and simplicity of equipment needed for thermal exchange compared to UV sources enables wider adoption of this approach.”

      (1) Greater explanation of the different coloured curves in Figures 1 and 2, and whether all curves represent samples that are incubated at 50 degrees Centigrade.

      We have now clarified in the figure legends that the different coloured curves represent the distinct peptide–HLA complexes analysed, and we explicitly state which curves correspond to samples incubated at 50 °C.

      (2) Addition of X-axis title for Figures 1 and 2.

      An X‑axis title was already present in Figures 1 and 2, but it was minimal; we have now revised it to make the labeling clearer and more informative.

      (3) Clarify whether the background signal (negative) increases with the addition of more tetramer in Supplementary Figure 3 (non-specific binding).

      The background (negative) signal did not appreciably increase with the addition of higher tetramer concentrations, indicating minimal non-specific binding under these conditions. This is consistent with observations in the MHC class I multimer field, where non-specific binding is generally limited under optimized staining conditions, and MHC class I multimers can be reliably used to detect antigen-specific T cells.

      (4) Address stability of different alleles, or whether they are similar.

      Peptide stability varies for each peptide–HLA combination rather than being strictly allele‑specific. We have therefore clarified this point in the manuscript. In addition, as requested by the reviewer, we have included a dedicated section describing the stability of the thermal‑exchange template peptides.

      “The peptides that formed stable complexes at 4°C but unstable complexes at 20–32°C and 50°C showed affinities ranging from 4 to 11 µM. Such low affinities are uncommon for endogenous peptides and are unlikely to have physiological relevance, given that the complexes are highly unstable at 37°C.”.

      (5) Measure fluorescence signal of tetramer before and after temperature exchange, compared to UV, to show fluorophore stability.

      Fluorescent streptavidin forms a highly stable complex. During UV-mediated peptide exchange, reagents are exposed to heat generated by the UV lamp, which can partially denature MHC-I proteins. For this reason, it is necessary to centrifuge the complexes after UV exchange to remove denatured protein aggregates. Importantly, the fluorescence of streptavidin itself is not affected by this process. In contrast, thermal exchange is performed at substantially lower temperatures than UV-mediated exchange and does not compromise MHC-I protein integrity. Therefore, in our view, it does not pose a significant risk to fluorophore stability. In addition, UV may destroy fluorescence by simple bleaching, which cannot be an issue with temperature-dependent peptide exchange.

      (6) Use HPLC to show stability of tetramer following temperature exchange versus UV.

      HPLC analysis of tetramers is not possible and this is also not performed by others. The reason is that the tetramers are very heterogeneous (clustering of streptavidin together and the amount of MHCI monomers attached to streptavidin). As discussed above we do not claim to be better or worse compared to UV-exchange. This technology has a some additional benefits compared to UV-exchange, such as the tetramerization can be done before the peptide exchange. Additional it does not need a calibrated UV lamp but just an heatblock is needed for the peptide exchange making the exchange less complicated and in our opinion easier to implement. The UV exposure may oxidize amino acids, which is unlike to occur under temperature dependent conditions.

      Reviewer #2 (Recommendations for the authors):

      Minor in figure:

      The authors should explain what "inputs" are in the figure legend.

      We have now clarified in the figure legends that the different coloured curves represent the distinct peptide–HLA complexes analysed, and we explicitly state the nature of the “inputs”.

      Minor in text:

      The authors should also state two important limitations when designing temperature-sensitive peptide MHC-I, which are peptide binding affinity and subsequent T cell recognition. Poorly designed peptides can result in unexchanged peptide MHC-I complexes that may be recognized by the CD8 T cells, leading to false positives.

      We have adjusted this in the text (discussion) although we did not make poorly designed peptides. The peptide presented in this manuscript are only stable at 4°C and unstable from 20°C and higher. As the T cell staining are performed at room temperature, there will be no peptide MHC-I complex of the original thermal-exchange peptide present as this is disintegrated. Only the stable, higher-affinity peptide-exchanged MHC-I is in complex. This does pose a problem for peptide exchange with low-affinity peptides, which is mentioned in the current version. However, this does not differ from the other loading technologies as in each case the mother peptide has to be exchanged for a proper peptide and a low-affinity peptide will be lost in time in each other case as well

      The authors should include other recent reloadable peptide MHC technologies, e.g. chaperone-assisted, enzyme-exchangeble, and small alcohol treatment.

      We apologize for not including these technologies and in the current manuscript they are included in the introduction. (see text below)

      “Several technologies have since been developed to allow the parallel production of multiple MHC-I multimers, facilitating high-throughput analysis. For instance, dipeptides have been used as catalysts for peptide exchange[7-10][FS1] , UV-sensitive conditional MHC ligands have been a widely adopted approach [11, 12], in which a photocleavable peptide is cleaved upon UV exposure. Additional peptide exchange technologies include: chaperone-mediated peptide exchange[13, 14] enzymatic cleavage of low-affinity peptides that are covalently linked [15] and small alcohol peptide exchange [16].”

      Major in data:

      The authors should show if any T cell was detected using the original unexchanged peptide MHC-I in cytometry, as the interpreted use of an irrelevant peptide also depends on the existence of antigen-specific T cells in circulation.

      The unexchanged peptide–MHC‑I complex cannot be used for T‑cell staining under our standard conditions because the template peptide dissociates at room temperature, leading to disintegration of the complex. Since our T‑cell staining protocol is performed at room temperature, unexchanged complexes would not remain intact long enough to allow reliable detection. Performing this experiment would require modifying the standard protocol and carrying out all staining steps strictly at 4°C. We choose not to change the staining protocol to perform this experiment.

      In addition, the thermal‑exchanged peptide–MHC‑I complexes do not produce elevated background staining. As shown in Figure 5, background staining would appear as single‑positive events (PE or APC only), which we do not observe. This indicates that the thermal exchange approach does not introduce nonspecific tetramer binding.

      Reviewer #3 (Recommendations for the authors):

      (1) The proportion of exchanged molecules should be quantified relative to those retaining the original placeholder peptides and completely empty molecules present in the sample, using quantitative mass-spectrometry analysis. This would provide critical information about exchange efficiency and help assess the method's reliability.

      We thank the reviewer for this point. We have performed this experiment and quantified the efficiencies. This is in the current version in figure 2b.

      (2) Validation studies demonstrating peptide exchange in the absence of reporter T cell lines should be included. This would strengthen the methodology's applicability for antigen/T cell discovery applications where such reporter lines may not be available.

      We thank the reviewer for raising this important point. Indeed, incomplete or unstable peptide exchange is a general concern inherent to all MHC-I peptide exchange protocols. To address this, we implemented a T cell–independent validation strategy based on LILRB1 binding. The innate immune receptor LILRB1 selectively recognizes properly folded peptide–MHC-I complexes by interacting with β2-microglobulin (β2M) and the α3 domain of the MHC heavy chain in a peptide-independent manner.

      Critically, in our system the conditional template peptides are thermally unstable and dissociate during the exchange step. As a result, only successfully exchanged complexes containing a stabilizing peptide remain intact. Consequently, LILRB1 binding serves as a functional readout of successful peptide exchange and pMHC stability.

      To assess this, we used K562 cells retrovirally transduced with LILRB1 and stained them with the corresponding fluorophore-conjugated pMHC multimers. Flow cytometric analysis enables clear discrimination between stable (successfully exchanged) and unstable complexes.

      This assay is fully independent of TCR-based reporter systems and can therefore be broadly applied in antigen discovery settings where such reagents are not available. Importantly, it complements our HPLC-based quantification of peptide exchange efficiency (Figure 2B) by providing a scalable quality-control readout of structural integrity (Figure 2C).

      We have now included this analysis in the Results section and updated the Discussion and Materials and Methods accordingly.

      (3) Optimization strategies to improve exchange efficiency should be explored, along with direct comparisons with established methods.

      In the revised manuscript, we have included the quantified exchange efficiencies of the thermal peptide exchange reaction, as determined by HPLC analysis on monomeric complexes. In addition, we now present a novel assay that enables routine quality control of each peptide exchange. This analysis is performed using LILRB1<sup>+</sup> cells and can be readily applied to any peptide–MHC complex using standard flow cytometry.

      Our data demonstrate that the exchange efficiencies obtained with our method are robust, and for the HLA alleles included in this study no further optimization was required. With respect to comparisons with established technologies, we chose to benchmark our approach against conventionally folded tetramers (Fig. 5). As stated above, we do not claim superiority over other peptide-exchange platforms; rather, we aim to present an alternative workflow with distinct practical advantages.

      (4) Potential protein aggregation or other irreversible structural changes resulting from temperature cycling should be quantified and addressed. Since misfolded MHC-I molecules can contribute to high background staining, this characterization is essential for assessing the method's reliability. This can be done using DLS studies, which should report on the fraction of misfolded, high MW species present in the sample upon temperature treatment.

      We thank the reviewer for raising this important point regarding potential aggregation or irreversible structural changes during temperature cycling. We agree that the presence of misfolded or aggregated MHC-I complexes could contribute to nonspecific staining and affect the reliability of the method.

      Although we did not perform dynamic light scattering (DLS), we addressed this concern using complementary biochemical and functional approaches. First, monomeric peptide–MHC complexes were analyzed by size-exclusion HPLC throughout the study. These analyses consistently showed well-defined peaks corresponding to properly folded complexes, without detectable high–molecular weight species that would indicate aggregation (Figures 1 and 2).

      Second, and importantly, we assessed the functional consequences of any potential misfolding or aggregation at the multimer level. If aggregated or misfolded MHC-I complexes were present, this would be expected to result in increased nonspecific binding and elevated background staining. However, across all experiments using both clonal T cell lines and primary PBMCs, we consistently observed low background staining and clear antigen-specific populations (Figures 3–5), arguing against the presence of aggregation-prone or sticky multimer species.

      Third, we incorporated an additional quality control step based on LILRB1 binding (Figure 2C). Because LILRB1 selectively recognizes properly folded peptide–MHC-I complexes, this assay provides a sensitive readout for structural integrity. Unstable or improperly folded complexes do not bind LILRB1, allowing discrimination between functional and non-functional pMHC complexes.

      Taken together, these complementary analyses indicate that temperature-based peptide exchange does not induce detectable aggregation or irreversible structural damage under our experimental conditions, and that the resulting multimer reagents are structurally intact and suitable for downstream applications. We have clarified this in the revised manuscript.

      (5) The method's capacity to detect low-affinity/low-avidity TCR-pMHC interactions in a well-characterized model antigen system should be explicitly addressed. This would define the sensitivity limits of the approach compared to established methods.

      The reviewer raises a valid and broadly relevant point that applies to all MHC-based technologies. However, we consider a full discussion of this topic to be outside the scope of the current manuscript. We do address this limitation for low-affinity peptides in the Discussion, where we write: “This technology is most likely not optimal for low-affinity peptides, as the template peptide itself must also have low affinity.” However, this problem may be universal since low-affinity peptides will simply release all MHC class I-peptide exchanged complexes during the staining process.

      (6) Since the current study focuses on HLAs with high thermal stability, the approach should be tested with HLA alleles exhibiting lower thermal stability profiles. A validation framework could be developed that could be applied when introducing new HLA alleles to this process.

      We thank the reviewer for this insightful comment. To our knowledge, there is no established classification of HLA alleles strictly based on “high” versus “low” intrinsic thermal stability; rather, stability is largely determined by the peptide–HLA combination.

      Regarding the development of a validation framework for additional HLA alleles, our data indicate that suitable template peptide affinities generally fall within a range of approximately 4–11 µM. We anticipate that this range may vary between alleles, and therefore each HLA allele will require empirical identification of an optimal template peptide to achieve appropriate thermal stability and efficient peptide exchange.

      This can be accomplished using the workflow presented in our study: first, assessing complex stability at 50 °C in the absence or presence of a high-affinity peptide (Fig. 1), followed by stepwise temperature reduction to determine optimal exchange conditions and incubation times (Fig. 2). In addition, LILRB1-based quality control can be incorporated to confirm the formation of properly folded and stable peptide–MHC complexes.

      (7) It is encouraged that the approach be explored for its ability to effectively load suboptimal peptides with lower thermal stabilities. Demonstrating this capability would significantly enhance the method's clinical relevance.

      We agree with the reviewer that evaluating the performance of the approach on suboptimal, low‑affinity peptides would be highly valuable and would further strengthen the clinical relevance of the method. In the current study, however, this falls outside our experimental scope. We are working on this in a follow-up project. We have now acknowledged the limitation of low-affinity peptides in the revised manuscript, noting that low‑affinity peptides are less suitable to this technology because the template peptide itself must also possess low affinity. Future work will be needed to systematically explore template design and exchange conditions optimized for such peptides.

    1. Author response:

      The following is the authors’ response to the original reviews.

      eLife Assessment:

      This important study reports a novel phenomenon of maternal growth during pregnancy that is independent of growth hormone (GH), adding a new dimension to maternal biology of reproduction. The evidence is convincing and supported by state-of-the-art methodologies conducted in mice and persuasive observations in humans with hereditary isolated GH deficiency. Revised discussion should focus on possible mechanisms, including the role of IGF2, and on directions for future research.

      We thank the editors for these valuable suggestions. In response, we assessed hepatic Igf2 mRNA expression. As shown in Author response image 1, hepatic Igf2 mRNA expression was higher in Ghrhr<sup>lit/lit</sup> mice but was not significantly affected by pregnancy. However, we recognize that IGF-2 is produced by multiple tissues, particularly at the maternal-fetal interface, as well as by other maternal tissues, exerting endocrine or paracrine effects. Therefore, we believe that hepatic Igf2 expression alone provides only a limited view of the potential contribution of IGF-2 to the maternal adaptations induced by pregnancy. For this reason, we chose not to include these data in the revised manuscript. Instead, we expanded the Discussion to address the potential role of IGF-2 in the observed phenotypes and to highlight important directions for future research, as suggested.

      Author response image 1.

      Public Reviews:

      Reviewer #1 (Public review):

      This work evaluates the impact of reproductive history on growth, body weight and body composition in mammals. In mice, somatic growth is stimulated by the first pregnancy while the second pregnancy increases body weight mainly by increasing adiposity. To probe the role of pituitary growth hormone (GH), the key regulator of somatic growth in these processes, was addressed by comparing the impact of reproduction on growth in normal ("wild type") and genetically GH-deficient females and by detailed characterization of the profile of fluctuations in circulating GH levels in both types of animals. Additional studies addressed the possible role of other endocrine pathways (ghrelin and estrogen) in the pregnancy-related growth. Surprisingly, reproduction-related growth was independent of GH, ghrelin and estrogen. To determine whether these results may apply ("translate") to human physiology, data on various parameters of somatic growth were collected from women with hereditary GH deficiency. The findings indicate that GH-independent stimulation of growth by reproductive events also occurs in women.

      Use of multiple animal models, rigorous characterization of GH levels in normal and GH-deficient females, and inclusion of data derived from a unique and well-characterised population of people with hereditary isolated GH deficiency and no GH replacement therapy are important strengths of these elegant and innovative studies. The results address a broader and clinically significant issue of permanent changes in body size, composition and function that result from pregnancy and lactation. This work also provides important background for further studies aimed at the identification of the mechanism involved and the role of specific reproductive events in the regulation of growth.

      We sincerely thank the reviewer for this thoughtful and highly positive evaluation of our work and for recognizing its novelty, rigor, and potential physiological and clinical significance.

      Reviewer #2 (Public review):

      This manuscript describes the fascinating phenomenon of growth hormone (GH)-independent growth occurring in the mother during pregnancy. This growth was most pronounced in dwarf mice that are lacking the receptor for growth hormone-releasing hormone (GHRH) and therefore showing isolated GH deficiency. However, the pregnancy-induced growth could also be observed in wild-type mice, suggesting that it is a normal part of the maternal adaptation to pregnancy. The study falls short of identifying the mechanism(s) driving this pregnancy-induced growth response, but it certainly reveals a novel insight into maternal physiology. The authors have completed a range of experiments in mice to prove that, as well as being GH independent, the pregnancy-induced growth also did not require GH signaling in the liver (i.e. not another pregnancy-specific ligand operating through the GHR to promote IGF). They also provided complementary data from a population of humans with untreated isolated GH deficiency that are broadly consistent with the hypothesis. While it is important to consider the significant species differences between rodents and humans, both in terms of growth physiology and also in terms of evolution of placental somato-mammotrophic hormones, this unique population are a valuable resource and adds credence to the study. Overall, I find this a compelling research story, but disappointingly unfinished. There are some areas where additional information could improve the ability to interpret the data, and some additional concepts that could be considered in the discussion. There are also areas where additional experiments might provide important insights. However, I think that such suggestions can be considered as appropriate for future research, rather than delaying consideration of the current manuscript.

      Main comments:

      (1) Data in Figure 1 are remarkable - not so much the growth in pregnancy in the wildtype mice, because while elevated GH is well known in pregnancy, but growth in the dwarf mice is indicative of GH-independent growth. From these data, it seems that there is good evidence that growth in pregnancy is an adaptive function. However, it is possible that growth is achieved in dwarf mice and that in wildtype mice may have been mediated through different mechanisms. The dwarf mice showed an increase in liver and plasma IGF1, suggestive of an additional ligand driving IGF in pregnancy. One could hypothesize that such an effect could be mediated by an additional pregnancy-specific ligand activating the GH receptor. In humans, placental growth hormone could be such a ligand, but as far as we know, there is no placental GH in mice. In contrast, the wildtype animals showed suppression of liver and circulating IGF1, and low levels of pSTAT5 in the liver during pregnancy. These data (in Figure 5) are very surprising. Given the high circulating GH in pregnancy, as well as high placental lactogen (which would be expected to activate STAT5 in the liver through the Prlr), the low levels of pSTAT5 are unexpected and would seem to indicate some sort of acquired insensitivity to GH. Is this entirely driven by down-regulation of STAT5b protein, or could there be activation of other, negative regulators of STAT signalling, such as SOCS? What is causing such a profound suppression of STAT5? Regardless of the mechanism, this suggests that pregnancy-induced growth in wildtype mice is independent of circulating IGF1 (potentially a different mechanism or in addition to that seen in IGHD mice).

      We thank the reviewer for this insightful comment. The mechanisms underlying the reduced hepatic STAT5b protein expression observed during pregnancy remain unknown. Previous studies have also reported desensitization of hepatic JAK2/STAT5 GH signaling during pregnancy, associated with increased expression of negative regulators of STAT signaling, including CIS (Miquet et al., Am J Physiol Endocrinol Metab 289–E607, 2005). In the current manuscript, we also observed increased Cish mRNA expression in the liver of pregnant mice. We have incorporated this information into the revised manuscript. In addition, we expanded the Discussion to acknowledge the possibility that pregnancy-induced growth may occur through distinct mechanisms in wild-type and GH-deficient mice and that, in wild-type mice, this response may involve liver-derived IGF-1-independent mechanisms.

      The data shown in Figure 6 are a major strength of the study, showing that the pregnancy-induced changes are not specific to one particular transgenic model, but still occur in a variety of models affecting GH through different approaches. Given the pregnancy-specific nature of the changes, however, it seems an oversight not to have evaluated the role of placental lactogens. Prlr is highly expressed in the liver, but the function of this hormone in the liver is not well established. Could the extremely high levels of PL be mediating this growth response? Given the low expression of STAT5 in the liver and the fact that plasma IGF1 is not markedly elevated, it seems more likely that this growth response may be mediated by locally produced IGF1 in target tissues.

      We thank the reviewer for this important suggestion. Although we were not able to investigate the role of prolactin receptor signaling using mouse models in the present study, we agree that prolactin may contribute to pregnancy-induced growth. Accordingly, we revised the Discussion to acknowledge this possibility and to include the potential roles of placental lactogens and locally produced IGF-1 as additional mechanisms that may underlie pregnancy-induced body growth.

      I think these possibilities could be addressed by an expanded discussion of species variation in placental hormones, to highlight that humans have expansion of the GH locus, but rodents have expansion of the prolactin axis (see Soares, M. J. The prolactin and growth hormone families: pregnancy-specific hormones/cytokines at the maternal-fetal interface. Reprod Biol Endocrinol 2, 51, 2004). Importantly, placental GH and chorionic somatomammotropins (CSM) in humans are all variants of the GH gene, but CSM have preferential activity at Prlr. This seems to be a fundamental species difference in pregnancy biology, but has been interpreted as an example of convergent evolution, with conservation of prolactin and GH-like functions at the maternal-fetal interface, mediated by different mechanisms, likely contributing to the metabolic adaptations of the mother (see Newbern D, Freemark M. Placental hormones and the control of maternal metabolism and fetal growth. Curr Opin Endocrinol Diabetes Obes. 2011; 18: 409-416). While the preceding function has focused on explaining the evolution of placental lactogens (either prolactin or GH variants), the present data suggest that there are also mechanisms to maintain growth in pregnancy, independent of GH (even in the absence of a placental GH).

      Thank you very much for this observation and suggestion. In the Introduction, we succinctly mention species-specific differences in the GH locus (see Introduction). Since our study focused primarily on mice, we believe expanding on this information would detract from the study's focus, especially given that such details are available in other publications. However, we have added a sentence to the discussion noting that, despite significant species-specific differences in the GH locus, there has been evolutionary conservation in the maintenance of pregnancy-induced growth, potentially involving distinct mechanisms in rodents and humans, though both appear to be GH-independent.

      “However, important differences are observed between humans and rodents. Humans, but not rodents, possess the GH2 gene, which encodes the placental growth hormone (GH) variant, whose production progressively replaces pituitary GH (derived from the GH1 gene) secretion during pregnancy (Liao et al., 2018). In contrast, rodents maintain pituitary GH secretion throughout gestation (Gatford et al., 2017; Liao et al., 2018). Additionally, human GH, both pituitary and placental variants, as well as chorionic somatomammotropins, can activate both the GH receptor (GHR) and the prolactin receptor (PrlR), explaining their lactogenic effects. In contrast, murine GH activates only the GHR (Bartke and Kopchick, 2015).”

      (2) The human data are very interesting, and my initial impression was that it seemed unlikely to be the same phenomenon. Was there any real evidence for "growth" in pregnancy? Pubertal maturation of long bone growth might be expected to prevent further growth in adulthood. However, these issues were appropriately discussed, and it seems well justified to evaluate this unique population of women with IGHD who underwent pregnancy. It would be very interesting to know if these women experienced elevated IGF1 during pregnancy, indicative of placental GH contributing to growth. Mechanistically, this might be more like the dwarf mouse situation of IGHD, that the situation in wildtype mice (associated with liver insensitivity to GH and low IGF1).

      We thank the reviewer for this comment. Unfortunately, the pregnancies of the women with IGHD occurred with limited medical assistance, and no additional clinical information is available, particularly regarding changes in circulating IGF-1 levels during pregnancy. Therefore, the evidence presented and discussed in the current manuscript represents the only information currently available on pregnancy-induced growth in this unique population.

      (3) It would be useful to include investigations that isolate the effects of pregnancy and the placental hormones. Such studies could include evaluating growth in pseudopregnant mice with IGHD (pregnancy-like changes in hormones but lacking the placental contribution) and in IGHD animals that experience pregnancy but not lactation (pups removed at birth). I accept that this might be too large an additional study to add for the present manuscript.

      We thank the reviewer for this valuable suggestion and agree that this experiment could provide valuable information regarding the role of placental hormones in pregnancy-induced growth. Interestingly, previous work has shown that female mice housed with vasectomized males exhibit increased body weight compared with non-reproductive females, although this increase is substantially smaller than that observed in females with successive litters (Garratt et al., Proc Natl Acad Sci U S A 117:15748–15754, 2020). We discuss this study in the current manuscript. However, this study did not provide additional information on whether this increase reflects greater adiposity, enhanced body growth, or both. Unfortunately, we are unable to perform these time-intensive experiments. We appreciate the reviewer's understanding and agree that this important question should be addressed in future studies.

      (4) It is an important and translationally relevant observation that pregnancy increased the risk of long-term weight gain, and that after the first pregnancy, the pregnancy-induced growth response was more directed to promoting fat deposition. Does this provide any mechanistic insight? Could a metabolic adaptation result in growth?

      We thank the reviewer for this thoughtful comment. At present, we do not have additional data to explain the mechanisms underlying the pregnancy-induced increases in body growth and adiposity or to determine whether these processes are mechanistically linked. In the revised manuscript, we have expanded the Discussion to address potential mechanisms that may contribute to the observed post-pregnancy growth, including hormonal and metabolic factors, while acknowledging that these possibilities remain speculative and require further investigation.

      Reviewer #3 (Public review):

      Summary:

      The study describes an increase in body growth and body composition in both mice and women. In mice, the impact on growth is mainly seen during the first pregnancy, and the changes postpartum on body composition are also different during the first and second pregnancies. The study has used various knock-out models in the growth hormone axis to understand these changes as well as some gene expression analysis related to GH, IGF-1 and estrogen signalling pathways.

      Strengths:

      (1) The inclusion of various knock-out mouse models that allow for exploration of mechanisms related to the above-mentioned changes.

      (2) The investigation of gene expression of GHR, IGF-1R and ER pathways.

      Weaknesses:

      The human findings are dependent on the patient's recollection of bodily changes after their pregnancies.

      Conclusion:

      The authors have partly achieved their aim of describing changes in growth and body composition that remain after pregnancy and the mechanisms behind these changes. This study may have importance for a wide variety of research areas as well as in the clinical setting. The study is also unique in its attempt to bridge findings in mice to a unique human model of congenital GH deficiency.

      We sincerely thank the reviewer for the thoughtful evaluation of our study, for recognizing its novelty and potential significance, and for highlighting the strengths of our experimental approach. We have revised the manuscript to further acknowledge the limitations of the human data, as suggested.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      The findings presented in this study are novel, exciting and important. I believe it would help the readers to include a diagram showing the timing of the various measurements and tissue collection in relation to conception, parturition and weaning. It would also be helpful to expand the discussion to include the author's thoughts on the possible role of various placental hormones, pituitary prolactin, metabolic changes and/or other factors in the observed growth. Finally, humans from whom the data were obtained should probably be referred to as individuals or subjects rather than patients.

      We thank the reviewer for these helpful suggestions. We included Figure 7 in the revised manuscript, which summarizes the study's experimental timeline. Additionally, we expanded the Discussion as recommended and replaced the term "patients" with "subjects" throughout the manuscript.

      Reviewer #2 (Recommendations for the authors):

      In addition to my comment above about addressing the different evolution of placental hormones, the following minor suggestions are provided:

      (1) Abstract line 23 "most" could be "some" (because lots of evidence that pregnancy-induced adaptations are long-term - e.g. brain structure, maternal behavior, endocrine changes) - see below.

      Done.

      (2) Is "reproductive experience" the best term? Or is it "pregnancy"? (likely specifically due to the presence of placental hormones and/or maternal patterns of hormones, rather than other aspects of "reproductive experience) e.g. mating, parturition or lactation?

      We appreciate the reviewer's point. However, because we cannot exclude potential contributions of mating, parturition, or lactation to the observed increases in body growth and adiposity, we prefer to retain the term "reproductive experience," as the mice in the present study underwent all of these processes rather than pregnancy alone.

      (3) Potentially, the introduction could add references to brain changes in humans in pregnancy (this is a particularly topical area of research where long-term changes have been reported; e.g. Pritschet L, Taylor CM, Cossio D, Faskowitz J, Santander T, Handwerker DA, Grotzinger H, Layher E, Chrastil ER, Jacobs EG. Neuroanatomical changes observed over the course of a human pregnancy. Nat Neurosci. 2024 Nov;27(11):2253-2260; Martínez-García M, Paternina-Die M, Barba-Müller E, Martín de Blas D, Beumala L, Cortizo R, Pozzobon C, Marcos-Vidal L, Fernández-Pena A, Picado M, Belmonte-Padilla E, Massó-Rodriguez A, Ballesteros A, Desco M, Vilarroya Ó, Hoekzema E, Carmona S. Do Pregnancy-Induced Brain Changes Reverse? The Brain of a Mother Six Years after Parturition. Brain Sci. 2021 Jan 28;11(2):168. There is also a significant literature on long-term effects of reproductive experience (Bridges RS. Long-term alterations in neural and endocrine processes induced by motherhood in mammals. Horm Behav. 2016 Jan;77:193-203).

      We thank the reviewer for this helpful suggestion. Accordingly, we incorporated these references into the Introduction to further emphasize the long-term effects of reproductive experience.

      (4) Figure 1: Why show body weight as a "delta" for primiparous animals, and "absolute "values for multiparous? Similarly, it seems that body length is an informative readout for these experiments, but this is only reported for one model, and most models are only shown as body weight and lean mass.

      We thank the reviewer for this comment. For the primiparous mice, we chose to present the change (Δ) in body weight and lean mass because it more directly illustrates the effects of the first reproductive experience relative to each animal's baseline while avoiding redundant presentation of both absolute and Δ values, as both analyses yielded the same statistical conclusions. For the multiparous mice, absolute values were presented to facilitate comparison with the corresponding images and to allow direct comparison of body size between wild-type and Ghrhr<sup>lit/lit</sup> mice. Regarding body length, these measurements were collected only in the multiparous cohort and were not obtained after the first reproductive experience. Therefore, we are unable to provide body length data for the primiparous groups.

      (5) It seems it would be better to present all of the mouse data first, then the supporting human data.

      Done.

      (6) The manuscript includes a high-quality investigation of GH secretion - particularly the pulsatile secretion of GH. Is it possible to have matching IGF data (at least multiple time points in pregnancy)?

      We agree with the reviewer that serial measurements of circulating IGF-1 during pregnancy would provide valuable additional information. Unfortunately, this analysis is not feasible because the limited blood volume collected during the study did not allow sufficient sample storage for additional measurements.

      (7) Line 221 - "GHRH signaling is required for pregnancy-induced increases in GH secretion...". Can you actually make that conclusion, or is it possible that the lack of GHRH developmentally has permanently altered the pituitary gland, so it cannot respond to other GH secretagogues?

      We thank the reviewer for this important comment. We agree that the congenital absence of GHRH signaling may cause developmental alterations in the pituitary that impair the response to other GH secretagogues. Therefore, we cannot distinguish whether the lack of pregnancy-induced increases in GH secretion reflects the absence of GHRH signaling per se or the developmental defects resulting from GHRH deficiency. We removed the aforementioned phrase from Results and have revised the Discussion to acknowledge this important limitation and to clarify that the observed phenotype may be secondary to impaired pituitary development.

      (8) Line 238 - "GHR signaling stimulates hepatic insulin-like growth factor 1 (IGF-1) secretion, particularly by activating the signal transducer and activator of transcription 5b (STAT5b) pathway" for this point, should probably cite: Davey HW, Xie T, McLachlan MJ, Wilkins RJ, Waxman DJ, Grattan DR. STAT5b is required for GH-induced liver IGF-I gene expression. Endocrinology. 2001 Sep;142(9):3836-41.

      Thank you for this suggestion; we added this reference.

      (9) Line 240 - "GH action in the liver is not only controlled by the pattern of GH secretion...". should probably cite Waxman's work regarding patterns of GH secretion (e.g reviewed in Waxman DJ, O'Connor C. Growth hormone regulation of sex-dependent liver gene expression. Mol Endocrinol. 2006 Nov;20(11):2613-29.).

      This reference was included in this sentence.

      (10) Methods: Check statistics - some of the analysis should have been repeated measures?

      We thank the reviewer for this comment. We carefully re-evaluated all statistical analyses and did not identify any experiment for which a repeated-measures analysis would have been appropriate. Therefore, no changes to the statistical analyses were necessary.

      Reviewer #3 (Recommendations for the authors):

      (1) Introduction: The context of the sentence "Furthermore, historically, females have been underrepresented in studies" is unclear.

      We thank the reviewer for this observation. Our intention was to emphasize that, because pregnancy is unique to females and females have historically been underrepresented in biomedical research, pregnancy-related physiology has received comparatively less attention. However, we agree that this statement was not essential in this context. Thus, we have removed it from the revised manuscript.

      (2) Introduction: Based on the paper, the main aim seems to be to study the lasting effects of pregnancy on the mother and not primarily to study the hormonal changes during pregnancy.

      We thank the reviewer for this helpful observation. We agree that our study primarily focuses on the long-term effects of pregnancy on the maternal organism rather than the hormonal changes that occur during pregnancy. Accordingly, we revised this sentence to better reflect the main objective of the study: “Therefore, the goal of this study is to investigate the lasting effects of pregnancy on the maternal organism and the possible involvement of the somatotrophic axis in these changes.”

      (3) Other endocrine factors could affect the changes seen after pregnancy in mice and humans, such as the insulin level and activation of the IR.

      We thank the reviewer for this valuable suggestion. In the revised manuscript, we expanded the Discussion to acknowledge the potential contribution of several endocrine factors, including insulin signaling, to pregnancy-induced growth.

      (4) The receptor activation in tissues other than the liver has not been studied, such as in the growth plate, adipose tissue and muscle.

      We thank the reviewer for this important comment. We agree with this point and have addressed this possibility in the revised Discussion.

      (5) Information on the age of the patient at the time of pregnancy could be included as well as the patient's height and weight before pregnancy and at follow-up.

      This information was added as Table 1.

    1. Author response:

      We greatly appreciate the editors and reviewers for their time and careful evaluation of our manuscript. It was clear that the reviewers valued our study that integrated RelB proximity proteomics with targeted HIV-CRISPR screening to identify chromatin and transcriptional regulators of AZD5582-mediated HIV reactivation. We appreciate all of the constructive comments and agree that the manuscript can be further strengthened by clarifying several technical points, correcting text and figure issues, and more clearly defining the scope of the study.

      A recurring theme of the reviews is the need to better define which RelB-associated factors are functionally meaningful regulators of HIV reactivation. We agree with the reviewers’ point that BioID/miniTurbo proximity labeling does not by itself establish direct physical interaction. That said, the method provides an in vivo cell measurement of protein proximity and can capture core complex interactions as well as transient, weak, or chromatin-associated interactions. Notably, such transient interactions are often lost during cell lysis and extraction, as well as co-IP. In the revised manuscript, we will clarify this distinction and emphasize that the BioID dataset identifies RelB-proximal candidate regulators rather than exclusively direct binding partners. We will also consider orthogonal validation of key hits using either co-IP or an orthogonal in cell proximity assay like PLA, which would preserve the cellular context of RelB-associated regulatory complexes.

      The reviewers also raised a fair concern regarding physiological relevance and the use of transformed latency models. We agree that primary cell validation would be an important next step for determining how broadly these findings apply to HIV regulation. At the same time, the present study was intended to be an initial resource of RelB-associated factors that contribute to HIV transcription in tractable latency models. Nonetheless, we will temper any language that implies broad generalization across all latency contexts and further discuss the limitations of clonal and transformed latency models. Additionally, and as the reviewers suggested, we will also test whether the KAT7/HBO1 and p300 inhibitor phenotypes extend to a primary CD4+ T-cell latency model.

      We also appreciate comments regarding the RelB-miniTurbo system; notably concerns with the basal expression of the fusion protein and presence of endogenous RelB. We will revise the manuscript to better describe these limitations and discuss how they may affect interpretation of the BioID data. In particular, we will emphasize that the dataset should be viewed as a resource for candidate RelB-associated regulatory factors that require functional and orthogonal follow-up.

      Several reviewers identified figure and text issues that will be addressed in the revised manuscript. Specifically, we will correct the Figure 1 legend and reference errors, the duplicated sentence, and other typos mentioned. We will also clarify the number of biological replicates and statistical thresholds used for the BioID comparisons, improve the Supplementary Table 1 annotation, and expand the discussion of p300/CBP to better reconcile our findings with prior literature.

      Overall, the revised manuscript will more clearly separate what this study establishes from what remains to be tested. Our goal for revision will be to enhance the value of the study while more clearly highlighting the limitations and what this resource provides for future directions.

    1. Author response:

      The following is the authors’ response to the original reviews

      Public Reviews:

      Reviewer #1 (Public review):

      We appreciate the authors have provided answers to many of the points we raised, and the changes made to their manuscript, which we think strengthen the overall evidence presented. However, we find that some important controls are still missing across experiments.

      Major comments:

      (1) Shortcomings in Immunofluorescence experiments:

      a. Antibody cross-reactivity was only tested against CK1ɛ, but should also be tested against CK1α, which is abundant in U2OS cells, and is also known to be involved in cell-cycle regulation.

      We selected the CK1δ antibody (abcam, ab85320 clone AF12G4) precisely because of its well-established specificity for CK1δ. In many well-cited studies [An et al., Nature Communications, 2022, PMID: 35810166], [Eng et al., PLOS One 2017, PMID: 28545154], some of which involve direct comparison with CK1α and CK1ε [Sinnberg et al., BMC Cancer, 2016, PMID: 27488834], [Beale et al., Journal of Biological Rhythms, 2019, PMID: 30898060], the CK1δ (ab85320) antibody is cited directly as the antibody used to specifically detect CK1δ.

      Additionally, through our previous eLife paper, we have confirmed the observation from previous studies that clearly demonstrate that this CK1δ (ab85320) antibody can specifically recognize CK1δ and not even its closest homolog CK1ε. Given the high degree of conservation in the kinase region between CK1δ and CK1ε, this implies that this antibody is likely directed at the divergent C-terminal tail (see sequence alignments in Author response image 1). Given that CK1α C-terminal tail is even more divergent from CK1δ, along with its reliable use in the literature from multiple working groups, it is safe to assume that this antibody can reliably distinguish CK1δ from CK1α.

      Author response image 1.

      Protein sequence alignments between CK1δ, CK1ε, and CK1α highlighting high sequence conservation in the structured kinase domain and sequence divergence at the C-terminal tail.

      b. Fig. 1: Statistical analyses are missing from the analysis.

      We have clearly added statistical analysis showing significant differences of CK1δ localization at the centrosome.

      c. Fig. 2: No colocalisation analysis shown for figure 2, only some arrowheads pointing to puncta. Appropriate colocalisation statistics are important since for practical reasons, only a few representative images can be shown on the figure.

      CK1δ colocalization is already well-established in the literature and additionally demonstrated in this study with the clear colocalization in Figures 1C and 1D. In Figure 2, we have chosen to report representative images which correspond to the typical phenotype we observe and can compare side-by-side which show clear and striking differences in terms of CK1δ localization between a) cells that form foci and lose CK1δ localization at a clear and distinct centrosome and b) cells that do not form foci and CK1δ is clearly localized to the apparent centrosome. By showing several fields-of-view, we demonstrate that this is the prevalent comparative phenotype.

      d. Fig. 6: Even if the figure is illustrative, it is important to show centrosome staining to visualise CK1ẟ's recruitment to the centrosome in G2/prophase, especially since this information is used to propose the model in figure 7.

      It is well-established that centrosomal duplication is a key hallmark of G2. Combined with our observations from Figure 2 showing that CK1δ to distinct puncta that one can only assume is the centrosome, and now showing in Figure 6, a clear duplication of these puncta. Importantly, this occurs in cells that also exhibit higher DAPI staining consistent with the duplicated and condensed genomic state when compared to other cells in the field of view, another hallmark of G2. Therefore, additional centrosomal staining and colocalization will only confirm what we already know about typical hallmarks of G2 and wider mitosis and the established CK1δ localization to the centrosomes.

      e. For all figures: Please mention the number of independent biological replicates in the figure legends (1, 2, 6). For figure 1, if there are 3 independent biological replicates, the quantification should take all of them into account (as opposed to the data points corresponding to 10 cells), and statistics must be done appropriately, taking those independent replicates into account. Same for the colocalisation analysis in figure 2 once you include it.

      We have mentioned the number of independent biological replicates where we considered it appropriate in Figures 3, 4, and 5. Figure 1 A and B are representative fields-of-view which show a replicable phenotype and we have quantified 10 cells to show the statistical difference in CKδ colocalization to PCNT. Figure 1 C and D show individual representative cells used for the line plot analysis but as one can already see from Figures 1 and B, these observations are clearly reproducible. Figure 2 A is an additional representative photo from observations we have made in our previous eLife publication. Figure 2 B already shows multiple fields-of-view which show a replicable result. Figure 6, again, shows a representative series of cells which already clearly demonstrate the change in CK1δ localization over the course of mitosis.

      (2) Shortcomings in biochemistry experiments:

      On CalA control, this is not a matter of confirming that CalA treatment works in principle, but rather to confirm that CalA treatment worked in this specific replicate. Aliquots may lose potency (e.g. with freeze-thaw cycles / exposure to light), hence checking for enrichment of phospho-proteins is essential to confirm the treatment was successful in this particular instance. In the worst-case scenario, the company may have sent the wrong compound altogether! A positive and a negative control is the basis for every experiment to make meaningful interpretation. On a separate note, many experiments have control and siRNA or compound treatments on two different gels - this should be rectified as they are meaningless if different exposures have been selected for different immunoblots.

      I find it hard to seriously answer to these points. I do not know what kind of reagents the reviewer is used to work with. On every experiment we show as a sub-figure, we use the same CalA that clearly works as intended since we can clearly see a phosphorylation-induced gel shift of the kinase. This rules out aliquots losing their potency or supplier providing the wrong compound. We also show a clear negative control in showing the absence of the gel shift prior to CalA treatment.

      On a separate note, we have no experiments with siRNA so we are unsure what the reviewer is referring to here. Of the 11 immunoblots we report here, each of which are representative of a triple replicate, only 1, Figure 3B, shows a split view on an equal exposure. Even then this was actually run on the same gel and this figure was simply spliced to simplify the message we want to convey. Therefore, we believe we have used the appropriate controls and level of rigor to make our observations and interpret them adequately.

      (4) As the authors mention, the kinase is not fully inactive when tail phosphorylated. Recent research has also suggested that tail-phosphorylated CK1ẟ may show increased catalytic activity for a few select, specific substrates, in the co-occurrence of pT220 (Cullati et al., 2022; Cullati et al., 2024). It is thus tricky to directly infer that phosphorylated CK1ẟ is inhibited, when no positive control for CK1ẟ inhibition was shown in the evidence presented. It would be necessary to either nuance your claim or include a positive control for CK1ẟ inhibition. Please revise statements in the manuscript accordingly.

      We have clearly demonstrated that CKδ tail phosphorylation leads to kinase inhibition and refer the reviewer to our work in PNAS [Marzoll et al., PNAS, 2021; PMID: 35217617].

      (5) It would be important to include statistical analyses for the immunofluorescence data in Fig. 1 and 2.

      We have included statistical analysis where we considered it appropriate in Figure 1 A and B. In Figure 1 C and D, statistical analysis is not appropriate to apply to compare single line plots as the individual data are clearly distinct from one another. For Figure 2 A and B, again, we are showing this data to show what is already a clear difference in CK1δ centrosomal localization when we compare cells that either form PER-CRY foci or do not.

      (9) The authors mentioned "In the eLife study, we show that inhibition of kinase activity by PF670462 stabilizes CK1δ and that the overexpressed kinase-dead mutant CK1δ-K38R is stable." Unfortunately, the data from biochemical analyses presented in the eLife publication is uninterpretable due to a lack of loading controls.

      We respect the reviewer’s opinion on this matter. However, the earlier study was independently peer-reviewed and has already been published. The reviewer was not involved in the assessment of that work, and we therefore feel that a retrospective evaluation of its merits is beyond the scope of the present review. We would respectfully ask that the current manuscript be evaluated on the basis of the questions it addresses and the evidence presented here.

      (10) While the data presented in Penas et al. strongly suggests a link between CK1ẟ stabilisation and the APC/C-Cdh1 complex, it is the only study to have shown it. Given that (1) science relies on data reproducibility and (2) your proposed model relies heavily on the relationship between CK1ẟ stabilisation and the APC/CCdh1 complex, it would be appropriate to include the investigations mentioned in our original comment.

      We respectfully point out that the purpose of the present review is to assess the manuscript under consideration, not to retrospectively reassess data that have already been published, such as those reported by Penas et al., even if this is the only study we cite in support of this particular point.

      After checking the peer review received from Review Commons, we cannot see the “investigations in our original comment” that this reviewer is referring to.

      Reviewer #2 (Public review):

      In this study, Serrano et al. employed a combination of cell biological and molecular approaches to investigate the localization and regulation of Casein Kinase CK1 during the cell cycle using U20S cells. They show that CK1 dynamically localizes between the centrosomes and the nucleus but can be sequestered away from the centrosomes upon overexpression of its binding partner PER2. They provide evidence that CK1 WT but not a phospho-null mutant strongly accumulates in a hyperphosphorylated form upon inhibition of phosphatases (using Calyculin and Okadaic Acid) and thus conclude that CK1 tail phosphorylation protects the kinase from degradation. Using synchronized cells, they show that CK1 accumulates unphosphorylated in S-phase (APC/Cdh1 inactive) but phosphorylated at the G2-M transition. Immunostaining shows that CK1 localizes to the centrosomes during mitosis.

      The manuscript has improved overall, but some sections are still inconclusive and require clarification.

      Major comments:

      Figure 1 is inconclusive. CK1 nuclear staining is highly similar in untreated cells and in cells treated with CHX + PF670462. The reduction in centrosomal staining in these cells is barely significant. However, the authors draw very strong conclusions from these data sets. In panel B, the cells appear to have been fixed incorrectly, and the anti-PCNT shows a strong background signal. Not convinced that immunofluorescence is the best approach to look at protein dynamics in vivo.

      Figures 1 A and B are meant to show how CHX and PF670462 may affect CK1δ localization to the centrosome (stained by PCNT) over several cells whereas Figures 1 C and D are meant to more clearly show this effect in individual cells. This effect is indeed modest in the endogenous situation compared to the overexpressed which shows a clearer redistribution of CK1δ. We show this when we compare the quantification in Figure 1A and the colocalization analysis in Figure 1 C (right panel; showing that some CK1δ still colocalizes to the PCNT-stained centrosome) to their overexpressed counterparts. This however, only emphasizes the strength of our overexpression approach as it has allowed us to observe a more dramatic shift in CK1δ centrosomal localization.  

      In Figure 2, panel B, the authors should co-stain the centrosomes of cells that co-express CRY1 and CK1, as some of these dots may represent the centrosomes.

      In principle, we indeed cannot exclude the possibility that a CRY-stained foci may actually be a centrosome. However, we refer to our comments to Reviewer #1 and add our observation that these PER-CRY foci are clearly nuclear based on our earlier eLife publication and are therefore unlikely to be centrosomal. (If some of the dots represent centrosomes, this would mean that a fraction of CRY1 is recruited from the nucleus to the centrosome in the cytosol. There is no mechanism for this known.)

      Figures 3B, please provide information on the non-phosphorylable CK1a mutant (it is mentioned as a variant in which all serine and threonine residues in the C-terminal tail were replaced by alanine). Specify the number of sites mutated and their exact position. Is this non-phosphorylable CK1a version catalytically active?

      As said, all serine and threonine residues in the tail have been changed, and yes, the kinase is of course active.

      Treatment of samples with inactivated PPase should be used as a control.

      It is unclear what this experiment would control for and how its outcome would affect any of the conclusions of the present study.

      Strengths:

      The authors reveal that the activity and abundance of dephosphorylated and phosphorylated CK1δ are regulated in a cell cycle-dependent manner. This suggests that these different pools are associated with distinct physiological functions.

      Weaknesses:

      Unfortunately, some of the data are inconclusive, and there is no data/information linking the cell cycle regulation of CK1δ to its function during the cell cycle.

      Although CK1δ continuously undergoes cycles of autophosphorylation and dephosphorylation, the kinase is predominantly found in its dephosphorylated, active state under steady-state conditions. This has obscured the physiological relevance of its well-established inhibitory autophosphorylation. We now identify mitosis as the cellular state in which this equilibrium shifts: autophosphorylated and consequently inhibited CK1δ accumulates. These findings resolve a longstanding question regarding the physiological function of CK1δ autophosphorylation and reveal it as a cell-cycle-regulated mechanism of kinase inhibition.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      Most of our minor comments related to editorial issues have been ignored by the authors and the errors persist. Simple corrections will improve the manuscript and make it more readable.

      We also found new minor errors as follows:

      69-70: 'dependent on its kinase is activity' --> 'its kinase activity'

      164: 'sites or targeted by' --> 'sites are targeted by'

      179: 'PF670' instead of 'PF670462'

      292: 'against higher the steady state levels' --> 'against the higher steady state levels' or 'against higher steady state levels'

      We thank Reviewer #1 for their close reading of our text. We have adjusted the text accordingly.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      The study addresses the organisation of synaptic connections from the medial to the lateral entorhinal cortex. Classic anatomical work has suggested these connections exist, but very little is known about their identity or functional impact. The manuscript argues that these projections are mediated by glutamatergic neurons, providing excitatory input from MEC to all layers of LEC, and by SST+ve interneurons sending inhibitory projections to L1 of LEC. This appears to be the most likely interpretation of the data, although in my opinion, more could be done to rule out the possible impact of the spread of the virus/tracer from the injection site.

      While this concern might seem overly picky, the importance of this level of detail is nicely shown by the authors' previous work clarifying connectivity from postrhinal to entorhinal cortices through careful analysis of similar types of data (Doan et al. 2019). If additional analyses/data can address the concern here, then I think this will be an important set of fundamental results that will influence thinking about circuit mechanisms for spatial cognition and episodic memory. In particular, it will nicely add to an emerging view that MEC and LEC can interact directly, showing that the organisation of these interactions is asymmetric and identifying a potentially interesting long-range inhibitory pathway.

      Reviewer #2 (Public review):

      Summary:

      The manuscript by Nilssen et al. presents a comprehensive study of the circuitry linking the medial and lateral entorhinal cortices (MEC and LEC). Using a combination of anatomical tracing, optogenetics, and in vitro electrophysiology, the authors convincingly demonstrate that the MEC sends both glutamatergic and long-range inhibitory SST+ GABAergic projections to the LEC, with distinct laminar and cell-type-specific targeting. Notably, they reveal that SST+ inhibitory projections selectively suppress the activity of layer IIa neurons, whereas excitatory inputs preferentially engage neurons in layers IIb and III, thereby differentially modulating hippocampal-projecting populations.

      Strengths:

      The experiments are carefully executed, the results are compelling, and the conclusions are well supported by the data. This work will be of broad interest to researchers studying memory circuits, cortical inhibition, and the organization of long-range connectivity.

      Weaknesses:

      Although the in vivo relevance of these connections remains to be determined, this is an important and timely contribution to our understanding of entorhinal-hippocampal interactions.

      The request for validation of injection specificity and viral spread, as detailed in the comments and suggestions of the two reviewers has been provided in the revised version. We added supplementary figures 1,2 and 6 as well as an extra insert into the old supplementary figure 5, now supplementary figure 9.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      Major Points:

      (1) Interpretation of the retrograde labelling experiment in Figure 1A-C is challenging, as the spread of the tracer at the injection site is not shown. It's important to see the full dorsal-ventral extent of the injection site in order to establish that the labelling of neurons in MEC results from projections to LEC and not adjacent areas (including MEC).

      As mentioned in our initial reply, we are fully aware of the risks associated with an incomplete assessment of injection sites and viral spread, so we provide a new Supplementary Fig. 1 showing 6 dorsoventral levels of the case shown in Fig. 1A. The injection site in case of FG often shows a core of damaged tissue with a halo of substantial unspecific fluorescence. Outside of the injection side, one only sees retrogradely labeled somata (often recognizable by FG signal clustered in lysosomes) and dendritic elements. As indicated in the legend, we report some tracer leakage along the needle track in temporal and perirhinal cortex, areas that receive only sparse MEC projections, but there is no apparent spread of the injection into MEC.

      Numbers are also quite low. E.g., Figure 1A is N=1/2 for retrograde labelling experiments.

      The reviewer would be correct if the experiments were meant to analyze MEC projections to LEC in full anatomical detail. This was not our intention (several papers addressed this pathway in detail), we merely aimed to distinguish between glutamatergic and potential GABAergic contributions to this pathway and to establish optimal coordinates in slices to prepare for the electrophysiological recording experiments. Two animals suffice for this purpose and using more would be against the aim of reducing the use of experimental animals as much as possible.

      The rationale here for the use of AAV2-CAG-tdTomato as a retrograde tracer is unclear. My understanding is that this is more effective as an anterograde tracer. Some clarification and validation would be important.

      The reviewer is correct that AAV2 is generally considered an effective anterograde tracer, but tracing the connectivity of entorhinal cortex with AAVs has been proven to be notoriously difficult, in particular retrograde tracing of inputs to layer II. In a neighboring lab in the centre, headed by Edvard and May-Britt Moser, it was established that AAV2 types show very efficient retrograde transport and that is why we decided to use the virus. Also, in our hands the virus showed excellent retrograde transport that served our purpose

      (2) Interpretation of the anterograde experiments in Figure 1D-E would also benefit from showing evidence that the injection sites are restricted to MEC. It should be straightforward to make a supplemental figure showing labelling at all dorsoventral levels.

      More careful analysis of the axon labelling in the dentate gyrus could also help make a case for the selectivity of the injection site for eGFP. In this case, only the intermediate portion of the molecular layer of the DG should be labelled. In the image shown, the labelled band is quite wide, but it's hard to tell if this reflects the plane of section or is because it also includes labelling in the outer molecular layer (which would be indicative of LEC expression).

      We thank the reviewer for these two suggestions, and we have prepared a new Supplementary Fig. 2 in line with this.

      Numbers are also on the low side for these experiments.

      See our response above

      (3) For optogenetic experiments in Figure 2, the selectivity of targeting of AAV to MEC is assessed through the specificity of labelling in the DG. This is great, but it's important to show that this specificity is maintained at all dorsoventral levels.

      Higher resolution images of labelling in LEC could also be helpful. It's hard to tell from the images in 2A if labelling is axonal or is in the soma adjacent to the nuclear NeuN signal (which would indicate a lack of selectivity for MEC).

      We thank the reviewer for these two suggestions and provide a new Supplementary Fig. 6, showing both the details of AAV1 being present only in neuropil in MEC not in somata as well as the specific labeling in the middle molecular layer of DG in detail. Including all dorsoventral levels would not provide additional information in view of the very well-established topographical organization of the entorhinal to dentate projection, reaching approximately 20 -25 % of the full long axis of DG (Van Groen et al., 2003)

      In addition, we have again carefully screened all tissue from the electrophysiological experiments for possible leakage of virus from MEC to LEC. We decided to exclude recordings from one mouse, which had labelling in MEC that was close to the border with LEC. Neuron counts have therefore been adjusted (pages 7-9) and the example recording showing responses to TTX/4-AP exposure in Figure 2B has been exchanged.

      (4) The analysis of excitatory and inhibitory opto-responses in Figure 2 is nice. It may be helpful to report quantification of the rise and decay kinetics of the synaptic currents. They appear much slower for the inhibitory input, which may be functionally important.

      This would indeed be nice to add, but it would not significantly impact or change the main message of our study. Since the lab of the senior author (MPW) has been discontinued and the resources for conducting these analyses are not readily available anymore, we have found it difficult to comply with the reviewer’s request

      (5) More direct evidence for SST axons projecting from MEC to LEC would strengthen the conclusions made. E.g., in experiments where the SST neurons are labelled, is it possible to follow the axons? Do they project as expected from the MEC to the LEC?

      In our view the tracing data provide convincing evidence in support of a direct projection from MEC to LEC by SST neurons, as shown in horizontal brain sections where SST axons labelled in MEC of an SST<sup>Cre</sup> mouse projects within Layer I from the site of origin in MEC to Layer I of MEC (Supplementary Figure 3). Similar visualizations were not possible to obtain in our electrophysiological experiments where semicoronal slices were used. This cutting angle has been shown to be optimal to preserve most of the axon and the dendritic tree of LEC neurons (Tahvildari and Alonso, 2005; Canto and Witter 2012), but does not maintain the projection from MEC to LEC.

      Minor Points:

      (1) "These layers are heavily innervated by medial entorhinal axons (Figure 1F...". I don't see a 1F.

      This has been corrected; should have been Figure 1E.

      (2) Methods should report series resistance values for patch-clamp experiments (range and mean).

      Fully agree and this information has now been added on page 22 of the manuscript:

      Under Voltage clamp: ‘Recordings with series resistance ≤ 25 MΩ were accepted, with an average of 16.2 MΩ for voltage clamp recorded neurons (range, 4.9 – 24.9 MΩ).’

      Under Current clamp: ‘All recordings (series resistance: 18.9 MΩ, 5.0 – 66.7 MΩ; mean, range) were included for analysis.’

      Reviewer #2 (Recommendations for the authors):

      (1) Please specify in the figure or, alternatively, in the figure legend which virus was used in each group shown in Figures 2H and 2I. This is somewhat confusing, since Figure 2E illustrates a specific combination of viruses and mouse lines that only corresponds to part of Figure 2H. While this information is provided in the text, including it directly in the figure would help the reader.

      We thank the reviewer for this excellent suggestion, and we have implemented this in the new version of figure 2.

      (2) In Figure 4, regarding the inputs from PIR, cLEC, and PER to LEC, the inhibitory components recruited by each input were not examined as thoroughly as for the MEC inputs. In fact, some inhibitory interneurons were double-labeled in the GAD67 mice (Figure 4B), which could also influence the responses of LEC neurons, especially for PER inputs. Recordings in Figure 4C appear to have been obtained near the reversal potential for inhibition, which may have prevented the observation of inhibitory effects. The authors could discuss this point in the Results.

      The reviewer is correct and this issue is now addressed in the relevant section in the results (page 11):

      ‘It should be noted, however, that it is possible that inhibitory effects could have been masked in some recordings, due to the resting membrane potential in our recordings being close to the theoretical chloride equilibrium potential. This could be particularly relevant for the inputs from PER, an area where we found LEC-projecting GABAergic neurons (Fig. 4B) and which is known to provide long-distance inhibition to LEC (Pinto et al., 2006; Apergis- Schoute et al., 2007).’

      (2) A diagram summarizing the known connections among MEC, LEC, and the hippocampal formation, highlighting the relevant cell types, layers, and the new connections identified in this study, would be a valuable addition, perhaps as a supplementary figure.

      We appreciate the suggestion, though find a full summary of known connectivity a bit overdone. Instead, we included a new figure 6 that summarizes the main new findings of the paper in the context of LEC projections to the hippocampal formation.

      (3) Although the main focus is on MEC-LEC connectivity, the experiments examining interactions with other cortical areas and converging inputs would benefit from a discussion of how MEC-driven inhibition of LEC might influence those inputs and shape the resulting output to the hippocampus. Including a short paragraph addressing this in the Discussion section would strengthen the manuscript.

      Excellent suggestion although we did speculate briefly in the result section on the possible effect. We have added a short paragraph in the discussion (page 15), reiterating the part in the results (page 13, last paragraph of results). We also briefly discussed the potential functional relevance of the suppression of the pathway from layer IIa to DG-CA3/CA2 versus the facilitation of activity in the pathway from layers IIb/III to CA1 and subiculum (last section of the discussion).

      (4) Lastly, it would be interesting to know what the main source of activation is for the SST long-range LEC projecting neurons. Are these neurons recruited in a feedback manner by the activity of MEC excitatory cells? I realize this question is beyond the scope of the present study, but if the authors have any data or insights related to this point, including a brief discussion would be valuable.

      This is an interesting thought, and we have included a new supplementary figure (supplementary Figure 5) showing data from experiments mapping monosynaptic inputs to MEC SST neurons using rabies virus. Although it was not possible to target only MEC SST neurons that project to LEC, the data show which are the main extrinsic inputs to the population of MEC SST neurons, most likely including those that project to LEC.

    1. Author response:

      The following is the authors’ response to the previous reviews

      Public Reviews:

      Reviewer #1 (Public Review):

      Summary:

      In this study, Millard and colleagues investigated if the analgesic effect of nicotine on pain sensitivity, assessed with two pain models, is mediated by Peak Alpha Frequency (PAF) recorded with resting state EEG. The authors found indeed that nicotine (4 mg, gum) reduced pain ratings during phasic heat pain but not cuff pressor algometry compared to placebo conditions. Nicotine also increased PAF (globally). However, mediation analysis revealed that the reduction in pain ratings elicited by the phasic heat pain after taking nicotine was not mediated by the changes in PAF. Also, the authors only partially replicated the correlation between PAF and pain sensitivity at baseline (before nicotine treatment). At the group-level no correlation was found, but an exploratory analysis showed that the negative correlation (lower PAF, higher pain sensitivity) was present in males but not in females. The authors discuss the lack of correlation.

      In general, the study is rigorous, methodology is sound and the paper is well-written. Results are compelling and sufficiently discussed.

      Strengths:

      Strengths of this study are the pre-registration, proper sample size calculation, and data analysis. But also the presence of the analgesic effect of nicotine and the change in PAF.

      Weaknesses:

      It would even be more convincing if they had manipulated PAF directly.

      We thank Reviewer #1 for their positive and constructive comments regarding our study. We appreciate the view that the study was rigorous and methodologically sound, that the paper was well-written, and that the strengths included our pre-registration, sample size calculation, and data analysis.

      In response to the reviewer's comment about more directly manipulating Peak Alpha Frequency (PAF), we agree that such an approach could provide a more direct investigation of the role of PAF in pain processing. We chose nicotine to modulate PAF as the literature suggested it was associated with a reliable increase in PAF speed. As mentioned in our Discussion, there are several alternative methods to manipulate PAF, such as non-invasive brain stimulation techniques (NIBS) like transcranial alternating current stimulation (tACS) or neurofeedback training. These approaches could help clarify whether a causal relationship exists between PAF and pain sensitivity. Although methods such as NIBS still require further investigation as there is little evidence for these approaches changing PAF (Millard et al., 2024).

      Reviewer #2 (Public Review):

      Summary:

      The study by Millard et al. investigates the effect of nicotine on alpha peak frequency and pain in a very elaborate experimental design. According to the statistical analysis, the authors found a factor-corrected significant effect for prolonged heat pain but not for alpha peak frequency in response to the nicotine treatment.

      Strengths:

      I very much like the study design and that the authors followed their research line by aiming to provide a complete picture of the pain-related cortical impact of alpha peak frequency. This is very important work, even in the absence of any statistical significance. I also appreciate the preregistration of the study and the well-written and balanced introduction. However, it is important to give access to the preregistration beforehand.

      Comment on latest version:

      I thank the authors for their efforts to respond to my previous concerns. I appreciate the additional analyses and the more cautious wording in several places. However, I still think the manuscript would benefit from a more direct interpretation of the findings.

      Reviewer #3 (Public Review):

      In this manuscript, Millard et al. investigate the effects of nicotine on pain sensitivity and peak alpha frequency (PAF) in resting state EEG. To this end, they ran a pre-registered, randomized, double-blind, placebo-controlled experiment involving 62 healthy adults who received either 4 mg nicotine gum (n=29) or placebo (n=33). Prolonged heat and pressure were used as pain models. Resting state EEG and pain intensity (assessed with a visual analog scale) were measured before and after the intervention. Additionally, several covariates (sex at birth, depression and anxiety symptoms, stress, sleep quality, among others) were recorded. Data was analyzed using ANCOVAequivalent two-wave latent change score models, as well as repeated measures analysis of variance. Results do not show ‘experimentally relevant’ changes of PAF or pain intensity scores for either of the prolonged pain models due to nicotine intake.

      The main strengths of the manuscript are its solid conceptual framework and the thorough experimental design. The researchers make a good case in the introduction and discussion for the need to further investigate the association of PAF and pain sensitivity. Furthermore, they proceed to carefully describe every aspect of the experiment in great detail, which is excellent for reproducibility purposes. Finally, they analyse the data from almost every possible angle and provide an extensive report of their results.

      The main weakness of the manuscript is the interpretation of these results. Even though some of the differences are statistically significant (e.g., global PAF, pain intensity ratings during heat pain), these differences are far from being experimentally or clinically relevant. The effect sizes observed are not sufficiently large to consider that pain sensitivity was modulated by the nicotine intake, which puts into question all the answers to the research questions posed in the study.

      We would like to express our gratitude to Reviewer #3 for their thoughtful and constructive review, including the positive feedback on the strengths of our study's conceptual framework, experimental design, and thorough methodological descriptions.

      We acknowledge the concern regarding the experimental and clinical relevance of some statistically significant results (e.g., global PAF and pain intensity during heat pain) and agree that small effect sizes may limit their practical implications. However, our primary goal was to assess whether nicotine-induced changes in PAF mediate pain changes, rather than to demonstrate large direct effects on pain sensitivity. Nicotine was chosen for its known ability to modulate PAF, and our focus was on the mechanistic role of PAF in pain perception. To clarify this, we have revised the discussion to better differentiate between statistical significance, experimental relevance, and clinical applicability. We emphasize that this study represents a preliminary step towards understanding PAF’s mechanistic role in pain, rather than a direct clinical application.

      We appreciate the suggestion to refine our interpretation. We have adjusted our language to ensure it aligns with the effect sizes observed and made recommendations for future research, such as testing different nicotine doses, to potentially uncover stronger or more clinically relevant effects.

      Although modest, we believe these findings offer valuable insights into the potential mechanisms by which nicotine affects alpha oscillations and pain. We have also discussed how these small effects could become more pronounced in different populations (e.g., chronic pain patients) and over time, offering guidance for future research on PAF modulation and pain sensitivity.

      Recommendations for the authors:

      Reviewer #2 (Recommendations for the authors):

      I thank the authors for their efforts to respond to my concerns. I very much admire the thoughts and effort that the authors have put into this study. This is a great study design, a fantastic research idea and an important path to study the neurophysiology of pain.

      I also understand that some of my suggestions are not compatible with the authors' current line of analysing their data. Since the authors did not change the analysis procedure and obviously could not change their experimental design, I would largely keep my public review.

      However, acknowledge the different opinions and have a few remarks and suggestions.

      (1) In agreement with reviewer 3, I would not consider the effect of nicotine to be meaningful. The random effect mentioned by the authors could have been addressed with a crossover design. In this case, the placebo and intervention could have been directly compared. Interindividual differences in pain perception are at least partially controlled for by analysing the difference between pre and post-gum. The distribution of the pre-post difference separately for placebo and nicotine would be a valuable addition to the manuscript. I still think the minimal effect of nicotine on pain is not meaningful and not interpretable. The relevance of any explanatory variable like stress could be by chance (PMID: 35296861). Reviewer 3 had a valid point (comment 6) and this is something that should be mentioned as clearly as possible: there was no effect of nicotine. For PHP the comparison with the placebo is irrelevant if there is no pre vs. post-effect.

      It is fair to say that some issues could have been resolved using a cross-over design, however, the choice of a parallel design was made, in part, due to the desire to mask the presence of a placebo gum. Having a single session per participant allowed us to produce a deception that all participants were receiving nicotine gum, which was later revealed during a debrief. This aspect is far less feasible in a cross-over design. In future, different approaches could be used. And we appreciated the reviewers recognition that this cannot, of course, be changed at this stage.

      Regarding the comments of 1) ’I would not consider the effect of nicotine to be meaningful’, 2) the minimal effect of nicotine on pain is not meaningful and not interpretable’, and 3) ’there was no effect of nicotine’, we discern that the latter differs considerably from the first two points. We would like to address this point by first calling into question what the reviewer(s) mean by meaningful, and highlighting that discerning this varies by context. Edenberg (2021) highlights that meaning can be situated within several contexts: statistical, biological (mechanistic), clinical, and public policy. We show the statistical context, and therefore would like to emphasise that we cannot state number 3) ’there was no effect of nicotine’.

      Although the complexity of our analysis is not at the same scale, we appreciate the need for thousands of participants for brain-wide associations, as cited (PMID: 35296861 = Marek et al., 2022). The article referenced states that reproducible brain-wide association studies require thousands of individuals, and thus we would like to highlight that our work indicating the potential relevance of sex/stress greatly differs from this. Though it may be by chance, the potential for that chance is 0.05 from a statistical significance perspective. Certainly, no finding should be taken as truth without replication, but that does not mean we should not report our finding of a statistically significant effect of stress on change in PAF in our model.

      Then, the question becomes, are we already at the point where the issue of ’how to go beyond statistical significance’ should be addressed? One could argue no, as this is the first study to assess this question of nicotine’s effect on PAF and pain at the same time. But we would like to argue yes, although only to the mechanistic/biological level, because the question of what is meaningful is dependent on the study goals (Edenberg, 2021). We aimed to gain mechanistic insight into the PAF-pain relationship.

      We hoped to achieve some biological/mechanistic meaning in the present study, however, as outlined in the discussion, with small effect sizes for nicotine on PAF and nicotine on heat pain, and lack of a mediating effect, we may not have achieved this. Although, if replicated, even small magnitude effects can shape our understanding of relevant mechanisms underlying pain and aid future clinical perspectives (Edenberg, 2021; Ross & Bassett, 2024). Meaningfulness in clinical or public policy contexts should of course be in mind, but were clearly not the focus of this present work.

      We have edited the manuscript to demonstrate the fact that our effect size is small.

      We corrected the rounding to 2 decimals, and now also refer the reader to the supplementary materials table:

      “Change in pain was reduced by a factor of -0.68 for the nicotine group compared to the placebo group when controlling for confounding variables (Figure 3). See Supplementary Material 3.2, Table 5, for full model output.”

      We edited the abstract and the first paragraph of the discussion to make clear to the reader that the effect sizes were small. In our desire to keep the text clear and readable, we did not intend to overstretch our claims, and apologise if the manuscript was unintentionally portraying this overstretch. These are very important sections of the manuscript in which to mention such nuances, as these are the parts viewed most when readers do not wish to read the entire manuscript.

      Abstract

      “The nicotine group showed a small decrease in heat-pain ratings compared to placebo group when controlling confounders, and a small increase in PAF across the scalp from pre- to post-gum, both with and without confounder adjustment. These effects were most pronounced in the central-parietal and right-frontal electrodes.”

      Discussion first paragraph

      “Compared to placebo, our data demonstrate three key findings: 1) nicotine increased PAF speed; 2) nicotine reduced prolonged heat pain intensity but only when controlling for confounding and not for the prolonged pressure pain model, and 3) decreases in prolonged heat pain intensity were not mediated by changes in PAF. This suggests that changes in heat pain due to nicotine occur through mechanisms unrelated to change in PAF and require replication as the effects required control for confounding and the reduction was small in magnitude.”

      Discussion section on effect of nicotine on PAF:

      “In line with previous literature in non-smokers [38,47,48], we contribute additional evidence that chewing 4 mg of nicotine gum produces a statistically significant increase in PAF speed in non-smoking, nicotine-gum-naïve, pain-free, adult participants. An exploratory cluster-based permutation analysis indicated that the change in wide-window PAF (8–12 Hz) produced by nicotine, was most pronounced in a cluster of electrodes in the central-parietal region and a separate cluster of electrodes in the right-frontal region, rather than in the pre-registered sensorimotor ROI (i.e., Cz, C1, C2, C3, C4).”

      Discussion section on the effect of nicotine on pain:

      “While acknowledging the modest effect size, it’s essential to consider the context of our study’s focus. Assessing the clinical relevance of pain reduction is pertinent in applications involving the use of any intervention for pain management [71]. However, from a mechanistic standpoint, particularly in understanding the implications of and relation to PAF, the specific magnitude of the pain effect becomes less pivotal, as small effects can still have mechanistic or biological meaning without establishing clinical meaning [72]. Nevertheless, future research should examine whether effects on pain increase in magnitude with different nicotine administration regimens (i.e. dose and frequency).” 

      Discussion section on relationship between PAF and pain:

      “However, as this is the first study attempting to directly manipulate PAF, observing only small effects on pain, we cannot confidently state that a causal relationship between PAF and pain sensitivity does not exist, and future research should explore these relationships with larger sample sizes, larger doses of nicotine, and alternative PAF modulators.”

      Discussion final paragraph:

      “We have shown that, compared to placebo, nicotine gum produced statistically significant increases global PAF speed and decreases pain ratings during prolonged heat pain. However, the effects of nicotine on heat pain were not mediated by changes in PAF. Therefore, we find no evidence that PAF is causally related to pain. The implication of this is that changing PAF may not be a useful target for pain modulation, because pain sensitivity may not be dependent on state changes in PAF. However, this is the first study to test modulation of PAF as a mechanism for reducing pain intensity. Moreover, while effects on PAF appear small but robust, effects on heat pain required control for confounding to be observed. More randomised experiments on the effects of nicotine that use larger sample sizes, higher nicotine doses, and pharmacokinetic tracking, whilst also reducing mediator measurement error are needed to confirm the present findings and uncover whether these factors account for the lack of mediation effect seen here.”

      (2) I still think the authors made a mistake in using nicotine. Their new wording did not convince me, and I doubt that any reader would buy the "mediation by design" phrase.

      We addressed the reviewers previous comment (comment 1) on nicotine being a ‘mistake’, and no longer suggest there is a “large body of evidence suggests that nicotine is an ideal choice for manipulating PAF”. We have been clearer about our intention to assess mediation-by-design, with the manipulation of PAF being out primary aim. For example, this edit in the discussion:

      “The choice of nicotine was driven by its potential to change PAF, but also, short-term nicotine use is thought to have acute analgesic properties in experimental settings, with a review reporting that nicotine increased pain thresholds and pain tolerance [51].”

      In addition, we discussed the ’direct’ manipulation of PAF using non-invasive brain stimulation methods, and have now added further future research directions using methods other than nicotine or NIBS:

      “Furthermore, there may have been other mediators that suppress the mediating effects of PAF within our model [66,82,83]. This is plausible, as nicotine is thought to act on pain through multiple pathways [52,54,84], and more direct PAF modulation could more definitively evaluate whether PAF is mechanistically linked to pain sensitivity. Future interventions to modulate PAF could use non-invasive brain stimulation (NIBS), such as transcranial alternating current stimulation (tACS) or repetitive transcranial magnetic stimulation (rTMS), to influence neuronal firing and thereby directly target the brain mechanisms theorised to generate PAF [85–87]. This approach has since been investigated following the initial preprint of

      the present manuscript [88,89]. In addition, other approaches to modulating approaches could be considered, such as exercise [32–34], visual stimulation [35,36], cannabis [90,91], and neurofeedback [92,93], while considering their viability in terms of blinding, tolerability, and scalability.”

      (3) I acknowledge the work of the authors on SNR, the frequency spectrum looks smooth enough to detect peaks. However, the problem of different alpha sources is not solved. This can be seen in the frequency spectrum, where some participants show two peaks. This is not the first time I have suggested this to the authors; the idea is not new. The fMRI analogue would be to average all GM voxels; instead of global alpha it would be "global brain activity". Some suggestions for a future approach that the authors might consider:

      Run a group ICA and select topographies from there. This should simplify the (potentially arbitrary) selection process.

      Consider filtering the data before running the ICA, at least >20 Hz to exclude muscle artefacts.

      We respectfully note that the reviewer’s comment appears to overlook the substantial revisions we have already made in direct response to this issue. Specifically, we implemented ICA in the revised manuscript, using an automated, objective pipeline to identify components with a clear alpha peak and a topography aligned with a predefined sensorimotor template. This was explicitly done to address concerns about overlapping alpha sources and improve anatomical specificity.

      Contrary to the reviewer’s implication, we did not rely solely on global analyses in the original or revised manuscript, as we also included pre-defined ROIs and data-driven ROIs from cluster-based permutation analysis. The additional ICA-based analyses—included in the first revision—produced results that were consistent with the original sensor-space ROI findings, supporting the robustness of the PAF–pain mediation effect regardless of the method used to isolate sensorimotor alpha.

      We agree that group ICA could be a valuable complementary approach. However, it is not without limitations, particularly in EEG where inter-individual variability in source topographies is high. Our choice to perform ICA at the individual level and apply an automated selection criterion based on spectral and spatial features was deliberate, data-driven, and avoids the subjectivity involved in manual selection or group-level back-projection.

      We have added a discussion of this point and fully acknowledge that future work may benefit from comparing multiple alpha sources (e.g., mu vs. occipital) more explicitly. However, we must emphasise that this is not a missing analysis—it is already included in the revised manuscript. In this second revision, we have added an additional reference to this supplementary analysis within the section previously titled “Exploratory cluster-based permutation anlaysis”, now titled “Exploratory data-driven analysis of alpha”, in case the previous reference to it was in a sub-optimal location:

      “Lastly, use of in-house code developed to automatically extract a sensorimotor alpha component using independent component analysis (ICA) showed similar results to the sensorimotor ROI mediation analysis (Supplementary Material 3.11). This supports the robustness of the PAF-pain effect regardless of the method used to isolate sensorimotor alpha.”

      We strongly disagree with the suggestion to apply a low-pass filter below 20 Hz prior to ICA. This would remove high-frequency content, including muscle activity—the very signals ICA is designed to isolate and separate from neural activity.

      By removing muscle-related frequencies before ICA, the reviewer’s proposed approach would prevent ICA from identifying muscle components in the data. This is methodologically flawed. as ICA works best when it has access to the full spectral range of the signal, allowing it to separate statistically independent sources— including muscle, eye movements, and neural oscillations—based on their spatial and temporal structure (Onton et al., 2006). Thus the desired sensorimotor alpha component would be more distinct if the full spectral range is included. Low-pass filtering the data before ICA designed to identify alpha would severely compromise artifact removal, degrade component separation, and reduce the effectiveness of our preprocessing pipeline.

      References for responses to reviewer 2

      Edenberg HJ. Perspective on beyond statistical significance: Finding meaningful effects. Complex Psychiatry 2021;7:1–8. https://doi.org/10.1159/000517237.

      Marek S, Tervo-Clemmens B, Calabro FJ, Montez DF, Kay BP, Hatoum AS, Donohue MR, Foran W, Miller RL, Hendrickson TJ, Malone SM. Reproducible brain-wide association studies require thousands of individuals. Nature. 2022 Mar 24;603(7902):654-60.

      Ross LN, Bassett DS. Causation in neuroscience: keeping mechanism meaningful. Nature Reviews Neuroscience. 2024 Feb;25(2):81-90.

      Reviewer #3 (Recommendations for the authors):

      I would like to thank the authors for the time and dedication that they clearly put into addressing the reviewer's comments. As researchers, we alternate between both sides (as authors and reviewers) and we are all privy of how difficult these tasks can be.

      For me as a reviewer, this is one of the tough times. I wanted to support this manuscript because it is clear that conducting the study had to be a monumental effort, and there were early indications that it was rigorously carried out. Specifically referring to rigor, I value preregistration as a tool to assess the strength of the hypothesis posed before conducting the study, and the severity with which the claims are tested. During my first review, I tried to access the preregistration and even provided my email address as a sign of transparency, but access was not granted. During my second review, the main file in the submission system contained two versions of the same manuscript (the first one corresponding to the old version with the wrong preregistration link). I was not initially aware of this and I apologize for the misunderstanding.

      With respect to the rest of my observations, I see that the authors made concessions on small and less relevant issues (e.g. comments #1, #2, #3), but did not satisfactorily address the main ones (#4, #5, #6, #7, #8 and #9). Addressing those comments (which are in line with the issues noted by other reviewers), would probably have lead to a different interpretation of the results compared with what they state in the first paragraph of the discussion.

      The main claims (abstract and first paragraph of the discussion) are " 1) nicotine increased PAF speed; 2) nicotine reduced prolonged heat pain intensity but not prolonged pressure pain intensity compared to placebo gum". Just by reading and contrasting the claims with the results, my assessment is that the strength of evidence is inadequate.

      I was now able to review the analysis plan, which did not contain an estimation of the effect sizes (only effect directions) and did not have a proper sample size estimation (comment #4) and the main outcome was not, to my understanding, based in terms of the beta coefficients (as you replied to reviewer #1). I also do not think that the possibility of no effect or a false positive (comment #5) is fairly weighed in relation to these main claims in the abstract an first paragraph of the discussion.

      I also do not consider the response to comment #6 as satisfactory, first because it is a mistake to consider that we (as reviewers) only interpret the 'mean results'. As we have detailed access to the data, we interpret these results in terms of signal-to-noise ratio, i.e., how large is the effect (signal) compared with the intra and interindividual variance (noise), and it should be clear for anyone working on this fields (pain and EEG) that not only the main effect is not experimentally relevant to support the claims (comments #6 and #7), but in some cases it is likely to have arisen from the unjustified inclusion of covariates (comment #8 and #9). I only raise the final strength of evidence in my assessment from 'inadequate' to 'incomplete', because of the additions to the discussion.

      As a final thought, I would have been more than happy to support and recommend the reading of a manuscript that described a carefully designed and preregistered study, but in which the hypothesis were not corroborated by the data. I would have even marked the strength of evidence as compelling. Unfortunately, the preregistered hypothesis cannot be severely tested (at least not in terms of a frequentist framework) because the effects sizes were not predefined and the required sample size was not estimated, and what I see from the manuscript is that there is an effort to maintain claims that are not properly supported by the data and the final analysis. I recognized that I myself can also be in the wrong, so it will be left for eLife readers to make up their own minds.

      We respectfully disagree with the assertion that our preregistered hypotheses "cannot be severely tested" due to the absence of predefined effect sizes and sample size estimation. First, the primary purpose of preregistration is to increase transparency and reduce analytical flexibility—not necessarily to formalize power calculations, especially when reliable effect size estimates are unavailable, as is the case in emerging areas of research such as this one (Nosek et al., 2018). Predefining effect sizes based on speculative or contextually irrelevant prior studies would have introduced unjustified assumptions and potentially distorted interpretation. In this case, we made the scientifically responsible choice to avoid anchoring our design on uncertain estimates. 

      Second, our sample size is comparable to or larger than those used in prior published studies addressing similar questions, and our analytic pipeline followed the preregistered plan. The reviewer suggests that we are attempting to maintain unsupported claims; however, our discussion is careful to reflect the limitations of the findings, including their statistical uncertainty, and we do not overstate conclusions. Where effects were weak or absent, we reported this transparently and interpreted them cautiously.

      Finally, while formal power calculations are useful under certain conditions, they are not a prerequisite for a study to be considered a "severe test" of a hypothesis—especially when the statistical approach is preregistered, data are handled transparently, and null results are acknowledged rather than hidden. The sample size was informed by resource and feasibility constraints (Lakens, 2022) and aligns with or exceeds that of comparable studies in the field (Bowers et al., 2015). We have now made this rationale explicit in the manuscript.

      “The sample size was informed by resource and feasibility constraints [98] and aligns with or exceeds that of comparable studies in the field [38], covering 60 participants in total, with two extra in case of incomplete data identified during later data analysis.”

      We therefore maintain that the study is a valid and informative contribution, regardless of whether the observed results confirm or disconfirm the hypotheses.

      Nonetheless, below we have revisited previous comments (#4, #5, #6, #7, #8 and #9) that reviewer 3 stated were not satisfactorily addressed.

      Previous comment 4) Availability of the pre-registration

      We consider this point now addressed, as access to the OSF pre-registration was resolved. Moreover, we can assure the reviewer that their identity was not revealed, as the request for access was not received/seen.

      Previous comment 5) Magnitude of pain change – possibility of a type 1 error.

      Previous comment 5) To be perfectly clear, I trust the results of this study more than some of the cited studies regarding nicotine and pain because it was preregistered, the sample size is considerably larger, and it seems carefully controlled. I just do not agree with the interpretation of the results, stated in the first paragraph of the Discussion. Quoting J. Cohen, "The primary product of a research inquiry is one or more measures of effect size, not P values" (Cohen, 1990). As I am sure the authors are aware of, even tiny differences between conditions, treatments or groups will eventually be statistically significant given arbitrarily large sample sizes. What really matters then is the magnitude of these differences. In general, the authors hypothesize on why there were no differences on the pressure pain model, and why decreases in heat pain were not mediated by PAF, but do not seem to consider the possibility that the intervention just did not cause the intended effect on the nociceptive system, which would be a much more straightforward explanations for all observations.

      Our previous response included the fact that N=62 is not an arbitrarily large sample size and our consideration of the possibility of a false positive. In addition, we agree that conclusions should not be made based on p-values alone. Therefore, we have added more careful descriptions to highlight the nuances of our findings to the reader.

      We edited the abstract and the first paragraph of the discussion to make clear to the reader that the effect sizes were small. In our desire to keep the text clear and readable, we did not intend to overstretch our claims, and apologise if the manuscript was unintentionally portraying this overstretch. These are very important sections of the manuscript in which to mention such nuances, as these are the parts viewed most when readers do not wish to read the entire manuscript.

      Abstract

      “The nicotine group showed a small decrease in heat-pain ratings compared to placebo group when controlling confounders, and a small increase in PAF across the scalp from pre- to post-gum, both with and without confounder adjustment. These effects were most pronounced in the central-parietal and right-frontal electrodes.”

      Discussion first paragraph

      “Compared to placebo, our data demonstrate three key findings: 1) nicotine increased PAF speed; 2) nicotine reduced prolonged heat pain intensity but only when controlling for confounding and not for the prolonged pressure pain model, and 3) decreases in prolonged heat pain intensity were not mediated by changes in PAF. This suggests that changes in heat pain due to nicotine occur through mechanisms unrelated to change in PAF and require replication as the effects required control for confounding and the reduction was small in magnitude.”

      Discussion section on effect of nicotine on PAF:

      “In line with previous literature in non-smokers [38,47,48], we contribute additional evidence that chewing 4 mg of nicotine gum produces a statistically significant increase in PAF speed in non-smoking, nicotine-gum-naïve, pain-free, adult participants. An exploratory cluster-based permutation analysis indicated that the change in wide-window PAF (8–12 Hz) produced by nicotine, was most pronounced in a cluster of electrodes in the central-parietal region and a separate cluster of electrodes in the right-frontal region, rather than in the pre-registered sensorimotor ROI (i.e., Cz, C1, C2, C3, C4).”

      Discussion section on the effect of nicotine on pain:

      “While acknowledging the modest effect size, it’s essential to consider the context of our study’s focus. Assessing the clinical relevance of pain reduction is pertinent in applications involving the use of any intervention for pain management [71]. However, from a mechanistic standpoint, particularly in understanding the implications of and relation to PAF, the specific magnitude of the pain effect becomes less pivotal, as small effects can still have mechanistic or biological meaning without establishing clinical meaning [72]. Nevertheless, future research should examine whether effects on pain increase in magnitude with different nicotine administration regimens (i.e. dose and frequency).”

      Discussion section on relationship between PAF and pain:

      “However, as this is the first study attempting to directly manipulate PAF, observing only small effects on pain, we cannot confidently state that a causal relationship between PAF and pain sensitivity does not exist, and future research should explore these relationships with larger sample sizes, larger doses of nicotine, and alternative PAF modulators.”

      Discussion final paragraph:

      “We have shown that, compared to placebo, nicotine gum produced statistically significant increases global PAF speed and decreases pain ratings during prolonged heat pain. However, the effects of nicotine on heat pain were not mediated by changes in PAF. Therefore, we find no evidence that PAF is causally related to pain. The implication of this is that changing PAF may not be a useful target for pain modulation, because pain sensitivity may not be dependent on state changes in PAF. However, this is the first study to test modulation of PAF as a mechanism for reducing pain intensity. Moreover, while effects on PAF appear small but robust, effects on heat pain required control for confounding to be observed. More randomised experiments on the effects of nicotine that use larger sample sizes, higher nicotine doses, and pharmacokinetic tracking, whilst also reducing mediator measurement error are needed to confirm the present findings and uncover whether these factors account for the lack of mediation effect seen here.”

      Previous comment 6) Magnitude of pain change

      Previous comment (6) In this regard, I do not believe that an average *increase* of 0.05 / 10 (Nicotine post pre) can be considered a "reduction of pain ratings", regardless of the contrast with placebo (average increase of 0.24 / 10). This tiny effect size is more relevant in the context of the considerable inter-individual variation, in which subjects scored the same heat pain model anywhere from 1 to 10, and the same pressure pain model anywhere from 1 to 8.5. In this regard, the minimum clinically or experimentally important differences (MID) in pain ratings varies from study to study and across painful conditions but is rarely below 1 / 10 in a VAS or NRS scale, see f. ex. (Olsen et al., 2017). It is not my intention to question whether nicotine can function as an acute analgesic in general (as stated in the Discussion), but instead, if it worked as such under these very specific experimental conditions. I also acknowledge that the authors note this issue in two lines in the Discussion, but I believe that this is not weighed properly.

      Our previous response included discussion of interpreting mean values, a correction to a table that showed the ”increase” erroneously displayed previously due to list-wise deletion in the analysis. We have further attempted to weigh this issue more thoroughly and to always highlight the nuances of our results, as seen in our response to your previous comment 5 above. In further consideration of the effect size, note that the bootstrapped 95% CI for the effect of gum on change in pain was [-1.28, -0.16], which indicates that the overall difference falls within this range when controlling for other factors in the model. Of course this means the difference may be as small as -0.16, but also may be as large as -1.28. Such an effect might have be considered clinically relevant. Replication of the results is therefore warranted.

      Also, as outlined in our response to reviewer 2 comment 1, our intention was not to establish a clinical utility at this stage. We hoped to achieve some biological/mechanistic meaning in the present study, and if our present findings are replicated in future, even these small-magnitude effects can shape our understanding of relevant mechanisms underlying pain and aid the direction of future clinical perspectives (Edenberg, 2021; Ross & Bassett, 2024). Meaningfulness in clinical (e.g., MID) or public policy contexts should of course be in mind, but were not the focus of this present work.

      Several additional changes were made to the manuscript to emphasise these points to the reader, which are also outlined in the second round of response to your first comment 5 above, as both this comment 6 and 5 focus on magnitude of pain change. We hope this point is now considered to be weighed properly.

      Previous comment 7) Magnitude of PAF change

      Previous comment (7) In line with the topic of effect sizes, average effect sizes for PAF in the study cited in the manuscript range from around 1 Hz (Boord et al., 2008; Wydenkeller et al., 2009; Lim et al., 2016), to 2 Hz (Foulds et al., 1994), compared with changes of 0.06 Hz (Nicotine post - pre) or -0.01 Hz (Placebo post - pre). MIDs are not so clearly established for peak frequencies in EEG bands, but they should be certainly larger than some fractions of a Hertz (which is considerably below the reliability of the measurement).

      In our first response to this comment, we acknowledged this difference in magnitude, agreed that MIDs for PAF are not established, discussed the potential impact of bin size, and highlighted this issue in the revised manuscript text. Although, note that we have now slightly reduced the emphasis on the bin size:

      “The ability to detect changes in PAF could be considerably impacted by the frequency resolution used during Fourier Transformations, an element that is overlooked in recent methodological studies on PAF calculation [16,95].”

      In addition, we would now like to highlight some more details regarding the prior studies.

      We aimed to determine whether nicotine gum could increase PAF in healthy, pain-free, non-smokers. In line with previous literature in non-smokers (Foulds et al., 1994; Harkrider and Champlin, 2001; Bowers et al., 2015), we contribute additional evidence that chewing 4 mg of nicotine gum produces small increases in PAF speed in non-smoking, nicotine-gum-naïve, pain-free, adult participants. The other three papers mentioned by the reviewer are not cited in our manuscript and compare healthy individuals to chronic pain patients (Boord et al., 2008; Wydenkeller et al., 2009; Lim et al., 2016), and are thus not relevant to this discussion on the effect of nicotine on PAF.

      A cluster-based permutation analysis indicated that the change in wide window PAF (8-12 Hz) produced by nicotine, was most pronounced in a cluster of electrodes in the central-parietal region and a separate cluster of electrodes in the right-frontal region, rather than in the pre-registered sensorimotor ROI (i.e., Cz, C1, C2, C3, C4). The mediation analysis results showed minimal differences when these clusters of electrodes were used compared to global results (global: b = 0.085, p < .018), except for the expected stronger effect of nicotine on change in PAF alongside greater confidence in this effect (bs = 0.11-0.14, ps < .003). See Supplementary Material 3.8-3.10.

      Previous work examining nicotine-induced changes in PAF in healthy non-smokers have used small samples (i.e. <= 20) with nicotine injections or patches (Foulds et al., 1994; Harkrider and Champlin, 2001), while a later investigation used 62 male participants and nicotine gum (Bowers et al., 2015). Therefore, the present study is the largest study to date on nicotine and PAF including non-smoking male and female participants. Bowers didn’t see effects as large as 1 or 2 Hz (approx. 10 or 20% increases) seen in studies with fewer participants, such as n=4 (Foulds et al., 1994) and n=20 (Harkrider & Champlin, 2001), and the magnitude and location of effect depended on the COMT (Bowers et al., 2015).

      Bowers et al (2015) showed that the Met allele was related to nicotine-induced increases in PAF, whereas Val/Val homozygotes did not demonstrate PAF changes. In addition, the distribution of PAF increases varied depending on whether Met allele carriers were heterozygotes (i.e. Val/Met: frontal, central, and occipital electrodes) or homozygotes (i.e. Met/Met: parietal electrode). The largest difference between placebo and nicotine gum was 0.51 Hz (a 5.8% increase) at the Fz electrode for the Val/Met group and the smallest significant difference was 0.34 Hz (a 3.5% increase) at the Pz electrode for the Met/Met group.

      This study from Bowers used 6mg of nicotine gum, whereas we used 4mg, which may contribute to the lower effect size seen in our study. Dose-dependent effects have not been assessed in non-smokers, but given the dose-dependent changes seen in smokers who abstained from cigarettes prior to EEG recording (Pickworth et al., 1989; Pickworth et al., 1988; Pickworth et al., 1986), the smaller effect sizes seen in the present study may be in line with Bowers study.

      Though genetic analysis was not included in the present work, the use of a lower nicotine dose, inclusion of male and female participants, use of more electrodes (64 rather than 8), and unmeasured genetic variations in PAF’s response to nicotine could explain the smaller effect sizes compared to (Bowers et al., 2015).

      We have written a condensed summary of this to include in the manuscript discussion:

      ”Research on nicotine-induced changes in PAF in healthy non-smokers has largely relied on small samples (≤20) using injections or patches [47,48], with Bowers and colleagues [38] providing the only larger study (n= 62 males) using 6 mg nicotine gum. Their results showed modest PAF increases (~0.34–0.51 Hz; 3.5– 5.8%) compared to the larger effects (1–2 Hz; ~10–20%) reported in earlier small-sample studies, with magnitude and scalp distribution influenced by COMT genotype: Met allele carriers exhibited nicotineinduced increases (Val/Met: frontal, central, occipital; Met/Met: parietal), while Val/Val homozygotes showed no change. The present study now the largest to include both male and female non-smokers found smaller effects, likely due to the lower nicotine dose (4 mg), consistent with dose-dependent PAF modulation reported in abstinent smokers [69]. Broader EEG coverage (64 vs. 8 electrodes), sex inclusion, and unmeasured genetic variation may also account for differences between the present study and Bowers and colleagues [38]. Interestingly, beyond nicotine’s main effect on PAF, our 2W-LCS mediation model indicated a significant influence of sex, with females showing greater PAF increases than males. Given that female participants were significantly lighter than males (Supplementary Material 3.4) and the model did not test the interaction between sex at birth and gum group, these finding should be interpreted cautiously and warrant further investigation.”

      Previous comment 8) removing confounders calls to question robustness of the findings. Simmons paper

      Previous comment (8) The authors also ran alternative statistical models to analyze the data and did not find consistent results in terms of PHP ratings (PAF modulation was still statistically significantly different). The authors attribute this to the necessity of controlling for covariates. Now, considering the effects sizes, aren't these statistically significant differences just artifacts stemming from the inclusion of too many covariates (Simmons et al., 2011)? How much influence should be attributable to depression and anxiety symptoms, stress, sleep quality and past pain, considering that these are healthy volunteers? Should these contrasting differences call the authors to question the robustness of the findings (i.e., whether the same data subjected to different analysis provides the same results), particularly when the results do not align with the preregistered hypothesis (PAF modulation should occur on sensorimotor ROIs)?

      In addition to our previous response, we would like to add the following: Although we were previously unaware of the author recommendations from Simmons et al (2011) during initial preparation of this manuscript, we find we cover all points and have added a few improvements to ensure our adherence to this guideline is clear.

      We cover all six recommendations for authors suggested in Simmons et al (2011):

      (1) We decided to collect 62 participants prior to commencing data collection, this covered 60 participants in total, with two extra in case of incomplete data identified during data analysis.

      (2) We had more than 20 participants per group. We have now outlined this decision in the methods section:

      “The sample size was informed by resource and feasibility constraints [98] and aligns with or exceeds that of comparable studies in the field [38], covering 60 participants in total, with two extra in case of incomplete data identified during later data analysis.”

      (3) We provide detailed methods, which outlines all the variables collected.

      (4) We report all experimental conditions, and had no failed manipulations to report. We have now slightly adjusted the wording of our experimental protocol within the methods section to make this clear:

      “Participants were randomly assigned to one of only two conditions, thus after the second resting-state EEG, either nicotine or placebo gum was administered with the chew procedure. Following completion of the chew procedure, the third resting state, the second pain assessments, and the fouth resting state were conducted.”

      Regarding recommendation (5), listwise deletion was used, as already stated in the manuscript (see Methods, Statistical analysis, Mediation analysis, Assumptions), to exclude participants for whom only one timepoint was available in either the pain or PAF measures, and thus it is not possible to conduct analysis on participants with this missing data. Otherwise, no participants were removed for other reasons. 6) As we conducted analyses using pre-registered covariates determined based on a DAG, we repeated analyses without including these covariates in the form of RM-ANOVAs. The effect on PAF remains, however, as Simmons et al (2011) suggests, the fact we no longer observed a significant effect of gum on heat pain ratings may indicate that the finding is reliant on the presence of a covariate, which does not necessarily mean that the finding is not relevant. However, as reviewer 3 suggests, this should also cause us to question the robustness of the findings and the possibility of type 1 error. Therefore, we have adjusted text in the discussion as follows:

      “This underscores the necessity of controlling for confounding variables, as nicotine may only produce pain reduction for those with higher stress, and calls for further investigation into the robustness of the effect of nicotine on heat pain ratings.”

      Lastly, regarding the influence that should be attributable to our confounding health-related measures, given the healthy population, we still observe variation in several of these confounders. ’Healthy’ populations still score across a range on these scales, with cut-offs acting as suggestions for problematic symptomology. Assumptions testing confirmed the normality of these covariates, and lack of collinearity so that they could be included in our analyses. We have added a sentence to the Sample Characteristics in Results to outline the ranges reported for the confounding variables:

      “Depressive symptoms ranged from 0-4 (out of a maximum of 6), anxiety from 0-6 (out of a maximum of 6), perceived stress from 2-18 (out of a maximum of 40), and sleep quality from 2-10 (out of a maximum of 10; i.e. “excellent sleep quality”).”

      Previous comment 9) Exploratory sex analysis?

      (9) Beyond that, I believe in some cases that the authors overreach in an attempt to provide explanations for their results. While I agree that sex might be a relevant covariate, I cannot say whether the authors are confirming a pre-registered hypothesis regarding the gender-specific correlation of PAF and pain, or if this is just a post hoc subgroup analysis. Given the large number of analyses performed (considering the main document and the supplementary files), caution should be exercised on the selective interpretation of those that align with the researchers' hypotheses.

      To reiterate our previous response to this comment, we stated that sex was an exploratory analysis in the results and was chosen based on other PAF-pain literature, and had also adjusted part of the discussion to align with this. However, we have now seen the first paragraph of the discussion was not adjusted. Therefore, we hope the below edit has now adequately address the previous reviewer 3 comment 9:

      “In addition, when assessing the whole sample, we found inconclusive evidence for 4) slower PAF speed at baseline being associated with higher pain ratings for both the heat and pressure pain models. However, during exploratory analysis we found moderate evidence that slower PAF speed at baseline is associated with higher heat pain ratings at baseline in males but not females. In contrast PAF was not associated with pressure pain ratings for males or females.”

      References for response to reviewer 3

      Boord P, Siddall PJ, Tran Y, Herbert D, Middleton J, Craig A. Electroencephalographic slowing and reduced reactivity in neuropathic pain following spinal cord injury. Spinal cord. 2008 Feb;46(2):118-23.

      Bowers H, Smith D, De La Salle S, Choueiry J, Impey D, Philippe T, et al. COMT polymorphism modulates the resting-state EEG alpha oscillatory response to acute nicotine in male non-smokers. Genes, Brain and Behavior 2015;14:466–76.

      Edenberg HJ. Perspective on beyond statistical significance: Finding meaningful effects. Complex Psychiatry 2021;7:1–8. https://doi.org/10.1159/000517237.

      Foulds J, McSorley K, Sneddon J, Feyerabend C, Jarvis MJ, Russell MA. Effect of subcutaneous nicotine injections on EEG alpha frequency in non-smokers: A placebo-controlled pilot study. Psychopharmacology 1994;115:163–6.

      Harkrider AW, Champlin CA. Acute effect of nicotine on non-smokers: III. LLRs and EEGs. Hearing Research 2001;160:99–110.

      Lakens D. Sample size justification. Collabra: psychology. 2022 Mar 22;8(1):33267.

      Lim M, Kim JS, Kim DJ, Chung CK. Increased low-and high-frequency oscillatory activity in the prefrontal cortex of fibromyalgia patients. Frontiers in human neuroscience. 2016 Mar 14;10:111.

      Nosek BA, Ebersole CR, DeHaven AC, Mellor DT. The preregistration revolution. Proceedings of the National Academy of Sciences. 2018 Mar 13;115(11):2600-6.

      Pickworth WB, Herning RI, Henningfield JE. Electroencephalographic effects of nicotine chewing gum in humans. Pharmacology Biochemistry and Behavior 1986;25:879–82.

      Pickworth WB, Herning RI, Henningfield JE. Mecamylamine reduces some EEG effects of nicotine chewing gum in humans. Pharmacology, Biochemistry, and Behavior 1988;30:149–53.

      Pickworth WB, Herning RI, Henningfield JE. Spontaneous EEG changes during tobacco abstinence and nicotine substitution in human volunteers. Journal of Pharmacology and Experimental Therapeutics 1989;251:976–82.

      Ross LN, Bassett DS. Causation in neuroscience: keeping mechanism meaningful. Nature Reviews Neuroscience. 2024 Feb;25(2):81-90.

      Simmons JP, Nelson LD, Simonsohn U. False-positive psychology: Undisclosed flexibility in data collection and analysis allows presenting anything as significant. Psychological science. 2011 Nov;22(11):1359-66.

      Wydenkeller S, Maurizio S, Dietz V, Halder P. Neuropathic pain in spinal cord injury: significance of clinical and electrophysiological measures. European Journal of Neuroscience. 2009 Jul;30(1):91-9.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      In this manuscript, the authors investigated factors required for neural progenitors to exit the cell cycle before the adult stage. They first show that Kr is turned on in pupal stage MBNBs, and depletion of Kr from pupal stage NBs leads to retention of MBNBs into the adult stage. Then they demonstrate that these retained NBs maintain the expression of Imp, and co-depletion of Imp abolishes the extended neurogenesis. Further, they show that co-depletion of kr-h1 significantly reduces the retained MBNBs caused by loss of kr, suggesting antagonistic genetic interactions between these two. In addition, they demonstrate that over-expressing Kr-h1 leads to the striking phenotype of tumor-like neuroblast overgrowth in adult brains.

      Strengths:

      (1) The authors leveraged well-controlled, powerful genetic tools (including temporal control of RNAi knockdown using the Gal80ts system), and provided strong evidence that Kr expression in pupal stage MBNBs is required to repress Imp and promote the end of neurogenesis. Similarly, the experimental result of co-depleting Kr-h1 and Kr, and the striking phenotype upon Kr-h1 mis-expression, support the antagonistic roles played by Kr-h1 and Kr in this process.

      (2) The sample sizes, quantification methods, and p-values are well documented for all experiments. In most parts, the data presented strongly support their conclusions.

      (3) Identification of two transcription factors with opposite roles in controlling cell cycle exit, and their possible interactions with the Imp/Syp axis, is highly significant for the study on how the proliferation of neural progenitors is regulated and limited before the adult stage.

      We thank Reviewer #1 for their thoughtful and constructive assessment of our manuscript. We are grateful that the reviewer recognised the strength of our genetic approaches, the significance of identifying Kr and Kr-h1 as opposing regulators of MBNB termination, and the value of linking these factors to the Imp/Syp axis. We have revised the manuscript substantially in response to the reviewer’s comments. In particular, we have further characterised Kr expression in the KrIf-1 mutant background, examined the relationship between Kr, Kr-h1 and E93, analysed Kr-h1 expression in MBNBs using a Kr-h1::GFP BAC reporter, revised the proposed model, improved figure presentation and corrected typographical errors throughout the manuscript.

      Weaknesses:

      (1) The nature of the KrIf-1 allele is not clear. It is mentioned that this allele leads to misexpression of Kr in various tissues. However, it is not clear if Kr is mis-expressed or lost in MBNBs in the KrIf-1 mutant. If Kr is mis-expressed in MBNBs in the KrIf-1 mutant, then it would be difficult to explain why both loss of Kr and mis-expression of Kr in MBNBs lead to the same NB retention phenotype. The authors should examine Kr expression in MBNBs in the KrIf-1 mutant.

      We agree that clarifying the nature of Kr expression in the KrIf-1 mutant background is important. We have therefore performed additional Kr immunostaining in KrIf-1 mutant brains using tyramide signal amplification (TSA) to enhance the weak endogenous Kr signal. These new data show that Kr is ectopically detected in MBNBs and their progeny in KrIf-1 mutant late pupal and adult brains (Fig. S3G, H), and quantification of TSA-enhanced Kr signals further supports Kr misexpression in MBNBs during late pupal stages (Fig. S3I). We have added these data to the revised manuscript. These results indicate that the KrIf-1 phenotype is associated with aberrant Kr expression in MBNBs rather than a simple loss of Kr expression. We agree with the reviewer that it may appear counterintuitive that both Kr depletion and Kr misexpression can lead to MBNB retention. We now discuss this point more explicitly. Our interpretation is that MBNB termination requires tight control of Kr activity during a narrow developmental window. Loss of Kr prevents the normal progression of the Imp-to-Syp transition and E93 activation, whereas ectopic or mistimed Kr expression in KrIf-1 mutants may also interfere with the same termination programme. Thus, both reduced Kr activity and inappropriate Kr expression can disrupt the precisely regulated Kr-dependent transition required for timely MBNB cell-cycle exit and elimination.

      We have revised the Results and Discussion to make this interpretation clearer and to avoid describing KrIf-1 simply as equivalent to Kr loss of function.

      (2) Some parts of the regulations and interactions between Kr, Kr-h1, Imp, Syp, and E93 are not well-defined. For example, the data suggest that Kr is turned on in the pupal stage MBNBs, and is required to end neurogenesis through repressing Imp and Kr-h1. To further support this conclusion, the authors can examine if Kr-h1 expression is up-regulated in kr-RNAi.

      The authors suggested that Kr-h1 may act upstream or in parallel to Imp/Syp, but also suggested that Kr-h1 may repress E93. The expression of Imp, Syp, and E93 can be examined in brains with Kr-h1 mis-expression to determine where Kr-h1 acts. If Imp expression is elevated when Kr-h1 is mis-expressed, then Kr-h1 may act upstream of Imp. If Imp/Syp expression does not change, then Kr-h1 may act on the E93 level.

      We thank the reviewer for this helpful suggestion. We agree that the regulatory relationships between Kr, Kr-h1, Imp/Syp and E93 were not sufficiently defined in the original manuscript. In the revised manuscript, we have therefore clarified which relationships are supported by our data and which remain unresolved.

      During revision, we placed particular emphasis on the relationship between Kr, Kr-h1 and E93, because our genetic interaction data showed that co-depletion of Kr-h1 partially suppresses MBNB retention caused by Kr depletion (Fig. 5A). This indicated that Kr and Kr-h1 functionally oppose each other during MBNB termination. We therefore asked whether this functional antagonism could be explained by a simple linear pathway in which Kr promotes termination by suppressing Kr-h1, which in turn antagonises E93.

      We first tested whether Kr-h1 regulates E93 in the MBNB lineage. Kr-h1 depletion increased E93 expression in the MBNB lineage, whereas Kr-h1 overexpression strongly reduced E93 expression (Fig. S5B). These data support the conclusion that Kr-h1 antagonises E93 expression in this lineage, consistent with the established antagonistic relationship between Kr-h1 and E93 in other developmental contexts.

      We next examined whether Kr regulates this Kr-h1–E93 axis by suppressing Kr-h1 expression. To address this, we used a functional Kr-h1::GFP BAC reporter. Kr-h1::GFP was readily detected in larval MBNBs but was strongly downregulated during pupal development, consistent with the MBNB-lineage-specific RNA-seq dataset of Liu et al. (2015). However, Kr depletion did not significantly increase Kr-h1::GFP levels in late pupal MBNBs (Fig. 5B and Fig. S5C). Moreover, despite the absence of detectable Kr-h1::GFP upregulation, Kr depletion strongly reduced E93 expression in the progeny region of the MBNB lineage, while the weak E93 signal detectable in MBNBs themselves was not substantially altered (Fig. 5B).

      These results argue against a simple linear pathway in which Kr promotes MBNB termination by directly repressing Kr-h1 expression. Instead, they suggest that Kr supports E93 expression within the MBNB lineage through a mechanism that does not require detectable upregulation of Kr-h1. Thus, Kr and Kr-h1 functionally oppose each other during MBNB termination, but they are unlikely to act through a simple linear Kr–Kr-h1–E93 pathway. We have revised the model accordingly, proposing that Kr and Kr-h1 act through convergent or parallel mechanisms to regulate the MBNB termination programme.

      Regarding the Imp/Syp axis, the original manuscript had already shown that Kr depletion causes persistent Imp expression in adult MBNB lineages and that co-depletion of Imp suppresses MBNB retention caused by Kr depletion. These data supported the conclusion that persistent Imp expression is required for MBNB retention following Kr depletion. In the revised manuscript, we strengthened this conclusion by analysing Imp and Syp expression during late pupal development, when MBNBs normally undergo cell-cycle exit and elimination. We found that Kr-depleted MBNBs maintain higher Imp expression and show reduced Syp expression compared with controls (Fig. 4A, B), supporting the idea that Kr promotes MBNB termination by facilitating the normal Imp-to-Syp transition.

      We also considered whether Kr-h1 acts upstream of the Imp/Syp transition. Kr-h1 overexpression caused persistent Imp expression in proliferating adult NBs (Fig. 5E). However, this manipulation produced a severe tumour-like overgrowth phenotype and likely represents a strongly non-physiological state. We therefore do not conclude that Kr-h1 normally acts upstream of Imp/Syp during MBNB termination. Rather, our revised interpretation is that Kr promotes MBNB termination through the Imp-to-Syp transition and by supporting E93 expression, whereas Kr-h1 counteracts termination at least in part by repressing E93. How the Imp/Syp and E93-associated pathways converge during MBNB termination remains an important question for future work.

      We have revised the Results, Discussion and Fig. 6D model accordingly, distinguishing experimentally supported relationships from more speculative connections.

      Reviewer #2 (Public review):

      Summary:

      In this paper, the authors study the role of Kruppel in regulating the survival of mushroom body neuroblasts. They first confirm that adult wild-type brains have no proliferation and report that Kruppel mutants and Kruppel RNAi in neuroblasts show a few proliferative clones; they show that these proliferative clones are localized in the mushroom body. They then show that Kruppel is expressed mostly during pupal stages and acts by downregulating the expression of Imp, which has been shown to positively regulate neuroblast proliferation and survival. Expectedly, this also affects neuronal diversity in the mushroom body, which is enriched in gamma neurons that are born during the Imp-expression window. Finally, they show that Kr acts antagonistically to Kr-h1, which is expressed predominantly in larval stages.

      Strengths:

      The main strength of this paper is that it identified a novel regulator of Imp expression in the mushroom body neuroblasts. Imp is a conserved RNA-binding protein that has been shown to regulate neural stem cell proliferation and survival in different animals.

      We thank Reviewer #2 for their critical assessment of our manuscript and for the specific suggestions regarding manuscript framing, figure clarity, public dataset analysis and textual accuracy. We have revised the manuscript extensively in response to these comments. In particular, we have clarified that our study does not aim to describe physiological adult neurogenesis in Drosophila, but rather investigates how normally terminating neural progenitors can retain or regain neurogenic potential when the developmental termination programme is disrupted. We have also revised the text to avoid overstatement about functional integration of adult-born neurons, improved figure presentation, removed the incomplete targeted-screen framing, added analysis of public MBNB-lineage transcriptomic data, and corrected multiple textual and citation issues.

      Weaknesses:

      (1) The main weakness of the paper is that the authors want to test adult neurogenesis in a system where no adult neurogenesis exists. To achieve this, they force neuroblasts to survive in adulthood by altering the genetic program that prevents them from terminating their proliferation. If this was reminiscing about "adult neurogenesis", the authors should at least show how adult neurons incorporate into the mushroom body even if they are born much later. On the contrary, this more likely resembles a tumorigenic phenotype, when stem cells divide way past their appropriate timing.

      We appreciate this important point and agree that Drosophila does not normally show substantial physiological neurogenesis in the adult central brain under standard conditions. We have therefore revised the manuscript to clarify the framing of our study. Our aim is not to claim that Kr depletion reveals a normal physiological adult neurogenesis programme, but rather to identify developmental mechanisms that normally terminate MBNB proliferation and restrict latent neurogenic potential in the adult brain.

      We note, however, that the original manuscript already provided evidence that the persistent proliferative cells induced by Kr depletion or the KrIf-1 mutation are associated with the MB lineage and generate neuronal progeny in young adult brains. EdU-positive clones were detected predominantly in the dorsoposterior MB cell body region (Fig. 2A, B). These clones generally contained a single Mira- and insc>GFP-positive NB-like cell, including mitotic cells with cortical Mira localisation (Fig. 2C, D), together with surrounding Elav-positive neuronal progeny (Fig. 2E). In addition, persistent mitotic cells in KrIf-1 mutant brains were found in the MB cell body region marked by mb247>GFP and OK107>GFP, and showed Mira localisation consistent with dividing MBNBs (Fig. 2F-H). Thus, although we have not directly demonstrated mature circuit integration, the original data support the conclusion that Kr depletion and the KrIf-1 mutation allow MBNBs to persist beyond their normal termination window and generate neuronal progeny within the MB region.

      At the same time, our data do not establish the precise neuronal identity, connectivity or functional incorporation of the newly generated progeny into mature MB circuits, nor do they determine the long-term behaviour of these progeny in older adult brains. We have therefore revised the text and Discussion to avoid overinterpreting these cells as fully integrated adult-born MB neurons, and now state that these issues remain important questions for future work.

      We also agree that prolonged progenitor proliferation can become pathological in some contexts. However, we do not think that the Kr-depletion and KrIf-1 phenotypes are equivalent to tumour-like overgrowth, at least under the conditions analysed here. In young adult brains, retained MBNBs remained spatially restricted to the MB cell body region, and each EdU-positive clone generally contained only a single NB-like cell with asymmetric Mira localisation, surrounded by Elav-positive neuronal progeny (Fig. 2C-E, G, H). This pattern is more consistent with persistent asymmetric MBNB divisions than with tumour-like expansion. This contrasts with Kr-h1 overexpression, which caused extensive tumour-like NB overproliferation with impaired neuronal differentiation; we now describe this latter phenotype as tumour-like NB overgrowth (Fig. 5C-E). We have revised the manuscript to distinguish these phenotypes more clearly.

      (2) Moreover, the figures are, in many cases, hard to understand, and the interpretation of the figures doesn't always match what one sees. The manuscript would benefit from better figures; for example, in Figure 2C, Miranda expression in insc>GFP in Kr-IF-1 is not visible.

      We thank the reviewer for pointing out the need to improve figure clarity. We have revised the figure presentation throughout the manuscript to improve readability, including increasing label size, improving panel labelling and ensuring that the interpretation in the Results is consistent with the corresponding figure panels and legends.

      Regarding the specific concern about Fig. 2C, we agree that the Mira signal was not sufficiently clear in the merged image. We have therefore added a Mira-only single-channel panel to Fig. 2C to allow the relevant signal to be evaluated more directly. We have also revised the text to clarify that retained MBNBs were identified based on combined positional, morphological and marker criteria, rather than by Mira signal alone.

      (3) The authors describe a targeted genetic screen, but they don't describe which genes were tested, how they were chosen, and why Kruppel was finally selected.

      We agree that the original description of a targeted genetic screen was insufficient. Because the screen was preliminary and incomplete, we concluded that presenting partial screening information would not be sufficiently informative and could overstate the scope of the present study. We have therefore removed the screen-based framing from the revised manuscript. Instead, the revised manuscript presents Kr as a candidate selected for focused functional analysis based on its known role in neuroblast temporal regulation and the strong MBNB retention phenotype observed upon Kr depletion and in the KrIf-1 mutant background.

      (4) The authors argue that Kr does not behave as a typical tTF in MBNBs. However, they show no expression in the embryo, limited expression in the larva and early pupa, and a peak around P24-P48. This sounds like a temporally regulated expression of a transcription factor. Importantly, they mentioned that they tested their observations against different datasets (FlyAtlas2, modENCODE, and MBNB-lineage-specific RNA-seq data), but they don't provide the data.

      We thank the reviewer for this helpful comment. We agree that our original wording could have been clearer. Our intention was not to argue that Kr cannot have a temporally restricted function in MBNBs, but rather that Kr does not behave like a canonical temporal transcription factor whose expression undergoes a strong stage-specific switch in this lineage.

      We have revised both the text and the corresponding quantification. In the original version, Kr signal levels in pupal MBNBs appeared to vary modestly across pupal stages. However, after reanalysing cytoplasmic and nuclear Kr signals separately using Welch’s ANOVA followed by Dunnett T3 multiple-comparison correction, no pairwise comparisons reached statistical significance (Fig. 3E, F). Thus, the revised quantification does not support a significant temporal change in Kr protein levels during the pupal stages analysed, and we have avoided describing Kr as showing a clear pupal expression peak.

      As requested, we have also included the public MBNB-lineage RNA-seq analysis in the revised manuscript as Fig. S5A. This analysis shows that Kr transcript levels remain low across the analysed developmental stages, in contrast to the stronger temporal changes observed for other regulators, including larval Kr-h1 expression followed by pupal downregulation, reciprocal induction of E93, and marked increases in Syp expression. Because FlyAtlas2 and modENCODE have limited spatial resolution for MBNB-specific expression, we now focus this comparison on the MBNB-lineage-specific RNA-seq dataset.

      We have therefore revised the manuscript to describe Kr as a postembryonic regulator required for pupal MBNB termination, rather than as a conventional temporally induced tTF in this lineage. In our revised interpretation, Kr expression is low and not detectably strongly temporally induced in MBNBs, whereas Kr function is temporally required during pupal MBNB termination, as supported by the Gal80ts knockdown experiments.

      (5) Finally, the contribution of Kr to the neuronal composition of the mushroom body is expected (since Imp is known to regulate neuronal diversity in the MB), but the presentation in the paper is very incomplete.

      We agree that, given the known role of Imp/Syp in MB neuronal temporal identity, altered MB neuronal composition is a plausible consequence of disrupted Kr function. However, we also agree that our study does not directly determine the precise neuronal identities, connectivity or functional properties of the progeny produced by persistent MBNBs. We have therefore revised the manuscript to present this aspect more cautiously.

      In the original manuscript, we had shown that Kr depletion and the KrIf-1 mutation affect MB morphology. In the revised manuscript, we have clarified the presentation of these data and added new analysis of the severe MB defects caused by Kr-h1 overexpression (Fig. 6C). We now describe these phenotypes as changes in MB morphology and lineage progression, rather than as direct evidence for altered neuronal composition.

      In the Discussion, we state that persistent Imp expression in Kr-depleted MBNBs could bias neuronal progeny toward earlier identities or delay their transition to later identities, but we explicitly note that neuronal identity and connectivity were not directly analysed. We also state that future studies will be required to determine whether prolonged MB neurogenesis alters MB circuit function, learning, plasticity or ageing. Thus, we have revised the manuscript to avoid overstating the contribution of Kr to MB neuronal composition.

      Unfortunately, based on the above, I am not convinced that the authors can use this framework to infer anything about adult neurogenesis. Therefore, the impact of this work is limited to the role of Kruppel in regulating Imp, which has already been shown to regulate the extent of neuroblast division, as well as the neuronal types that are born at different temporal windows.

      We understand the reviewer’s concern and have revised the manuscript to avoid implying that our data establish physiological adult neurogenesis in Drosophila. Instead, we now frame the study as identifying mechanisms that normally terminate MBNB proliferation and restrict latent neurogenic potential in the adult brain.

      We respectfully note, however, that the impact of this study is not limited to showing that Kr regulates Imp. First, we identify Kr as a postembryonic regulator required for timely MBNB termination during pupal development. Second, we show that both Kr depletion and the KrIf-1 mutation allow MBNBs to persist beyond their normal termination window and generate neuronal progeny in the adult MB region. Third, we show that Kr promotes not only the Imp-to-Syp transition but also proper E93 expression within the MBNB lineage. Finally, we identify Kr-h1 as a functionally opposing KLF-family factor that represses E93 and can drive tumour-like NB overgrowth when misexpressed. We have revised the manuscript to present these conclusions more clearly and cautiously.

      Reviewer #3 (Public review):

      Summary:

      Drosophila neuroblasts (NBs) serve as a well-established model for studying neural stem cell biology. The intrinsic genetic programs that control their mitotic potential throughout development have been described in remarkable detail, highlighting a series of sequentially expressed transcription factors and RNA-binding proteins that together constitute the temporal patterning system.

      However, the mechanisms that limit the number of NB divisions remain largely unknown in a specific subset of NBs known as mushroom body neuroblasts (MB NBs). Unlike other NBs, which terminate proliferation before or shortly after the onset of metamorphosis, MB NBs continue dividing until the end of metamorphosis, ceasing only just before adulthood.

      In this study, the authors identify the transcription factor Krüppel (Kr), a member of the conserved Krüppel-like family, as temporally regulated in MB NBs. They demonstrate that Kr knockdown during pupal stages maintains expression of the RNA-binding protein Imp and results in prolonged MB NB proliferation into adulthood. Their data suggest that Kr contributes to the timely silencing of Imp during metamorphosis. The authors further identify Kr-h1, a related transcription factor, as a potential antagonist. While Kr-h1 appears dispensable for the timely termination of MBNBs under normal conditions, its overexpression leads to their continued proliferation and tumor-like expansion in adults.

      This work provides the first evidence for a transcription factor-driven temporal regulation mechanism in MB NBs, offering new insight into the control of neural stem cell self-renewal. Given the evolutionary conservation of Krüppel-like factors, this study may have broader implications for the neural stem cell field.

      Strengths:

      (1) The study possibly identifies a new series of temporal transcription factors that are specific for mushroom body neuroblasts.

      (2) The mechanism could be conserved in vertebrates.

      We thank Reviewer #3 for their positive and constructive assessment of our study. We are grateful that the reviewer recognised the significance of identifying Kr as a regulator of mushroom body neuroblast termination, and the potential broader relevance of KLF-family transcription factors to neural stem cell regulation.

      In response to the reviewer’s comments, we have substantially revised the manuscript. In particular, we have added new data on Kr expression in the KrIf-1 mutant background, Kr-h1 expression in MBNBs, and the regulation of E93 by Kr and Kr-h1. We have also incorporated public MBNB-lineage transcriptomic data to place Kr, Kr-h1, E93, Imp and Syp within the known temporal progression of the MB lineage. Finally, we have revised the proposed model to distinguish experimentally supported interactions from open mechanistic questions.

      Weaknesses:

      Some proposed regulatory interactions, particularly between Kr, Kr-h1, and other temporal factors like Imp, Chinmo, and E93, have not been thoroughly investigated, which weakens the support for the proposed model. Additional experimental validation is needed to confirm these relationships and strengthen the mechanistic framework.

      We agree with the reviewer that some regulatory relationships in the original model required further experimental support. In response, we have added new data and revised the model substantially to distinguish experimentally supported interactions from unresolved mechanistic links.

      In the revised manuscript, we provide additional analysis of the Imp/Syp axis after Kr depletion, direct evidence for Kr-h1 expression in MBNBs, and new data showing that Kr-h1 antagonises E93 expression in the MBNB lineage. We also found that Kr depletion reduces E93 expression in the progeny region of the MBNB lineage without significantly increasing Kr-h1::GFP levels in MBNBs, arguing against a simple linear pathway in which Kr promotes termination by directly repressing Kr-h1. Together, these results support a revised model in which Kr promotes MBNB termination by facilitating the Imp-to-Syp transition and supporting E93 expression, whereas Kr-h1 functionally opposes termination at least in part through E93 repression.

      Recommendations for the authors:

      Reviewing Editor Comments:

      The majority of the reviewers agreed that a few major important points should be addressed, in particular:

      (1) Better characterization of the nature of the KrIf-1 allele.

      (2) Better define the regulations and interactions between Kr, Kr-h1, Imp, Syp, chinmo, and E93.

      (3) More information about the genetic screen performed.

      (4) The timings of expression of Kr in pupal MBNBs and of KrIf-1.

      The reviewers also found that a general proofreading of the manuscript would greatly benefit its readability and comprehension and suggested several small corrections and more detailed explanations.

      We thank the Reviewing Editor and Senior Editor for their careful assessment of our manuscript and for summarising the major points that required revision. We have addressed these points as follows.

      (1) Better characterisation of the nature of the KrIf-1 allele

      We agree that clarifying the nature of the KrIf-1 allele was important. We have now examined Kr expression in KrIf-1 mutant brains using TSA-enhanced Kr immunostaining. These new data show ectopic Kr signal in MBNBs and their progeny in KrIf-1 mutant late pupal and adult brains (Fig. S3G–I), supporting the conclusion that the KrIf-1 phenotype is associated with Kr misexpression rather than simple loss of Kr expression. We have revised the Results and Discussion to explain that MBNB termination requires precise control of Kr activity, and that both Kr depletion and inappropriate Kr expression can disrupt this termination programme.

      (2) Better definition of the regulatory relationships between Kr, Kr-h1, Imp, Syp, Chinmo and E93

      We have strengthened this part of the manuscript by combining the genetic evidence already present in the original manuscript with new expression analyses of temporal and hormone-responsive regulators. The original manuscript already showed that co-depletion of Imp suppresses MBNB retention caused by Kr depletion, supporting Imp as a key downstream effector of Kr. In the revised manuscript, we further show that Kr depletion causes persistent Imp expression and reduced Syp expression in late pupal MBNBs (Fig. 4), supporting the conclusion that Kr promotes MBNB termination by facilitating the Imp-to-Syp transition.

      We have also added new data on Kr-h1 and E93. Kr-h1 depletion increases E93 expression in the MBNB lineage, whereas Kr-h1 overexpression reduces E93 expression (Fig. S5B), supporting an antagonistic relationship between Kr-h1 and E93 in this lineage. In addition, Kr depletion reduces E93 expression in the surrounding progeny of the MBNB lineage without detectably increasing Kr-h1::GFP levels in late pupal MBNBs (Fig. 5B). These data argue against a simple linear Kr-Kr-h1-E93 pathway and instead support a model in which Kr and Kr-h1 function through convergent or parallel mechanisms to regulate MBNB termination.

      Regarding Chinmo, we agree that it is an important temporal factor. However, Chinmo is best characterised in this context as an early temporal fate regulator acting downstream of the Imp/Syp programme in MB lineages, where Imp and Syp regulate Chinmo translation post-transcriptionally (Liu et al., 2015). Because our study focuses primarily on late pupal MBNB termination, and because we were unable to obtain reliable Chinmo antibodies or reporter lines within the timeframe of this revision, we did not directly analyse Chinmo expression. We have therefore removed Chinmo from the main model and revised the Discussion to focus on the experimentally supported Imp/Syp and Kr-h1/E93 axes.

      (3) More information about the genetic screen

      We agree that the original screen-based description was not sufficiently informative. Because the targeted screen was preliminary and incomplete, we have removed the screen-based framing from the revised manuscript. Instead, we now present Kr as a candidate selected for focused functional analysis based on its known role in neuroblast temporal regulation and the strong MBNB retention phenotype observed upon Kr depletion and in the KrIf-1 mutant background.

      (4) Timing of Kr expression in pupal MBNBs and in KrIf-1

      We have clarified the timing of Kr expression in MBNBs. In wild-type brains, weak Kr signals were detected in MBNBs during pupal development using two Kr antibodies and a Kr::GFP BAC reporter, and these signals were reduced by Kr RNAi (Fig. 3E, F and Fig. S3F). We also analysed MBNB-lineage RNA-seq data, which show relatively low but persistent Kr transcript levels during postembryonic development (Fig. S5A). In the KrIf-1 background, TSA-enhanced Kr staining revealed ectopic Kr expression in MBNBs and their progeny during late pupal and adult stages (Fig. S3G–I). We have revised the manuscript to describe these expression patterns more clearly and to avoid overinterpreting weak embryonic or larval Kr signals.

      We have also proofread the manuscript, corrected typographical errors, standardised figure references and nomenclature, improved figure legends and revised several figures for clarity.

      Reviewer #1 (Recommendations for the authors):

      (1) The authors identified Kr from a targeted genetic screen. Information about how many factors and what factors they have screened will also be very helpful to readers.

      We thank the reviewer for this suggestion. In the original manuscript, we briefly referred to a targeted genetic screen that led us to focus on Kr. However, because this screen was preliminary and incomplete, we agree that including partial screening information would not be sufficiently informative and might overstate the scope of the present study. We have therefore revised the manuscript to remove the screen-based framing and instead present Kr as a candidate selected for focused functional analysis based on its known role in neuroblast temporal regulation and the strong MBNB retention phenotype observed upon Kr depletion and in the KrIf-1 mutant background.

      (2) In Figure 2C wild type brains, what are the Mira+ cells and insc>GFP+ cells? There seems to be one cell that expresses both. Could it be a dormant NB?

      We thank the reviewer for pointing this out. We agree that a small number of weakly Mira-positive and insc>GFP-positive cells can occasionally be observed in adult control brains, as well as in KrIf-1 mutant brains. These cells were few in number, were generally located outside the stereotyped MBNB region, and showed much weaker marker signals than the retained MBNBs observed after Kr depletion or in KrIf-1 mutants. Because they did not appear to express other NB markers examined in this study, such as wor>GFP, we did not investigate them further. Their identity therefore remains unclear, and we cannot exclude the possibility that they represent rare dormant or NB-like cells in the adult brain.

      We have revised the text and figure legend to clarify that the retained MBNBs analysed in this study were identified based on their stereotyped MB-region position and strong NB-marker expression.

      (3) Kr is normally expressed in stage 10 embryonic NBs. Have stage 10 embryos been examined to make sure that there is no Kr expression in MBNBs?

      We thank the reviewer for this important point. We agree that Kr expression in early embryonic neuroblasts is well established. Early embryonic MBNBs can in principle be identified using a detailed positional and combinatorial marker map, as shown by Kunz et al. (2012), who traced individual MBNBs from late embryonic stages back to stage 9 using combinations of Dac, Ey, Svp-lacZ and Rx, together with morphological and positional criteria. However, reliable identification of MBNBs at such early stages is technically challenging in our assay, because our analysis depended on simultaneous detection of OK107>GFP, Mira and Kr, and OK107>GFP/Mira-based identification of the MB lineage was more robust at later embryonic stages. We therefore focused our embryonic Kr analysis on stages at which MBNBs could be confidently identified by their position and marker expression.

      In these embryos, Kr was broadly detected in surrounding embryonic CNS cells, including thoracic NBs, but was not robustly detected in OK107>GFP- and Mira-positive MBNBs (Fig. S3A, B). We cannot fully exclude the possibility that MBNBs transiently express very low levels of Kr at earlier embryonic stages before they can be reliably identified in our assay. However, our temporally controlled Gal80ts experiments show that Kr depletion during the pupal stage, but not during earlier embryonic or larval stages, is sufficient to cause MBNB retention in adult brains (Fig. 3C, D). Thus, any transient embryonic Kr expression, if present, is unlikely to be the main cause of the adult MBNB retention phenotype described here.

      We have revised the text to avoid overinterpreting the absence of embryonic Kr expression and to emphasise that the critical requirement for Kr in this study occurs during pupal MBNB termination.

      (4) In Figure S3C, Kr expression seems to be cytoplasmic. Also in S3D, the expression of KrGFP in NBs is not obvious. Overall, Kr expression in pupal MBNBs is much more convincing than the larval expression.

      We agree with the reviewer. Kr expression in larval MBNBs is weak and less convincing than the pupal signal. We have therefore revised the manuscript to describe larval Kr expression more cautiously. In the revised text, we state that Kr was weakly detected in larval MBNBs by antibody staining and that the Kr::GFP BAC reporter showed stronger signals in cells adjacent to MBNBs, likely corresponding to GMCs or immature neurons that may have inherited Kr::GFP from MBNBs.

      We now base our main conclusion primarily on the pupal-stage data. At this stage, weak Kr signals were detected in MBNBs using two independent Kr antibodies and the Kr::GFP BAC reporter, and Kr depletion reduced the antibody signal (Fig. 3E, F and Fig. S3F). Importantly, this expression pattern is consistent with our functional data showing that pupal-stage-specific Kr depletion is sufficient to induce MBNB retention in adult brains, whereas earlier embryonic or larval depletion did not produce the same phenotype (Fig. 3C, D). Thus, both the expression and temporal knockdown data support a critical role for Kr during pupal MBNB termination.

      We also discuss the observation that Kr signals in pupal MBNBs appear partly cytoplasmic, raising the possibility that Kr may not act solely as a canonical nuclear transcription factor in this context, or that its localisation may be dynamically regulated during MBNB termination. Thus, we agree that the pupal expression data provide the strongest support for Kr expression in MBNBs, and we have revised the text accordingly.

      (5) A thorough proofreading is needed to correct the typos.

      We apologise for the typographical and formatting errors in the original manuscript. We have thoroughly proofread the revised manuscript, corrected typographical errors, standardised figure references and gene/protein nomenclature, and revised multiple sections for clarity and readability. We have also revised the figure legends and improved figure presentation where possible.

      Reviewer #2 (Recommendations for the authors):

      (1) The authors should proofread for typos; there are quite a few ("survivial", "fount", "mitoic", "persistenc").

      We apologise for these typographical errors. We have thoroughly proofread the revised manuscript, corrected typographical errors and formatting problems, and revised multiple sections for clarity and readability.

      (2) In line 59, "adult eclosion" is incorrect. MBNBs also cease dividing before adult eclosion.

      We thank the reviewer for pointing this out. We have revised the wording to avoid the incorrect phrase “adult eclosion” and now state that MBNBs normally terminate during late pupal development, before adulthood.

      (3) In line 70, this progression of transcription factors is seen in the mammalian retina, not the brain.

      We thank the reviewer for this correction. We have revised the relevant sentence to more accurately describe temporal patterning in mammalian neural progenitors, including the well-characterised example of retinal progenitor temporal progression and broader examples of temporal competence changes in cortical development.

      (4) In lines 73-75, I don't think that any of the cited papers show that Cas triggers cell cycle exit. Ref 11 shows that, in UAS-Cas, NBs persist (as the authors also say in lines 79-81).

      We agree that the original wording was too strong and potentially misleading. We have revised this section to state more generally that temporal transcription factors can influence NB proliferation and NB lifespan, rather than claiming that Cas directly triggers cell-cycle exit. We have also adjusted the discussion of Cas and Svp to better reflect the cited literature.

      (5) In lines 133-134, it should be Figure 2A, B instead of Figure 3A, B.

      We thank the reviewer for identifying this error. We have corrected the figure reference.

      (6) Figures 1B and 1C are impossible to read. The x-axis should be reorganized and grouped into positive and negative CCRs to make a better argument. Moreover, the purpose of this figure is unclear. We already knew that neurons are postmitotic and all adult clusters are neurons. IF there were any NBs in the adult, they would be so few that they would be invisible with this resolution.

      We thank the reviewer for this comment. We agree that the dot plots are dense, because they summarise the expression of 112 selected cell-cycle regulator (CCR) genes across multiple adult and larval brain cell clusters. In preparing the revised manuscript, we have ensured that the figure legends explain the meaning of colour intensity and dot size, and that the submitted PDF preserves sufficient resolution for the gene and cluster labels to be read upon enlargement.

      In the original figures, CCR genes were arranged according to broad functional categories. We have not forced all CCR genes into a simple positive-versus-negative classification, because the function of many CCRs is context-dependent. For example, APC/C components can contribute to either mitotic progression or G1 maintenance depending on co-activator context, and mitotic regulators such as Polo and Aurora kinases regulate multiple aspects of mitosis rather than acting simply as positive cell-cycle drivers. We therefore present the genes according to broad functional categories and discuss representative examples of positive and inhibitory regulators in the Results and figure legends, rather than implying that every CCR can be assigned unambiguously to one of two categories.

      Regarding the purpose of these analyses, our aim was not simply to restate that adult neurons are postmitotic, nor to claim that scRNA-seq can definitively exclude extremely rare adult progenitors. Rather, we used published scRNA-seq datasets to compare CCR expression programmes across adult and larval brain cell populations in an unbiased manner. The analysis shows that no adult brain cluster displays a coordinated larval NB-like positive CCR expression programme, whereas such a programme is readily observed in larval NB clusters. We have clarified this point in the text and acknowledge the limitation that very rare or non-canonical progenitor-like cells may not be detected by this approach.

      (7) The survival assays are confusing. Do the authors believe that the presence or absence of 2-3 clones in the adult brain of a few cells would lead to such a limited survival?

      We thank the reviewer for raising this point. We agree that the survival assay required clearer explanation and should be interpreted cautiously. In this experiment, E2F1-Dp and Cdk2-CycE were expressed using TH-Gal4 to test whether forced activation of positive cell-cycle regulators can drive postmitotic neurons into aberrant cell-cycle re-entry. Although only a small number of pH3-positive cells may be detected at any single time point, this represents only a snapshot of an ongoing process and may underestimate the cumulative number of affected cells over time.

      TH-Gal4-positive dopaminergic neurons are relatively limited in number, but they include functionally important neuronal populations involved in motor behaviour, arousal, sleep/wake regulation and ageing-associated behavioural decline. Therefore, broad induction of aberrant cell-cycle re-entry and apoptosis within these neurons could plausibly affect organismal survival. However, we agree that the survival phenotype should not be overinterpreted. We cannot exclude the possibility that TH-Gal4 expression outside dopaminergic neurons, developmental effects of the manipulation, or other indirect consequences contribute to the reduced survival. Moreover, the precise cause of death was not determined in this study. We have therefore revised the manuscript to present the survival assay as supporting evidence that inappropriate activation of positive cell-cycle regulators is deleterious in postmitotic neurons, rather than as a direct mechanistic explanation for organismal lethality.

      (8) In Figure 2, how many of the proliferative clones are found in the mushroom body. Is it all of them?

      We thank the reviewer for this question. In Fig. 2, EdU-positive proliferative clones were scored based on their stereotyped position in the dorsoposterior MB cell body region. Under the conditions analysed, the scored clones were consistently detected within this MB region, and their number did not exceed four per brain hemisphere, consistent with the expected number of MBNBs (Fig. 2A, B). In addition, the identity of these clones as retained MBNB lineages was supported by NB marker expression, Mira localisation, insc>GFP expression where applicable, and their association with MB lineage markers such as mb247>GFP and OK107>GFP in KrIf-1 mutant brains (Fig. 2C-H). We have clarified this point in the revised text and figure legend.

      (9) In Figure 2C, why are there so many Miranda-positive cells?

      We thank the reviewer for this question. We agree that several Mira-positive cells can be observed in Fig. 2C, including in control brains. The identity of these additional Mira-positive cells remains unclear. They did not consistently co-express the canonical NB markers examined in this study, such as insc>GFP or wor>GFP, and therefore do not appear to represent canonical proliferative NBs. However, we cannot exclude the possibility that some weak Mira-positive cells represent rare dormant or NB-like cells in the adult brain. We have revised the text and figure legend to clarify this point.

      (10) In Figure 3C, the authors argue that Kr has an opposing function in NB regulation during larval stages, however, the Kr mutant (which is in both larval and pupal stages) has the highest number of EdU-positive clones. Moreover, conditions 2 and 9 have a comparable (low) number of EdU positive clones, although condition 2 has Kruppel downregulated in all stages.

      We thank the reviewer for this comment. We agree that this part of the temporal knockdown experiment required more careful interpretation, and we have revised the manuscript to avoid overinterpreting small quantitative differences among individual temperature-shift conditions.

      First, Fig. 3C does not include a Kr mutant condition. We assume that the reviewer is referring to the constitutive insc>KrIR condition grown at 29°C throughout development (condition 1). This condition does not contain tub-Gal80ts and may therefore produce stronger and more continuous Kr RNAi induction than the Gal80ts-based temporal knockdown conditions. In addition, for practical reasons, flies in all conditions were initially kept at 25°C during egg laying to obtain sufficient embryos before being shifted to the indicated temperature regime, including condition 2. These differences may explain why condition 1 produced the highest number of EdU-positive clones. For this reason, we do not interpret condition 1 as a temporal-control condition and do not use it for direct quantitative comparison with the Gal80ts-based conditions.

      Second, regarding the comparison between conditions 2 and 9, we agree that these conditions should not be used to infer a simple relationship between the total duration of Kr knockdown and the number of retained MBNBs. We therefore avoid using these differences to infer an additional larval function of Kr. Instead, we now interpret this temporal knockdown experiment more conservatively: Kr depletion during the pupal period is sufficient to induce MBNB retention in adult brains, whereas depletion restricted to earlier embryonic/larval stages or later adult stages has little or no effect.

      Thus, the key conclusion supported by these data is the pupal-stage requirement for Kr in MBNB termination, rather than detailed comparisons among all temperature-shift conditions. We have revised the text accordingly.

      Overall, we have revised the manuscript to address the reviewer’s concerns by narrowing the framing of adult neurogenesis, clarifying the distinction between persistent MBNBs and tumour-like overgrowth, improving figure presentation, removing the incomplete screen description, adding public dataset analysis, and correcting textual and citation errors. We believe these revisions make the scope and conclusions of the study more precise.

      Reviewer #3 (Recommendations for the authors):

      Major Points

      (1) Targeted screen: The authors mention performing a targeted genetic screen. Please specify which transcription factors were tested.

      We thank the reviewer for this suggestion. In the original manuscript, we briefly referred to a targeted genetic screen. However, this screen was preliminary, incomplete, and included a broader set of candidate regulators rather than a systematically completed transcription-factor collection. We therefore agree that listing a partial set of tested factors would not be sufficiently informative and could overstate the scope of the present study.

      We have therefore removed the screen-based framing from the revised manuscript. Instead, the revised manuscript presents Kr as a candidate selected for focused functional analysis based on its established role in neuroblast temporal patterning and the strong MBNB retention phenotype observed upon Kr depletion and in the KrIf-1 mutant background. We also no longer use the preliminary screen as part of the evidence supporting our conclusions.

      (2) KrIf-1 allele : The authors report that KrIf-1 mutants retain MB NBs in adults, a phenotype resembling Kr loss of function. They propose that this results from Kr deregulation. However, KrIf-1 is a neomorphic allele known to cause ectopic expression in imaginal discs, raising the possibility that Kr is upregulated, not downregulated, in MB NBs. The authors should present experimental data on Kr expression in MB NBs in the KrIf-1 background to clarify this point.

      We agree that clarification of Kr expression in the KrIf-1 background is important. We have therefore performed additional Kr immunostaining in KrIf-1 mutant brains using tyramide signal amplification (TSA) to enhance the weak endogenous Kr signal. These new data show that Kr is ectopically detected in MBNBs and their progeny in KrIf-1 mutant late pupal and adult brains (Fig. S3G, H), and quantification of TSA-enhanced Kr signals further supports Kr misexpression in MBNBs during late pupal stages (Fig. S3I).

      These results indicate that KrIf-1 is associated with ectopic or aberrant Kr expression in MBNBs, rather than simple loss or downregulation of Kr expression. We have revised the manuscript to clarify this point and no longer interpret KrIf-1 as a simple Kr loss-of-function condition. Although both Kr depletion and KrIf-1 lead to MBNB retention, our revised interpretation is that MBNB termination requires precise temporal and spatial control of Kr activity. Kr depletion disrupts the normal Imp-to-Syp transition and reduces E93 expression in the MBNB lineage, whereas ectopic or mistimed Kr expression in KrIf-1 mutants may also interfere with the termination programme. Thus, both reduced Kr activity and inappropriate Kr expression can perturb the tightly regulated transition required for timely MBNB cell-cycle exit and elimination.

      (3) Line 258 - OK107>GFP subset (Fig. 2G): Please clarify why only a subset of EdU-positive clones co-express OK107>GFP. Is this due to EdU labeling other NB lineages not related to the mushroom body?

      We thank the reviewer for raising this point. We do not think that the OK107-negative EdU-positive clones represent unrelated NB lineages. The EdU-positive clones analysed in Fig. 2G were located in the dorsoposterior MB cell body region and were associated with Mira-positive NB-like cells, supporting their identification as persistent MBNB-lineage clones.

      The reason that only a subset of EdU-positive clones clearly co-express OK107>GFP is likely that, while OK107-Gal4 strongly labels MB neurons and lineage cells, its activity in MBNBs and very young progeny appears to be weaker or more variable at the stages analysed. Thus, the absence of strong OK107>GFP signal in some EdU-positive cells does not necessarily indicate that these clones belong to non-MB lineages.

      We have revised the text and figure legend to clarify this point.

      (4) Line 261 - Early adulthood mitotic activity: The statement that NBs retain mitotic activity during early adulthood (citing Technau, 2007; Li and Hidalgo, 2020) is misleading. To my knowledge, this mitotic activity has only been reported in glial cells, not NBs. Please revise accordingly.

      We thank the reviewer for pointing this out. We agree that the original wording was misleading, because it could be read as implying that normal NBs retain mitotic activity during early adulthood. We have revised the text accordingly. The revised manuscript now refers more cautiously to the previously described early-adult period during which rare residual cell-cycle or proliferative activity has been reported in the adult Drosophila brain, without attributing this activity to normal persistent NBs.

      (5) Line 313 - Public dataset analysis: The manuscript mentions analysis of publicly available data, but no results are presented. Please include these findings.

      We agree and have now included the public dataset analysis in the revised manuscript. We analysed a published MBNB-lineage-specific RNA-seq dataset and present the expression profiles of selected temporal regulators in Fig. S5A.

      This analysis shows that Imp and chinmo transcripts are high during larval stages and decrease during pupal development, whereas Syp is strongly upregulated during the same period. Kr transcript levels remain relatively low throughout the analysed larval and pupal stages and do not show strong temporal induction. In contrast, Kr-h1 is highly expressed during larval stages and sharply downregulated after the larval-to-pupal transition, whereas E93 is strongly induced during pupal development.

      These expression profiles support the idea that MBNBs undergo a major temporal transition during pupal development, including the Imp/Syp transition and reciprocal changes in Kr-h1 and E93 expression. They are also consistent with our experimental finding that Kr-h1 antagonises E93 expression in the MBNB lineage. We have added this analysis to the Results and incorporated it into the revised model.

      (6) Figure 3A - Kr localization: Kr is detected predominantly in the cytoplasm, which contrasts with its function as a transcription factor. Is cytoplasmic localization typical for Kr? Please discuss.

      We thank the reviewer for this important observation. We agree that the weak Kr signal in pupal MBNBs appears partly enriched in the cytoplasm, which is unexpected for a canonical nuclear transcription factor. We have revised the Discussion to address this point.

      Because this signal was reduced upon Kr RNAi, we think that it is likely to represent a Kr-dependent signal rather than nonspecific background. However, we do not yet know whether the apparent cytoplasmic enrichment reflects dynamic regulation of Kr localisation, a non-canonical aspect of Kr function in postembryonic MBNBs, or technical limitations associated with detecting very low endogenous Kr levels. We therefore avoid overinterpreting the cytoplasmic signal, but note that Kr localisation and activity in pupal MBNBs may be more complex than expected for a canonical nuclear transcription factor. Future studies will be required to determine how Kr activity and localisation are regulated in pupal MBNBs.

      (7) Temporal Kr knockdown experiment: The result that Kr knockdown during pupal stages - but not earlier - leads to MB NB persistence is interesting but counterintuitive. Given the limitations of RNAi (e.g., leaky expression, incomplete knockdown), MARCM clones for Kr mutants would provide stronger evidence and improve confidence in this conclusion.

      We agree that MARCM analysis of Kr mutant MBNB clones would provide a valuable independent test of the temporal RNAi results. We attempted to establish this approach during revision, but it proved technically difficult within the available timeframe.

      A major practical limitation is that MBNBs are very few in number, with only four per brain hemisphere. Conventional MARCM or flip-out approaches therefore generate stochastic clones that are inefficient for reliably recovering and analysing MBNB clones. We also explored the possibility of using MB-lineage MARCM reagents reported in a previous study (Rossi & Desplan, 2020), but the available stocks were not directly compatible with the FRT chromosome required for our Kr mutant analysis. Generating the necessary compatible stocks and recovering sufficient MBNB clones would require substantial additional crossing and screening.

      For this reason, we were not able to include Kr mutant MARCM data in the revised manuscript. Instead, we base our conclusion on several complementary lines of evidence, including temporal Gal80ts-based Kr RNAi, two independent Kr RNAi lines, the reduction of Kr signal upon Kr RNAi newly added in this revision, and the independent KrIf-1 phenotype, which supports the idea that precise regulation of Kr activity is required for MBNB termination.

      (8) OK107-GAL4 activity: Please indicate early in the manuscript that OK107-GAL4 is not active in MB NBs but is active in their progeny. This would clarify the rationale for using the pan-NB driver insc-GAL4 for manipulating MB NBs.

      We thank the reviewer for this suggestion. We have revised the manuscript to clarify the use of OK107-Gal4 and insc-Gal4 earlier in the Results and in the relevant figure legends.

      Although OK107-Gal4 activity is not completely absent from MBNBs, its activity in MBNBs is stage-dependent and weaker or more variable than in MB neurons and their progeny. We therefore used OK107-Gal4 mainly to visualise MB structures and MB lineage regions, whereas insc-Gal4 was used for robust NB-specific manipulation. This clarification should help explain why insc-Gal4, rather than OK107-Gal4, was used for MBNB-targeted knockdown experiments.

      (9) Figure 5A - Mira+ cell numbers: There appears to be an excess of Mira+ cells compared to the expected number of MB NBs. Please explain this observation.

      We thank the reviewer for pointing this out. In Fig. 5A, we quantified the number of EdU-positive clones, not the total number of Mira-positive cells. As shown in Fig. 2, proliferative cells retained in Kr-depleted or KrIf-1 mutant adult brains were identified as persistent MBNBs based on combined criteria, including EdU incorporation, NB marker expression such as Mira and insc>GFP, NB-like morphology, and stereotyped location in the dorsoposterior MB region.

      We agree that additional Mira-positive cells can be observed in adult brains, including in control and Kr-depleted brains. However, these cells were not associated with EdU-positive proliferative clones and did not consistently express canonical NB markers examined in this study. Their identity therefore remains unclear, and they were not scored as retained MBNBs.

      (10) Line 430 - Kr-h1 over-expression phenotype: The amplification phenotype caused by Kr-h1 overexpression is reminiscent of that caused by chinmo overexpression (Narbonne-Reveau et al., 2016), suggesting that Kr-h1 may promote chinmo and Imp expression. Also, what is the expression pattern of Kr in the supernumerary adult MB NBs following Kr-h1 overexpression? Is Kr silenced? Investigating this would help clarify the regulatory links between Kr, Kr-h1, and Imp/chinmo.

      We agree that the Kr-h1 overexpression phenotype is reminiscent of NB amplification phenotypes associated with forced or aberrant activation of early temporal growth programmes, including those linked to Chinmo. Narbonne-Reveau et al. showed that Chinmo can promote NB amplification and tumour growth, and that Chinmo, Imp and Lin-28 form a growth-promoting module in neural tumours. Consistent with this idea, our revised manuscript shows that Kr-h1 overexpression causes extensive tumour-like NB overgrowth, impaired neuronal differentiation and persistent Imp expression (Fig. 5C–E).

      Although we did not analyse Chinmo expression in this revision, we did examine Imp expression following Kr-h1 overexpression and found persistent Imp expression in tumour-like NB cells (Fig. 5E). These data are consistent with the idea that excessive Kr-h1 activity can reinforce a progenitor-like state. However, we have interpreted this result cautiously, because Kr-h1 overexpression produces a severe tumour-like phenotype with impaired asymmetric division and neuronal differentiation. Thus, persistent Imp expression in this context could reflect either a more direct effect of Kr-h1 on early temporal programmes or an indirect consequence of the strongly perturbed progenitor-like state.

      We also did not directly analyse Kr expression in supernumerary NB-like cells following Kr-h1 overexpression. This is an interesting question, but the severe tissue disruption caused by Kr-h1 overexpression would make it difficult to distinguish a physiological regulatory effect on Kr from an indirect consequence of tumour-like overgrowth. In addition, endogenous Kr signals in MBNBs are weak, making it technically challenging to reliably quantify changes in Kr expression in this strongly perturbed condition.

      We have therefore revised the Discussion to clarify that the Kr-h1 overexpression phenotype should be interpreted mainly as evidence that excessive Kr-h1 activity can oppose MBNB termination and maintain Imp-positive progenitor-like cells, rather than as evidence for a defined normal regulatory pathway from Kr-h1 to Chinmo, Imp or Kr. In parallel, our revised loss-of-function and expression analyses show that Kr depletion causes persistent Imp and reduced Syp expression, that Kr supports E93 expression in the MBNB lineage (Fig. 5B), and that Kr-h1 antagonises E93 expression (Fig. S5B). Because Kr depletion did not significantly increase Kr-h1::GFP expression (Fig. 5B), we no longer present a simple linear model in which Kr promotes MBNB termination by repressing Kr-h1 expression.

      (11) Kr-h1 expression in MB NBs: Please provide direct evidence that Kr-h1 is expressed in MB NBs during development.

      We agree that direct evidence for Kr-h1 expression in MBNBs is important. We have therefore analysed Kr-h1 expression using a functional Kr-h1::GFP BAC reporter. Kr-h1::GFP was clearly detected in MBNBs during third-instar larval stages, with nuclear enrichment, but became barely detectable in late pupal MBNBs (Fig. 5B and Fig. S5C).

      This developmental downregulation is consistent with the published MBNB-lineage RNA-seq dataset, which shows high Kr-h1 transcript levels during larval stages and strong reduction after the larval-to-pupal transition (Fig. S5A). Together, these data provide direct evidence that Kr-h1 is expressed in MBNBs during development and is downregulated before MBNB termination.

      (12) Figure 6D - Model validation: The model in Figure 6D is appealing, but many of the proposed interactions remain untested. For example:

      - It is not established that Kr-h1 antagonizes E93 or vice versa in MB NBs.

      - The antagonistic relationship between Kr and Kr-h1 has not been experimentally confirmed.

      - The temporal expression of Kr-h1 in MB NBs is unknown.

      - The repression of E93 by Kr-h1 is unlikely to fully explain the MB NB amplification phenotype.

      We thank the reviewer for this helpful critique. We have substantially revised Fig. 6D and the accompanying text to distinguish experimentally supported interactions from unresolved regulatory links.

      First, we have now tested the relationship between Kr-h1 and E93 in the MBNB lineage. Kr-h1 depletion increased E93 expression, whereas Kr-h1 overexpression reduced E93 expression (Fig. S5B), supporting the conclusion that Kr-h1 antagonises E93 expression in this lineage. Reciprocal antagonism between Kr-h1 and E93 has been reported in other insect developmental contexts. However, because we did not directly test whether E93 represses Kr-h1 in MBNBs, we now present this possible E93-to-Kr-h1 regulation as an unresolved or putative interaction rather than as an experimentally established relationship in our system.

      Second, we have clarified the relationship between Kr and Kr-h1. Our genetic data show that Kr-h1 knockdown partially suppresses MBNB retention caused by Kr depletion (Fig. 5A), indicating that Kr and Kr-h1 have opposing functions during MBNB termination. However, although Kr depletion reduced E93 expression in the MBNB lineage, it did not detectably increase Kr-h1::GFP levels in late pupal MBNBs (Fig. 5B). We therefore no longer present Kr as a direct upstream repressor of Kr-h1. Instead, the revised model proposes that Kr promotes MBNB termination by supporting the Imp-to-Syp transition and E93 expression, whereas Kr-h1 opposes termination at least in part by repressing E93.

      Third, we now provide direct evidence for Kr-h1 expression in MBNBs using a functional Kr-h1::GFP BAC reporter. Kr-h1::GFP was detected in larval MBNBs and became strongly reduced during pupal development (Fig. 5B and Fig. S5C). This temporal pattern is also consistent with the published MBNB-lineage RNA-seq dataset, which shows high Kr-h1 transcript levels during larval stages and downregulation after the larval-to-pupal transition (Fig. S5A).

      Finally, we agree that repression of E93 by Kr-h1 is unlikely to fully explain the strong tumour-like NB overgrowth caused by Kr-h1 overexpression. In the revised manuscript, we show that supernumerary tumour-like NB cells induced by Kr-h1 overexpression retain high Imp expression (Fig. 5E). This suggests that excessive Kr-h1 activity can oppose MBNB termination and maintain an Imp-positive progenitor-like state.

      However, we interpret the Kr-h1 overexpression phenotype cautiously, because this strong gain-of-function condition causes severe tumour-like overgrowth and may not accurately reflect the physiological regulatory relationship between Kr-h1 and the normal MBNB termination programme. We have therefore revised the Discussion to state that Chinmo, an early temporal factor linked to the Imp/Syp programme, may be relevant to the persistent progenitor-like state observed after Kr depletion or Kr-h1 overexpression. However, because we did not directly analyse Chinmo expression in this study, we do not include Chinmo in the main model and leave this question for future work.

      Minor Points

      (1) OK107-GAL4 activity: Please check and indicate early on in the manuscript that OK107-GAL4 is not active in MB NBs (although being active in their progeny). It would clarify why the authors keep using the pan NB insc-GAL4 to manipulate MB NBs.

      As described in our response to Major Point 8, we have clarified earlier in the Results that OK107-Gal4 strongly labels MB neurons and the MB lineage, but is not a robust or consistent driver in MBNBs at the stages relevant to our functional assays. We therefore used OK107-Gal4 primarily for visualising MB structures and MB lineage regions, whereas insc-Gal4 was used for robust NB-specific manipulation.

      (2) CCR list: Please clarify how the list of candidate cell cycle regulators (CCRs) was compiled.

      We have revised the Materials and Methods to clarify how the list of candidate cell-cycle regulators was compiled. Briefly, the CCR list was manually curated to include core cell-cycle regulators, cyclins and CDKs, DNA replication factors, checkpoint regulators, mitotic regulators, APC/C and ubiquitin-proteasome components, and non-canonical CDKs with known roles in transcriptional regulation.

      (3) Line 77-78 - Cas and Svp: The statement that Cas and Svp regulate neurogenesis termination by directly regulating cell cycle regulators needs references. As far as I know, the direct targets of Cas and Svp remain unidentified.

      We agree that the original wording was too strong. We have revised the text to state more generally that temporal transcription factors, including Cas and Svp, influence NB proliferation and lifespan, without implying that they directly regulate known cell-cycle target genes.

      (4) Line 410: Please add references to support this statement.

      We have added the appropriate reference to the original genetic modifier screen by Abrell et al., 2000, in which Kr-h1 mutations were identified as enhancers of the KrIf-1 eye phenotype. We have also revised the wording to state that this finding suggests a functional interaction between Kr and Kr-h1, rather than using it alone as evidence for a direct regulatory relationship.

      (5) Typos and minor edits:

      - Line 38: "capable" (spelling)

      - Line 102: Replace "unexplored" with "explored"

      - Line 106: "potential" (spelling)

      - Line 243: "mitotic" (spelling)

      - Line 260: "KrIf-1" (correct gene formatting)

      We have corrected the typographical errors and formatting issues indicated by the reviewer, including spelling errors and KrIf-1 gene formatting. We have also proofread the manuscript throughout.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      The study is technically extensive and employs a wide range of experimental approaches, including in vivo analyses, cell-based assays, and transcriptomic data integration. The authors provide a detailed characterization of inflammatory and stress-related pathways activated following IMQ exposure in mouse skin. These datasets may be informative for researchers specifically interested in IMQ-induced dermatitis or in stress responses triggered by chemical skin irritants.

      We sincerely thank the reviewer for this positive assessment of our study. We appreciate the recognition of the breadth of our experimental approaches, including the integration of in vivo analyses, cell-based experiments, and transcriptomic analyses, as well as the acknowledgement that our findings provide useful insights into IMQ-induced dermatitis and stress responses triggered by chemical skin irritants. We have carefully considered the reviewer's comments and have substantially revised the manuscript to address the concerns regarding the interpretation and disease relevance of our findings. Detailed responses to the specific points raised are provided below.

      Strengths:

      The study is technically extensive and employs a wide range of experimental approaches, including in vivo analyses, cell-based assays, and transcriptomic data integration. The authors provide a detailed characterization of inflammatory and stress-related pathways activated following IMQ exposure in mouse skin. These datasets may be informative for researchers specifically interested in IMQ-induced dermatitis or in stress responses triggered by chemical skin irritants.

      We sincerely thank the reviewer for this positive assessment and for recognizing the breadth of our experimental approaches and the potential value of our findings for researchers studying IMQ-induced dermatitis and stress responses.

      Weaknesses:

      A major limitation of the manuscript is its exclusive reliance on the IMQ model, which does not adequately represent the immunological drivers, cellular interactions, or therapeutic responsiveness of human psoriasis, despite the manuscript's framing. IMQ-induced inflammation is dominated by innate immune activation and mouse-specific pathways, whereas human psoriasis is driven primarily by IL-23/IL-17-mediated interactions between keratinocytes and Th17/Tc17 cells. As a result, conclusions drawn entirely from IMQ-based experiments have limited relevance to human disease biology.

      Consistent with this issue, the manuscript places strong emphasis on pathways such as TLR signaling, inflammasome activation, and IL-1-associated responses, none of which are established as central drivers of plaque psoriasis in patients. Therapeutic strategies targeting these pathways have failed to achieve clinical efficacy comparable to IL-23 or IL-17 blockade, yet this translational gap is not adequately addressed.

      The in vitro keratinocyte experiments further limit interpretability. Stimulation of keratinocytes with IMQ is not an accepted model of psoriasis-relevant keratinocyte activation, and the study does not demonstrate induction of well-established psoriasis signature gene programs. Without this validation, it is difficult to assess the relevance of the observed cellular stress responses to human disease.

      The RNA-sequencing analyses raise additional concerns regarding rationale and interpretation. The basis for selecting specific mouse and human datasets is unclear, including the use of unpublished or non-psoriasis inflammatory datasets. Key methodological details related to data processing, normalization, cross-species comparison, and statistical analysis are insufficiently described. In addition, the limited number of differentially expressed genes identified does not align with the extensive psoriasis transcriptomic literature, raising concerns about analytical rigor.

      Finally, the manuscript emphasizes a small number of genes described as "psoriasis-associated" while failing to demonstrate regulation of widely accepted psoriasis signature genes known to correlate with disease activity and therapeutic response in patients.

      We thank the reviewer for this thoughtful and comprehensive assessment of our study. We carefully considered each of the concerns raised regarding the interpretation and translational relevance of our findings and have substantially revised the manuscript accordingly.

      Specifically, we have tempered our interpretation throughout the manuscript to clearly distinguish IMQ-induced dermatitis from human plaque psoriasis and to emphasize that our conclusions should be interpreted primarily within the context of the IMQ-induced inflammation model. To improve the relevance of our findings to psoriasis biology, we performed additional experiments using IL-17A- and TNF-α-stimulated primary keratinocytes and incorporated these data into the revised manuscript. We also expanded the description of our RNA-seq analyses, including dataset selection, analytical procedures, and cross-species comparison, and clarified the rationale for selecting representative UPR-responsive genes for validation. In addition, we revised the Introduction and Discussion to more appropriately position the roles of inflammasome signaling, IL-1-associated pathways, and Gelsolin in the context of IMQ-induced inflammation and human psoriasis.

      We believe that these revisions substantially strengthen the manuscript and address the reviewer's major concerns. Detailed responses to each specific point are provided below.

      Reviewer #2 (Public review):

      Summary:

      This paper shows that imiquimod, a compound often used to induce a psoriasis-like skin inflammation in mice, has a TLR7-independent effects that induce the unfolded protein response and amplify cytokine expression in dendritic cells. Although these effects of imiquimod have been described in the literature before, this study provides more detailed evidence and different contexts to this observation. These findings add to existing literature that imiquimod has a pleotropic mechanism of action involving changes in mitochondrial functions and cellular stress responses. Specifically, the authors show that imiquimod can induce calcium signaling in immune cells and potentiate two branches of the unfolded protein response in a TLR7-independent and MyD88-independent manner. They also show that some of these effects might be partially mediated by direct binding of imiquimod to Gelsolin. These findings expand our understanding of imiquimod-mediated inflammation and are useful for the field of experimental skin immunology and mouse models of psoriasis. However, the molecular and cellular mechanisms connecting Gelsolin to the unfolded protein response and skin inflammation presented in this paper require further investigation in the context of TLR-mediated inflammation.

      We sincerely thank the reviewer for this thoughtful and balanced assessment of our study. We greatly appreciate the recognition that our work provides additional mechanistic insight into the TLR7-independent actions of IMQ and expands current understanding of IMQ-induced inflammation, mitochondrial dysfunction, and unfolded protein response signaling. We also appreciate the recognition that our findings may be valuable for the fields of experimental skin immunology and mouse models of psoriasis. In response to the reviewer's comments, we have further revised the manuscript to clarify the rationale for investigating Gelsolin, to better distinguish IMQ-induced inflammation from human psoriasis, and to more appropriately discuss the limitations of our mechanistic interpretation. Detailed responses to the specific points raised are provided below.

      Strengths:

      (1) TLR7-independent effects of imiquimod on the expression of genes and proteins involved in the unfolded protein response are well demonstrated.

      (2) Gelsolin is identified as a new imiquimod-binding protein in mouse cells.

      We sincerely thank the reviewer for these positive comments. We greatly appreciate the recognition that our study provides clear evidence for the TLR7-independent effects of IMQ on unfolded protein response signaling and identifies Gelsolin as a novel IMQ-binding protein. We are grateful for the reviewer's positive assessment of these findings.

      Weaknesses:

      (1) Effects of imiquimod on mitochondrial Ca signaling are not clear from the presented data.

      (2) The mechanism of action connecting imiquimod to Gelsolin on the unfolded protein response and cytokine production remains not fully explained.

      (3) It remains unclear if Gelsolin contributes to regulating TLR7 (or other types of TLR-mediated) inflammation in vivo.

      We thank the reviewer for these thoughtful comments. We have carefully considered each of the concerns raised regarding the interpretation of mitochondrial Ca<sup>2+</sup> signaling, the mechanistic link between Gelsolin and UPR signaling, and the role of Gelsolin in TLR-mediated inflammatory responses. In the revised manuscript, we have clarified the interpretation of our mitochondrial Ca<sup>2+</sup> data, strengthened the discussion regarding the mechanistic role of Gelsolin based on the additional experiments performed in this revision, and more clearly defined the scope of our conclusions regarding Gelsolin in IMQ-induced inflammation. We believe these revisions substantially strengthen the manuscript while avoiding conclusions that extend beyond the experimental evidence. Detailed responses to each point are provided below.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      The following points outline specific issues that would need to be addressed to substantially strengthen the manuscript. Several of these represent fundamental limitations of the current study design and interpretation.

      We thank the reviewer for this overall assessment. We have carefully addressed each of the points raised and have revised the manuscript accordingly. Detailed point-by-point responses are provided below.

      (1) Model limitations

      - The manuscript relies exclusively on imiquimod (IMQ), which does not model the core immune drivers or treatment responsiveness of human psoriasis.

      - Claims regarding relevance to human psoriasis should therefore be substantially tempered, or alternative models more reflective of human disease biology should be incorporated.

      We thank the reviewer for this important comment. We agree that the IMQ-induced dermatitis model does not fully recapitulate the immunopathology, chronicity, or therapeutic responsiveness of human plaque psoriasis. Accordingly, we have substantially tempered our interpretation throughout the manuscript. In the revised Introduction and Discussion, we explicitly state that our findings should be interpreted primarily in the context of IMQ-induced skin inflammation rather than human psoriasis, and that further validation in human psoriasis-relevant systems will be required. We have also revised statements throughout the manuscript to avoid overgeneralization regarding human psoriasis. In addition, to improve the disease relevance of our mechanistic findings, we have performed additional keratinocyte experiments using IL-17A and TNF-α stimulation, which better reflect the canonical inflammatory pathways implicated in human psoriasis. Together with the revised interpretation throughout the manuscript, we believe these changes appropriately position our findings within the context of the IMQ-induced dermatitis model while improving their relevance to human psoriasis.

      Changes made in the manuscript: See Figure S6

      - The Introduction and Discussion were revised to clarify the limitations of the IMQ-induced dermatitis model and to distinguish IMQ-driven inflammation from human plaque psoriasis.

      - Statements implying direct relevance to human psoriasis were revised to more appropriately reflect the scope of the study.

      - Additional experiments using IL-17A and TNF-α-stimulated keratinocytes were incorporated to strengthen the relevance of the findings to established psoriasis biology.

      (2) Immune context

      - gdT cells should be removed from the Introduction as contributors to IL-17A production in human psoriasis, as this is a feature of mouse models rather than human disease (PMID: 28945199).

      - The roles of Th17 and Tc17 cells should be emphasized, with appropriate acknowledgment that IMQ-driven inflammation differs substantially from human psoriasis immunopathology.

      We thank the reviewer for this valuable comment. We agree that gdT cells are major IL-17A-producing cells in the IMQ-induced mouse model but are not considered the principal source of IL-17A in human plaque psoriasis. Accordingly, we have revised the Introduction to remove statements implying that gdT cells are major contributors to IL-17A production in human psoriasis and have instead emphasized the established roles of Th17 and Tc17 cells. In addition, we have revised the Discussion to explicitly acknowledge that the immunopathology of the IMQ-induced dermatitis model differs substantially from that of human psoriasis and that our findings should therefore be interpreted within the context of IMQ-induced skin inflammation.

      Changes made in the manuscript:

      - Statements describing gdT cells as major IL-17A-producing cells in human psoriasis were removed from the Introduction.

      - The roles of Th17 and Tc17 cells in human psoriasis were emphasized.

      - Additional text was added to the Discussion clarifying the immunological differences between the IMQ-induced dermatitis model and human plaque psoriasis.

      (3) Keratinocyte stimulation

      - IMQ stimulation of keratinocytes is not an accepted model of psoriasis-relevant keratinocyte activation.

      - To support disease relevance, experiments should incorporate stimulation with IL-17A (100 ng/ml) {plus minus} TNF-a (10 ng/ml) and appropriate time points consistent with established psoriasis biology.

      We thank the reviewer for this constructive suggestion. We agree that stimulation of keratinocytes with IL-17A and TNF-α more closely reflects cytokine-mediated keratinocyte activation in human psoriasis than stimulation with IMQ alone.

      We would like to clarify that our IMQ stimulation experiments were not intended to serve as a model of psoriasis-associated keratinocyte activation. Rather, these experiments were designed to investigate the molecular mechanisms by which IMQ directly induces UPR signaling in keratinocytes, as IMQ is the primary experimental stimulus used throughout this study.

      To address the reviewer's concern regarding disease relevance, we performed additional experiments using primary keratinocytes stimulated with IL-17A and TNF-α. As expected, IL-17A and TNF-α robustly induced canonical psoriasis-associated genes, including S100a8, S100a9, and Defb14, thereby providing complementary evidence supporting the relevance of our findings to psoriasis-associated inflammatory signaling. These new data have been incorporated as Figure S6.

      We believe that these additional experiments appropriately complement our mechanistic studies by linking the identified pathways to established psoriasis-associated inflammatory signaling while preserving the original objective of the IMQ stimulation experiments.

      Changes made in the manuscript: See Figure S6

      - New experiments using IL-17A and TNF-a-stimulated primary keratinocytes were performed.

      - A time-course analysis was conducted to evaluate cytokine-induced gene expression.

      - The new data have been included as Figure S6.

      (4) Inflammasome and IL-1-related claims

      - The manuscript should acknowledge that IL-1 and inflammasome targeting have failed to demonstrate clinical efficacy in plaque psoriasis.

      - Observations in inflammasome-, MyD88-, or TLR-deficient mice should not be interpreted as evidence of underexplored human psoriasis pathways, but rather as reflecting IMQ-specific biology.

      We thank the reviewer for this important comment. We agree that the contribution of IL-1 signaling and inflammasome activation to IMQ-induced skin inflammation should not be directly extrapolated to human plaque psoriasis. Accordingly, we have revised the Discussion to acknowledge that clinical studies targeting IL-1 signaling have not demonstrated consistent therapeutic efficacy in plaque psoriasis. We have also tempered our interpretation of findings obtained from inflammasome-, MyD88-, and TLR-deficient mouse models, emphasizing that these observations likely reflect mechanisms specific to the IMQ-induced dermatitis model rather than underexplored pathways in human psoriasis. Throughout the revised manuscript, statements implying direct relevance to human psoriasis have been modified accordingly.

      Changes made in the manuscript:

      - The Introduction and Discussion now acknowledge the limited clinical efficacy of IL-1-targeted therapies in plaque psoriasis.

      - Statements regarding inflammasome-, MyD88-, and TLR-dependent mechanisms have been revised to clarify that they primarily reflect IMQ-specific biology.

      - Interpretations linking these pathways directly to human psoriasis have been moderated throughout the manuscript.

      (5) Cathelicidin and defensin biology

      - Statements suggesting that LL37 or b-defensins "exacerbate psoriasis" should be revised to reflect their contributory roles in disease pathogenesis rather than disease worsening.

      - It should be acknowledged that CRAMP- or defensin-deficient mice do not show improvement in IMQ-induced dermatitis, consistent with IMQ bypassing these pathways.

      We thank the reviewer for this valuable comment. We agree that LL37 and b-defensins should not be described as factors that directly exacerbate psoriasis, but rather as multifunctional mediators that contribute to disease pathogenesis in a context-dependent manner. Accordingly, we have revised the relevant statements throughout the manuscript to more accurately reflect their proposed roles.

      In addition, we have expanded the Discussion to acknowledge previous studies demonstrating that CRAMP- or b-defensin-deficient mice do not exhibit substantial improvement in IMQ-induced dermatitis. We now explicitly state that IMQ-driven inflammation can proceed independently of these pathways, highlighting the distinction between mechanisms contributing to human psoriasis pathogenesis and those operating in the IMQ-induced dermatitis model.

      Changes made in the manuscript:

      - Statements describing LL37 or b-defensins as exacerbating psoriasis were revised to indicate that they contribute to disease pathogenesis.

      - The Discussion was expanded to acknowledge that CRAMP- or b-defensin deficiency does not substantially attenuate IMQ-induced dermatitis, consistent with the IMQ model bypassing these pathways.

      - The limitations of extrapolating these observations to human psoriasis were clarified.

      (6) Gelsolin and IMQ-binding experiments

      - Experiments focused on proteins that bind IMQ have limited translational relevance.

      - If gelsolin is to be emphasized, the rationale should be grounded in human psoriasis data demonstrating altered gelsolin levels rather than IMQ binding (PMIDs: 36902587, 32002760).

      We thank the reviewer for this important comment. We agree that the translational relevance of proteins identified solely through their ability to bind IMQ is limited. Accordingly, we have revised the manuscript to clarify that our rationale for focusing on Gelsolin is supported not only by its interaction with IMQ but also by independent evidence demonstrating altered Gelsolin expression in patients with psoriasis and psoriatic arthritis. We have incorporated these human studies into the Introduction and Discussion and have revised the relevant text to emphasize the potential clinical relevance of Gelsolin beyond its interaction with IMQ.

      Changes made in the manuscript:

      - Statements emphasizing IMQ binding as the primary rationale for studying Gelsolin were revised.

      - Additional references reporting altered Gelsolin expression in patients with psoriasis and psoriatic arthritis were incorporated.

      - The Discussion now clarifies that the rationale for investigating Gelsolin is supported by both its interaction with IMQ and independent observations from human disease.

      (7) Vehicle controls

      - Appropriate vehicle controls for IMQ treatment (Aldara alone) should be included and clearly described, particularly given the known inflammasome-activating properties of isostearic acid (PMID: 23463003).

      - The use of DMSO or ethanol as vehicle controls is not justified in this context.

      We thank the reviewer for this important comment. We agree that inclusion of an appropriate vehicle control for Aldara cream would have strengthened the interpretation of the in vivo experiments. Unfortunately, the vehicle formulation of Aldara was not commercially available to us and therefore could not be included in the present study.

      Because the in vivo experiment assessing mtDNA accumulation in ear tissue following topical IMQ cream application could not be appropriately controlled, we have removed these data from the revised manuscript. We believe this is the most appropriate approach to avoid overinterpretation of results that may potentially be influenced by the cream formulation.

      Importantly, our in vitro experiments were performed using purified IMQ rather than IMQ cream. Thus, our conclusion that IMQ induces mtDNA release is supported by experiments performed with purified IMQ, independent of the topical cream formulation.

      Changes made in the manuscript: See Figure 4

      - The in vivo experiment assessing mtDNA accumulation in ear tissue following topical IMQ cream application has been removed from the revised manuscript.

      - The Results and corresponding figure have been revised accordingly.

      - The Discussion has been updated to acknowledge the limitation associated with the absence of an Aldara vehicle control.

      (8) RNA-sequencing and bioinformatics

      - The rationale for selecting specific mouse and human RNA-sequencing datasets should be clearly articulated.

      - All datasets analyzed should be explicitly identified, with clarification of their relevance and publication status.

      - Methods describing normalization, differential expression analysis, false-discovery correction, and cross-species gene mapping should be expanded to ensure transparency and reproducibility.

      We thank the reviewer for this constructive comment. We have substantially expanded the description of the RNA-sequencing and bioinformatics analyses to improve transparency and reproducibility.

      First, we now explicitly describe the rationale for selecting the public RNA-seq datasets. GSE289485 was selected because it contains transcriptomic profiles from an IMQ-induced mouse model of psoriasis-like dermatitis, whereas GSE117405 contains transcriptomic data from human psoriasis lesions and healthy control skin, enabling comparison between the mouse model and human disease. We also clarify that both datasets were publicly available at the time of analysis.

      Second, detailed information regarding all GEO datasets analyzed, including accession numbers, sample descriptions, publication status, and the specific samples included in the present study, has been provided in Supplementary Table 14.

      Finally, the bioinformatics workflow has been described in substantially greater detail. The revised Methods now include descriptions of raw data retrieval from the SRA, quality trimming, sequence alignment, rRNA read removal, read counting, normalization, differential expression analysis, multiple-testing correction, and the orthology-based cross-species comparison used to identify conserved transcriptional responses between mouse and human datasets.

      Changes made in the manuscript: See Table S14

      - The rationale for selecting GSE289485 and GSE117405 was added.

      - Detailed information for all analyzed datasets was summarized in Supplementary Table 14.

      - The RNA-seq Methods were expanded to describe quality control, alignment, read counting, normalization, differential expression analysis, false-discovery correction, and orthology-based cross-species comparison.

      (9) Gene selection and validation

      - Validation should include canonical psoriasis signature genes known to correlate with disease activity and therapeutic response (e.g., S100A8/A9, IL-17C, IL-36g, IL-23, TNF; see PMID: 21085185).

      - The current emphasis on Ccl20, Nr4a3, and Defb14 does not adequately capture established psoriasis biology and should be better justified.

      We thank the reviewer for this valuable suggestion. We agree that validation using canonical psoriasis-associated genes strengthens the disease relevance of our findings. Accordingly, we performed additional experiments using primary keratinocytes stimulated with IL-17A and TNF-α and evaluated the expression of established psoriasis signature genes, including S100a8 and S100a9. As expected, both genes were robustly induced by IL-17A and TNF- a stimulation. In addition, Defb14, which was also induced by IMQ stimulation, was similarly upregulated by IL-17A and TNF-α. These results further support the relevance of our findings to psoriasis-associated inflammatory signaling.

      We have also clarified the rationale for selecting Ccl20, Nr4a3, and Defb14 for further validation. These genes were not intended to represent canonical psoriasis biomarkers but were selected because our transcriptomic analyses identified them as representative UPR-responsive genes that were strongly induced by IMQ stimulation. Accordingly, they were used to investigate the mechanistic contribution of UPR signaling rather than to represent the overall psoriasis transcriptional signature. This rationale has now been clarified in the revised Results section.

      Changes made in the manuscript: See Figure S6, and S7

      - Additional validation experiments were performed using IL-17A/TNF-a-stimulated keratinocytes.

      - The rationale for selecting Ccl20, Nr4a3, and Defb14 was clarified in the Results section.

      (10) Histology and data presentation

      - Ear skin sampling procedures should be standardized and clearly described.

      - All relevant control groups should be shown histologically.

      - Figures require clearer labeling, consistent terminology (e.g., ear skin vs. ear lobe), appropriate white balancing, and improved quantitative presentation (e.g., dot plots where appropriate).

      - qRT-PCR data should be presented using clearly defined raw or normalized values rather than scaled or ambiguous controls.

      We thank the reviewer for these helpful suggestions. We have revised the manuscript to improve the description of histological procedures and the presentation of histological and quantitative data.

      First, the Methods section has been expanded to clearly describe the ear skin sampling procedure. We now specify that approximately the distal 2 mm of the ear was collected and processed for histological analysis, thereby ensuring consistent sampling among all animals.

      Second, we carefully reviewed the histological figures and confirmed that the relevant control groups are included in the revised manuscript.

      Third, figure labeling and terminology have been standardized throughout the manuscript. In addition, quantitative histological data are now presented with individual data points overlaid on the graphs where appropriate, thereby improving data visualization and transparency. The representative histological images are intended to illustrate epidermal thickening, whereas the conclusions are based on quantitative measurements rather than qualitative assessment of image appearance.

      Finally, the presentation of the RT-qPCR data has been clarified. The Y-axis labels now explicitly indicate the reference condition used for normalization, and the Methods section has been expanded to describe the DDCt method, including the reference genes used for normalization.

      Changes made in the manuscript: See Figure 4D, and 5C

      - The ear skin sampling procedure was described in greater detail in the Methods.

      - Histological figures and figure labels were reviewed and terminology was standardized throughout the manuscript.

      - Individual data points were added to quantitative graphs where appropriate.

      - The RT-qPCR y-axis labels were revised to clearly indicate the normalization reference, and the DDCt analysis was described in the Methods.

      Reviewer #2 (Recommendations for the authors):

      (1) The effects of IMQ in Figure 1B are very small. I recommend adding an orthogonal approach to support that mitochondrial Ca is involved.

      We sincerely thank the reviewer for this thoughtful and constructive comment. We agree that the increase in the Rhod-2 signal observed following IMQ stimulation is quantitatively modest. However, we respectfully believe that the biological significance of this observation should not be judged solely by the magnitude of the fluorescence change. Rather, the increase in mitochondrial Ca<sup>2+</sup> should be interpreted in the context of the multiple independent functional assays presented throughout Figure 1, all of which consistently support a role for mitochondrial Ca<sup>2+</sup> in IMQ-induced inflammatory responses.

      First, we demonstrated that IMQ stimulation significantly increased intracellular ROS production, as assessed by CellROX staining (Figure 1C), and that this increase was significantly suppressed by pretreatment with 2-APB, suggesting that Ca<sup>2+</sup> dysregulation functionally contributes to ROS generation. In addition, 2-APB markedly reduced IL-1b secretion (Figure 1D), further supporting a functional link between Ca<sup>2+</sup> signaling and inflammasome activation.

      Second, IMQ stimulation induced mitochondrial dysfunction, as demonstrated by JC-1 staining (Figure 1G), and significantly increased mitochondrial ROS production, as measured by MitoSOX (Figure 1H). These findings indicate that IMQ triggers a cascade of mitochondrial events extending beyond the modest increase in mitochondrial Ca<sup>2+</sup>, ultimately resulting in oxidative stress and mitochondrial damage.

      Furthermore, treatment with the mitochondria-targeted antioxidant MitoQ, as well as the antioxidants GSHEE, NAC, and PDTC, significantly suppressed IMQ-induced IL-1b secretion (Figures 1I and 1K), supporting the conclusion that mitochondrial ROS is a critical downstream mediator of IMQ-induced inflammatory signaling.

      Taken together, these complementary findings provide multiple independent lines of evidence supporting a role for mitochondrial Ca<sup>2+</sup>-associated signaling in IMQ-induced inflammation. Although the increase in Rhod-2 fluorescence was relatively modest, it was consistently accompanied by mitochondrial ROS generation, mitochondrial dysfunction, and inflammasome activation. We therefore believe that the biological significance of mitochondrial Ca<sup>2+</sup> is best evaluated in the context of these convergent functional outcomes rather than by the magnitude of the Rhod-2 signal alone.

      We agree that an independent approach for measuring mitochondrial Ca<sup>2+</sup> would further strengthen this conclusion. However, because several complementary functional assays consistently support the involvement of mitochondrial Ca<sup>2+</sup>-associated mitochondrial dysfunction in IMQ-induced inflammatory responses, we believe that the current data collectively provide strong evidence for the proposed mechanism.

      (2) Figure 7E-G would benefit from testing effects of IMQ versus RSQ on observed phenotypes to confirm that they are mediated by Gelsolin-IMQ interaction but not an effect of Gelsolin on TLR7-mediated inflammation.

      We sincerely thank the reviewer for this valuable suggestion. We agree that it is important to determine whether the observed phenotypes reflect a specific interaction between Gelsolin and IMQ rather than a general role of Gelsolin in TLR7-mediated signaling.

      In response to this comment, we performed additional experiments using resiquimod (RSQ), a TLR7/8 agonist. Gelsolin-deficient MEFs were stimulated with RSQ, and the same parameters analyzed in the IMQ experiments were evaluated.

      Unlike the phenotypes observed following IMQ stimulation, RSQ stimulation did not reveal significant differences between wild-type and Gelsolin-deficient MEFs. Specifically, the Xbp1s/Xbp1 ratio was comparable between the two genotypes following RSQ stimulation. Similarly, mitochondrial ROS production, assessed by MitoSOX staining, and MAM formation, evaluated by proximity ligation assay (PLA), were not significantly altered by Gelsolin deficiency under RSQ stimulation.

      Although the IMQ and RSQ experiments were performed independently and were not intended as a direct side-by-side quantitative comparison, the absence of genotype-dependent effects in the RSQ experiments indicates that Gelsolin deficiency alone does not generally enhance TLR7-mediated responses. Instead, these findings support the interpretation that the enhanced UPR activation, mitochondrial ROS production, and MAM formation observed in Gelsolin-deficient cells are specific to IMQ stimulation, consistent with the interaction between Gelsolin and IMQ.

      Accordingly, the Results section has been revised to include these additional experiments, and the corresponding data have been incorporated into the revised Figure S11.

      Changes made in the manuscript: See Figure S12

      - Additional experiments using RSQ-stimulated wild-type and Gelsolin-deficient MEFs were performed.

      - The Xbp1s/Xbp1 ratio, mitochondrial ROS production, and MAM formation were evaluated following RSQ stimulation.

      - No significant genotype-dependent differences were observed under RSQ stimulation, supporting the specificity of the phenotypes observed following IMQ stimulation.

    1. Author response:

      The following is the authors’ response to the previous reviews.

      Public Reviews:

      Reviewer #2 (Public review):

      (1) The differing behavior of the MG1655 and MC4100 strains remains a lingering question concerning the generality of the conclusions. It appears unlikely that ribosomes or other growth factors partition significantly differently in the MC4100 strain than in the MG1655 strain. Furthermore, based on Fig. S15, it is still unclear to what extent MC4100 exhibits growth-rate fluctuations, as stated in the text, rather than primarily size fluctuations, as shown in the figure. It is also unclear why such very slow fluctuations would lead to qualitatively different behavior, given that the proposed mechanism appears to be rather fundamental. It would be helpful for the authors to discuss these two points.

      We thank the reviewer for revisiting this point. Here, we re-examined the MC4100 data in more detail and found that our original analysis was inaccurate; we now clarify this below along with new supporting analyses.

      We agree that there is no a priori reason for ribosome or growth-factor partitioning to differ between MC4100 and MG1655, and our expanded analysis now supports this directly in Fig.S15.

      Using the Class-1 promoter of the flagellar cascade in MC4100, which behaves under our conditions as a quasi-constitutive promoter, we find a positive correlation between instantaneous elongation rate and promoter activity that is comparable in magnitude to MG1655 (Fig.15C). We further analyzed publicly available data from two independent studies of strains expressing a constitutive fluorescent protein (new Fig.S18): Tanouchi et al. [44, 48], who tracked MC4100 at 25°C and 37°C, and Wang et al. [33], who tracked MG1655 and B/r strains. In these datasets, we found the same positive coupling between instantaneous elongation rate and expression, consistent with what we observe in MG1655. Together, these results indicate that the short-timescale coupling between growth-factor availability and gene expression that underlies our proposed mechanism is not strain-specific and is present in MC4100 for constitutively expressed and Class-1 activity.

      On the nature of MC4100's slow fluctuations: We thank the reviewer for pointing out that Fig. S15 did not distinguish growth-rate from size fluctuations. We have now computed the autocorrelation function of elongation rate for both strains and added it to Fig. S15. This analysis shows that MC4100's characteristic oscillation is present in cell size but is absent from the elongation-rate autocorrelation. We have revised the text accordingly to state that MC4100 displays long-timescale oscillations in cell size, rather than describing this as a growth-rate phenomenon.

      On why MC4100 does not show coupling between elongation rate and flagellar Class-2 activity despite this coupling being present at Class-1: In MC4100, the positive correlation between elongation rate and promoter activity, comparable to MG1655 at Class-1, is markedly attenuated at Class-2. Since both promoters are measured from the same cells and time series, this rules out our first assumption, a generic masking effect, and instead localizes the discrepancy to the Class-1-to-Class-2 step of the flagellar cascade, the pulse-generating switch we and others have described previously (Sassi et al., 2020, [24]). We do not have data to determine the molecular basis of this attenuation and present it as an open question.

      (2) It is unclear what fraction of the total proteome mVenus represents in different measurements. Adding this information would strengthen the conclusions.

      We agree that a direct proteomic quantification (e.g., Coomassie staining or mass spectrometry) would be the most direct way to determine the fraction of the proteome occupied by mVenus. However, we are no longer in a position to carry out such experiments.

      As in our original response, our elongation-rate reductions (1.3-9.3% across our promoter series; see Table S3) remain far smaller than the 67% reduction associated with ~27% proteome occupancy reported by Scott et al. [6], making it unlikely that mVenus approaches such an extreme fraction in our system.

      Now we used a validated quantitative model relating relative growth-rate reduction to unnecessary-protein fraction, built on the same ribosome-allocation theory as Scott et al. and empirically calibrated specifically for a GFP-family fluorescent protein (Bienick et al., 2014, PLoS ONE [59]). This model predicts μ/μ<sub>max</sub> = 1 - b·ɸ<sub>U</sub>, with b = 2.33 µg dry cell weight (DCW) per µg protein determined for eGFP across multiple growth media. Applying this relationship to our own elongation-rate data, using the growth rate of our non-expressing WT strain as μ<sub>max</sub>, we estimate that mVenus constitutes approximately 0.6-4.0% of dry cell weight across our promoter series, reaching ~4.0% in our strongest-expressing strain, P5.

      While this remains a model-based estimate rather than a direct proteomic measurement and involves some extrapolation across growth media and strain background relative to the original Bienick et al. study, both independent approaches converge on the same conclusion: mVenus occupies a modest fraction of the proteome in our experiments, well below the f<sub>U</sub> = 14.4% upper value explored in our simulations. This supports our original framing of f<sub>U</sub> = 14.4% as a conservative exploratory upper bound rather than an underestimate of experimental burden, and we have added this quantitative estimate (Table S3) to the revised manuscript to strengthen this point, as suggested.

    1. Author response:

      The following is the authors’ response to the previous reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      The authors combine discriminative auditory fear conditioning with longitudinal in vivo calcium imaging to ask how prelimbic (PL) representations of learned and generalized threat evolve across recent and remote memory time points. Using two different CS+ frequencies and a noshock control group, they report that PL population activity tracks graded behavioral generalization, that population similarity is highest for tones eliciting strong threat responding, and that distinct subnetworks can be identified that appear to encode tone-specific sensory features versus learned threat-related response structure.

      To my knowledge, this may be the first study to comprehensively examine neural encoding of fear generalization in prelimbic cortex (PL). The manuscript is ambitious and technically interesting, and several aspects are potentially important. In particular, the suggestion that neurons showing graded, learning-related response patterns become selectively stabilized over time is intriguing. The inclusion of two CS+ training conditions and a no-shock control also strengthens the case that at least some of the reported effects are related to associative learning rather than simple sensory differences. However, in its current form, the manuscript does not yet fully support the strength of the conceptual claims. Several issues limit confidence in the interpretation, including the possibility that repeated testing itself contributes to changes across days, uncertainty about the relationship between neural activity and freezing behavior, limited quantitative documentation of longitudinal cell registration, and a number of problems in figure clarity and statistical framing. Overall, the study contains promising observations, but the claims should be narrowed, and several analyses or controls would be needed to fully support the proposed framework.

      Comments on revised version.

      The authors have addressed my previous concerns well, and the revised manuscript is substantially improved. In particular, the additional analyses strengthen the conclusion that prelimbic cortical activity reflects learned threat value rather than simply freezing behavior, while the revised framing and additional controls clarify the interpretation of the longitudinal neural dynamics. This paper represents an important contribution to our understanding of the neural mechanisms supporting aversive learning, memory, and generalization.

      We thank Reviewer 1 for his/her constructive comments, which significantly contributed to strengthen our conclusions.

      In response to the reviewer’s recommendations, we added two new analyses to Fig. 4, presented in Fig. 4c–g.

      Reviewer #2 (Public review):

      The authors have substantially revised the paper in response to the original review, which is greatly appreciated. It is clear that it will eventually make a nice contribution to the literature. This being said, the following points are somewhere between major and minor in term of their implications for interpretation of the study results. If they were to be addressed, the paper would be again improved.

      We thank Reviewer 2 for the careful second review, which helped us sharpen our arguments and improve the manuscript. The reviewer’s additional comments prompted us to refine the scope and precision of several interpretations. Accordingly, we have removed or clarified potentially confusing language, reframed the longitudinal findings in terms of repeated retrieval rather than the passage of time, and explicitly acknowledged the limitations of relying exclusively on freezing as a behavioral measure. We now also recognize repeated nonreinforced testing as the most direct explanation for the sharpening of the generalization gradients and the responses of newly recruited neurons, while clarifying below how we view this additional learning as contributing to memory updating. We believe these revisions have substantially improved the manuscript, and we are grateful for the reviewer’s thoughtful and detailed feedback.

      There are a few remnants of the past language that are not helpful for the interpretation of the study results: 1) "Specifically, the observed population gradients could emerge either from the pooled activity of frequency-selective neurons that respond to individual tones or from neuronal subpopulations that integrate information across tones to encode their learned threat-value."; and 2) "Together, these findings suggest that the PL integrates sensory similarity with learned threat value to generate stable representations that support adaptive generalization and discrimination." Neither of these statement follows what has been shown in the study, even with inclusion of the results from the GLM analysis (see point 4 below).

      We directly address this point in response to the reviewer’s point 4

      (1) This paragraph in the Discussion is difficult to follow: "Generalization has traditionally been explained by perceptual similarity (Shepard, 1987), whereby stimuli resembling a conditioned cue recruit overlapping sensory representations and evoke similar behavioral responses (Corches et al., 2019; Grosso et al., 2018). Although perceptual similarity clearly influences the extent of generalization, accumulating evidence indicates that it cannot fully account for generalized responding (Verra et al., 2026). More recent frameworks propose that associative learning assigns learned value to novel stimuli by integrating their sensory similarity with previous experience, allowing behavior to scale according to predicted biological significance (Verra et al., 2026; Zaman et al., 2023). Our findings provide a neural framework consistent with these ideas. Sensory similarity promoted consistent neuronal population responses across tones, whereas associative learning organized these responses into graded representations that tracked learned threat value across the stimulus continuum. Thus, sensory similarity appears to define the neuronal substrate upon which associative learning constructs value-based representations that support graded behavioral generalization."

      While the revisions have removed the many unnecessary references to inference and integration, this paragraph seems like it is adhering to the original idea of how the authors wished to present their work. If the authors wished to talk about something more than perceptual similarity in the context of generalization, they should have used a task that lends itself to a more-than-perceptual-similarity explanation. Again, the inclusion of the GLM analysis is suggestive for some of what the authors wish to say, but doesn't justify the statements that: "Sensory similarity promoted consistent neuronal population responses across tones, whereas associative learning organized these responses into graded representations that tracked learned threat value across the stimulus continuum." In short, the analysis does not substitute for the design that could have and should have been used to assess learned threat value independently of sensory similarity.

      We thank the reviewer for this comment, which helped us identify ambiguity in our terminology. By “learned threat value,” we did not intend to imply that the PL independently infers or computes the value of each novel tone, separate from perceptual similarity. Rather, we used this term to denote the associative significance acquired by the CS+ and CS− during conditioning. Novel cues may then be evaluated according to their perceptual similarity to these learned associations. We have now defined “learned threat value” when it first appears in the manuscript.

      Furthermore, we agree that perceptual similarity can account for the graded generalization of responses from the CS+ to neighboring frequencies. We therefore do not consider learned associations and perceptual similarity to be competing explanations. Instead, conditioning determines which stimulus anchors the gradient and its direction according to their acquired “threat value”, whereas perceptual similarity governs how the response extends across intermediate frequencies. This interpretation is supported by our reversed conditioning design: the same frequency continuum produced opposite neural gradients depending on whether 3 or 15 kHz served as the CS+, and no gradients emerged in control animals exposed to the same tones without conditioning. Thus, the physical relationships among the tones shape the graded response, but mnemonic experience determines its organization along the frequency continuum.

      The GLM analysis was not intended to demonstrate threat value independently of sensory similarity. Rather, it showed that the learning-dependent gradient remained after accounting for freezing and therefore could not be explained solely by this behavioral response (we address the point of other potential fear responses below).

      “Generalization has traditionally been explained in terms of perceptual similarity (Shepard, 1987): stimuli resembling a conditioned cue recruit overlapping sensory representations and therefore evoke similar behavioral responses (Corches et al., 2019; Grosso et al., 2018). More recent frameworks propose that responses to novel stimuli depend not only on sensory similarity but also on mnemonic representations of learned threat value, allowing behavior to scale with the predicted significance of each stimulus (Verra et al., 2026; Zaman et al., 2023). This mnemonic contribution should be especially important when generalization is assessed long after conditioning because responding to a novel cue requires retrieval of the associations formed during learning. Our design did not manipulate sensory similarity and learned threat value independently. However, the reversed conditioning procedure dissociated them in one respect: depending on whether 3 or 15 kHz served as the CS+, the neural gradients ran in opposite directions along the same frequency continuum, with each anchored to the threat-associated tone. A gradient determined by spectral features alone would have run in the same direction in both groups. Thus, the learned associations and their mnemonic representations must have determined the anchor and direction of the neural gradient. By contrast, the contribution of sensory similarity is inferred rather than directly demonstrated: intermediate tones were represented in an order that followed their spectral distance from the CS+. Because discriminative conditioning tends to narrow generalization gradients (Dunsmoor & LaBar, 2013; Herzog et al., 2021; Jenkins & Harrison, 1960; Lommen et al., 2017), tracking neural representations over 30 days allowed us to examine how PL populations evolved as behavioral discrimination became progressively more precise during repeated retrieval. Whereas stable neuronal populations retained consistent response profiles across retrieval sessions, neurons recruited after conditioning exhibited changes that paralleled the behavioral sharpening. These results suggest that memory, new learning, and sensory similarity interact to shape generalization gradients.”

      (2) The next paragraph in the Discussion is also confusing. "Such reorganization has been proposed to provide flexibility by allowing new information to be incorporated into existing cortical representations while preserving stable behavioral performance (Mau et al., 2020; Zaki & Cai, 2024). Several mechanisms could contribute to this turnover, including systems consolidation, retrieval-induced reconsolidation or memory updating, and repeated nonreinforced stimulus exposure (Lacagnina et al., 2019; Mau et al., 2020; Sangha, 2015; Zaki & Cai, 2024). Although our experiments cannot distinguish between the first two possibilities, the behavioral data argue against extinction as the primary explanation. Extinction is generally associated with the formation of new CS+-safety associations (Bouton et al., 2021), whereas discrimination ratios increased across retrieval sessions, indicating that animals progressively improved their discrimination between threat-associated and safe stimuli rather than acquiring generalized safety responses. This pattern is consistent with previous work showing that discrimination learning sharpens stimulus representations and narrows behavioral generalization gradients (Dunsmoor & LaBar, 2013; Herzog et al., 2021; Jenkins & Harrison, 1960; Lommen et al., 2017). Importantly, turnover was not uniform across the population. Graded neurons retained remarkably consistent response profiles across retrieval sessions, and their activity remained more strongly associated with learned threat value than with freezing behavior. These observations indicate that stable components of the population code can coexist with extensive reorganization of surrounding neuronal ensembles."

      The issue with repeated testing is not caused by extinction per se. The issue is that nonreinforcement across the repeated testing should differentially affect the CS+ and CS-. Specifically, it should extinguish responding to the CS- stimulus at a rate that matches its distance from the CS+, thereby sharpening the CS+ versus CS- discrimination in precisely the ways that have been observed. Ergo, the repeated testing is a problem for inferences that might be drawn about the way that generalization gradients change with; and is a problem for statements regarding "dynamic reorganization of cortical activity patterns over time." There is nothing in the study that allows one to comment on the reorganization of cortical activity patterns over time. The reorganization can and should be attributed to the repeated testing, which is confounded with time. Nonetheless, the reorganization must be due to the repeated testing and NOT time as the present findings are inconsistent with the well-documented broadening of generalization gradients with time.

      We agree with the reviewer that discrimination between the CS− and CS+ sharpened across retrieval sessions and that repeated testing may have contributed to this effect. Our discussion of extinction was included specifically to address a concern previously raised by Reviewer 1 and to clarify that the observed sharpening did not reflect a uniform reduction in conditioned responding. We now only left this explanation in the results section.

      We also agree that later retrieval sessions are not passive readouts of the original memory. Repeated presentation can provide new opportunities for learning, update reactivated memory traces, and initiate reconsolidation. The intermediate tones illustrate this point particularly well: they are novel during the first retrieval session but become familiar through subsequent exposure, and their representations may therefore change across sessions. Thus, new learning, memory updating, and reconsolidation are not mutually exclusive explanations but interacting processes engaged by repeated retrieval. We have revised the Discussion to acknowledge these contributions more explicitly.

      We also agree that our use of phrases such as “over time” was imprecise. We have replaced this language with “across retrieval sessions” to avoid implying that the passage of time alone produced ensemble turnover.

      However, we respectfully disagree that cortical reorganization cannot be evaluated across repeated retrieval sessions or that repeated testing alone necessarily accounts for all the observed changes. Multiple studies have documented turnover within cortical ensembles following learning (Lacagnina et al., 2019; Mau et al., 2020; Sangha, 2015; Zaki & Cai, 2024). Importantly, we observed ensemble turnover by test day 1, before repeated testing could have exerted a cumulative effect, and similar early turnover has been reported by other laboratories (Kitamura et al., 2017; DeNardo et al., 2019). These previous studies have also interpreted changes in ensemble composition between conditioning and subsequent retrieval sessions, including remote retrieval, as evidence of cortical reorganization. Our paradigm differs from these studies because we introduced novel tones to examine how representations of the original CS+/CS− associations interact with representations of perceptually similar cues.

      In summary, we agree with the reviewer that repeated testing may generate additional learning that contributes to the sharpening of behavioral generalization gradients and the responses of newly recruited neurons. However, we view this learning as inseparable from memory updating and reconsolidation, because information acquired during retrieval must be incorporated into existing memory representations to persist across sessions.

      “The ensemble turnover observed here is consistent with previous studies demonstrating dynamic reorganization of cortical activity patterns across temporally separated retrieval sessions (DeNardo et al., 2019; Gallego et al., 2020; Kitamura et al., 2017; Tome et al., 2024). Such reorganization has been proposed to provide flexibility by allowing new information to be incorporated into existing cortical representations while preserving stable behavioral performance (Mau et al., 2020; Zaki & Cai, 2024). Several processes could contribute to this turnover, including additional learning during repeated nonreinforced testing, memory updating, and reconsolidation (Lacagnina et al., 2019; Mau et al., 2020; Sangha, 2015; Zaki & Cai, 2024). In our experiments, turnover was already evident at the first retrieval session, before repeated testing could have exerted a cumulative effect, indicating that this reorganization emerges early after learning. Nevertheless, repeated testing provides a plausible explanation for changes during subsequent sessions. Each retrieval session reactivated the original CS+/CS− associations while presenting the conditioned and intermediate tones without reinforcement, thereby creating opportunities for additional discrimination learning. These experiences may have progressively sharpened differentiation between the CS+ and CS-, modifying the retrieved memory representations and changing which neurons participated in representing the refined associations. Although our data do not establish a mechanistic link between neuronal turnover and additional learning, they raise the possibility that dynamic ensemble membership provides the flexibility needed to incorporate new information.”

      (3) In the next paragraph, the authors state: "At the same time, narrower generalization gradients and improved discrimination across retrieval sessions suggests ongoing memory updating. These observations are consistent with contemporary theories proposing that systems consolidation and retrieval-dependent updating are complementary processes through which memories continue to evolve after learning (Mau et al., 2020; Tome et al., 2024; Zaki & Cai, 2024)."

      In general, I'm not sure why one would invoke systems consolidation or retrieval-induced reconsolidation as an explanation for any of the present findings: they are not explanations of much at all. In this specific text, the authors seem to be implying an updating process that occurs independently of what is learned across the repeated sessions of testing. Why? The changes that occur in the behaviour and neuronal representations are perfectly explicable in terms of additional learning that occurs - of the sort that I hope to have made clear in my previous comment. Why invoke more than what is needed to explain the observed pattern of results?

      We appreciate the reviewer’s clarification. As discussed in our response to the preceding comment, we agree that repeated nonreinforced testing provided additional learning opportunities and offers the most direct explanation for the progressive sharpening of behavioral discrimination and neuronal responses. We recognize that our original wording could have been interpreted as proposing memory updating as a process occurring independently of learning during the test sessions. This was not our intention. By “memory updating,” we meant that new information acquired during repeated retrieval modified the existing representations of the CS+ and CS−, allowing these stimuli to become more clearly differentiated. Thus, the additional learning that occurs through repeated testing provides the experience through which the original associations are refined.

      We agree that systems consolidation and retrieval-induced reconsolidation are not required as direct explanations for the observed sharpening and that our design cannot isolate their contributions. However, ensemble turnover was evident by day 1, before repeated testing could have exerted cumulative effects, indicating that repeated testing cannot fully explain the turnover. We view the additional learning acquired during subsequent retrieval sessions as refining the represented values of the CS+ and CS− and, if these changes persist, as requiring incorporation into existing memory representations through updating and reconsolidation. These processes therefore complement, rather than compete with, additional learning. The revised Discussion distinguishes repeated testing as the most direct explanation for the sharpening of discrimination from the broader memory processes that may accompany this learning and contribute to cortical ensemble reorganization.

      “In summary, PL population responses formed generalization gradients that paralleled behavioral generalization and were primarily organized according to tone-learned threat value. The overlap among responses to conditioned and novel tones was consistent with their perceptual similarity, whereas repeated nonreinforced testing was accompanied by progressive sharpening of both behavioral discrimination and the response gradients expressed by neurons recruited after conditioning. Together, these findings provide a potential neural framework through which stored threat associations may guide the evaluation of perceptually similar cues.”

      “The coexistence of these stable neurons with dynamic ensembles may allow repeated retrieval to refine a memory while preserving core features of its original representation (Mau et al., 2020; Tome et al., 2024; Zaki & Cai, 2024). Determining whether these stable graded neurons are causally required for memory storage or retrieval—and whether they constitute a persistent cortical memory trace—will require longitudinal imaging combined with selective manipulation of this population.”

      (4) Re the GLM analysis - The authors write that: "the fact that the GLM analysis indicates that these neurons reflect learned threat value more than freezing behavior, suggests that they encode an abstract property of the learned stimulus rather than simply mirroring behavioral output."

      This is fine if freezing fully indexes the state of conditioned fear and there are no other behaviours in which animals express their fear. If, however, fear is expressed in a range of other behaviours that are likely coordinated by the PL (e.g., startle, vigilance, scanning, orienting to source of danger), this interpretation of the GLM analysis is unwarranted. This is an important point and would be worth noting somewhere in the paragraph where the statement appears.

      We agree with the reviewer. Our GLM demonstrates that the graded neuronal responses cannot be explained by freezing behavior alone, but it does not exclude contributions from other unmeasured manifestations of conditioned fear, including vigilance, scanning, orienting, startle, or physiological responses. We have therefore removed the claim that these neurons primarily encode threat value and revised the Discussion to acknowledge this limitation explicitly.

      “Freezing, however, does not exhaust the conditioned defensive state, and we cannot rule out contributions from unmeasured behavioral or physiological correlates of fear, including vigilance, scanning, orienting, startle, and changes in autonomic state. Our findings are therefore consistent with PL neurons representing the learned significance of the stimuli, but they do not establish that this representation is independent of all fear-related behavioral and physiological states.”

      Reviewer #3 (Public review):

      Summary:

      Normandin et al. explore the coding of stimuli predicting an aversive event in the prelimbic cortex. Stimuli could either be explicitly paired, explicitly unpaired, or novel but with an inferred association with the aversive event (generalization). Long-term tracking of GCaMP positive neurons allowed them to examine how coding evolves out to a month following training. In general, they found two types of ensemble codes. One was ensembles coding for each stimulus independently, but with enhanced responding to the one eliciting a freezing response. The other was ensembles that responded to all stimuli in proportion to their similarity to the stimulus paired with the aversive event, either increasing or decreasing their activation with the degree of freezing elicited by a stimulus. Importantly, this second set of ensembles was more stable across days, potentially providing a memory trace.

      Strengths:

      (1) The authors track ensembles in prelimbic cortex over long time scales, providing valuable information on the consolidation of neural codes.

      (2) Neural coding of generalization is examined, which is under examined in the field.

      Comments on revised version.

      The authors have convincingly and thoroughly addressed my concerns. I have no further issues regarding this study.

      We thank reviewer 3 for his thoughtful and constructive comments and the suggestion to use the GLM which greatly improved the interpretation of our data.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      One small point is that the authors could report the beta coefficients for the tone and freezing predictors from the GLM analysis shown in Figure 4. Providing these values would make it easier to directly compare the relative contributions of tone-related and freezing-related activity to the model.

      We now include this analysis in Figure 4c and 4g

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      A growing body of evidence indicates that Alzheimer's disease is not simply a disease of neurons accumulating toxic protein aggregates, but one in which the immune system, both its resident brain component and its circulating peripheral arm, plays an active and sustained role. Understanding how these two immune compartments interact with one another and with diseased neural tissue has been hampered by the fact that the mouse immune system differs fundamentally from the human one in ways likely to matter for disease progression. The authors set out to address this gap by building a modular laboratory model that brings together three human cell types in a three-dimensional setting: brain organoids derived from human stem cells to provide a neural substrate, stem cell-derived brain immune cells (microglia) to represent the resident immune compartment, and circulating immune cells (CD8-positive T cells) harvested from human blood to represent the peripheral adaptive immune response. By exposing this tri-cellular system to a toxic form of amyloid protein, the hallmark aggregating molecule of Alzheimer's disease, the authors aimed to dissect, step by step, how microglia respond to amyloid stress, what inflammatory signals they release as a consequence, and whether those signals are sufficient to attract T cells into the neural environment. They further aimed to test whether blocking the molecular receptors that guide T cell movement could interrupt this process, with the broader goal of positioning the platform as a tool for human-relevant drug screening.

      Strengths

      The conceptual architecture of the platform is one of its clearest strengths. The decision to add immune components in a stepwise, modular fashion, first characterising the neural response to amyloid, then adding microglia, then adding T cells, makes it possible to attribute observed changes to specific cellular contributions in a way that a more complex all-at-once model would not allow. This staged design is well thought-through, and its logic is clearly communicated. The combination of single-cell transcriptional profiling, calcium imaging for real-time functional readouts, transwell migration assays, and protein secretion measurements gives the study a genuinely multi-modal character that goes beyond what purely transcriptomic or purely imaging-based approaches can offer. The observation that T cells failed to migrate toward amyloid-treated organoids in the absence of microglia is a clean and conceptually important result, clearly supporting the idea that the resident immune response acts as an intermediary between amyloid pathology and the recruitment of peripheral immune cells. The identification of specific chemokine receptor pathways mediating T cell movement and the demonstration that pharmacological blockade of those receptors reduces migration and provide a degree of mechanistic resolution useful for thinking about future therapeutic strategies.

      Weaknesses

      Despite these strengths, several aspects of the work as presented substantially limit the confidence one can place in its conclusions.

      The most consequential issue concerns the origin of the cells used in the model. The three cellular components: the brain organoids, the microglia, and the T cells are derived from genetically unrelated individuals. The T cells, in particular, come from healthy blood donors unrelated to the stem cell lines used to generate the neural tissue. This means the immune cells and the tissue they are interacting with carry different molecular identity markers (the proteins that the immune system uses to distinguish self from non-self). In this setting, any T cell activation or directed movement could reflect a generic rejection-like response to foreign tissue rather than a disease-relevant, chemokine-directed recruitment process. This is not a subtle concern: it represents a fundamental ambiguity at the heart of the model's central finding, and it is not acknowledged anywhere in the manuscript. For the transwell migration data to be interpretable as a model of Alzheimer's disease rather than of immune incompatibility, the authors would need to demonstrate that migration is driven by the specific chemokine environment and not by the genetic mismatch between cells, for example, using cells from the same donor or from matched donors, or by showing that blocking identity-marker recognition does not alter migration.

      A related concern is that the T cells used are from healthy individuals, whereas T cells from people with Alzheimer's disease are known to differ in their activation state, surface receptor expression, and functional behaviour. The platform cannot yet claim to model the specific T cell biology of Alzheimer's disease until disease-relevant T cells are incorporated.

      Beyond this foundational issue, the study frequently describes findings in causal terms that the experimental design does not support. The resident immune cells are said to "drive" T cell recruitment and "establish" a feedback loop. These are strong mechanistic claims. The evidence presented indicates that when microglia are present, more T cells migrate, and that blocking T cells receptors reduces migration. What is missing is direct evidence that the specific molecules measured, particularly the chemokines CCL4 and CCL5, are the agents responsible, as opposed to other signals also present in the conditioned environment. No experiment directly neutralises these chemokines to test whether their removal is sufficient to abolish T cell recruitment. Without such an experiment, the receptor-blocking data show only that the receptors matter, not that the measured ligands are the ones activating those receptors.

      The abstract describes one particular molecule, CXCL10, as a contributor to T cell recruitment, but the data in the paper itself show no significant change in CXCL10 levels between conditions. This discrepancy between the abstract and the results is misleading to readers who may not read the figures in detail.

      The single-cell sequencing data, which form the basis for claims about changes in cell populations following amyloid treatment or microglia addition, are presented without validation of the cell type labels against established reference datasets from human brain tissue. The proportional shifts in cell populations between conditions (Figures 1H and 3E) are described as significant findings but are shown without any statistical test appropriate for this type of compositional data. Comparisons of cell-type proportions derived from single-cell sequencing require specialised statistical approaches that account for the interdependence of proportions and the variability between samples; standard tests are not appropriate here, and none are applied.

      There is also an unresolved inconsistency in the age at which the organoids were analysed by single-cell sequencing: the text states day 90, while the figure legend states day 60, and the methods section contains a passage describing experimental conditions (including a cholesterol treatment and a drug called semaglutide) that are entirely unrelated to this study and appear to have been copied from a different manuscript. These issues raise concerns about the rigour of the manuscript preparation and should be corrected.

      Finally, the sample sizes underpinning several key conclusions are small (typically three to four organoids per group), particularly for the protein-secretion measurements used to identify the inflammatory signals responsible for T cell recruitment. While organoid studies are inherently limited in scale, the strength of the mechanistic claims made here would benefit from larger sample size or independent experimental replication.

      Conclusion:

      The authors have built a platform that is conceptually well-conceived and generates data consistent with a role for microglia in bridging amyloid pathology and T cell recruitment. In that sense, they have made meaningful progress toward their stated aims. However, the platform, as described, cannot yet deliver the human-specific mechanistic insight it claims to provide, primarily because the non-autologous configuration of the model introduces an uncontrolled variable that confounds the interpretation of the immune interaction data. The claim to have provided "the first human-specific mechanistic demonstration" of microglial activation as a bridge between amyloid pathology and adaptive immune recruitment is not supported by the evidence presented. The data are consistent with this interpretation but do not establish it.

      The general approach, building increasingly complex human neural-immune models by adding components in a controlled, stepwise manner, is a valuable direction for the field and one that other groups working on neuroinflammation will find useful to consider. The combination of live calcium imaging and transcriptional profiling in the same experimental system is a practical contribution that demonstrates the kind of multi-modal readout this class of model can support. If the autologous confound is resolved in future iterations and if the mechanistic claims are grounded in more direct experimental evidence, this type of platform could become a genuinely useful tool for investigating human neuroimmune biology and for screening candidate therapeutic compounds in a human-relevant context. As currently presented, however, readers and researchers considering adopting this approach should be aware that the immune interaction data may reflect genetic mismatches between cell sources rather than disease-specific biology, and that the causal conclusions drawn from the chemokine and migration data go beyond what the experiments can support.

      Reviewer #2 (Public review):

      Summary:

      In this study, the authors developed a human forebrain organoid model incorporating both iPSC-derived microglia and CD8<sup>+</sup> T cells, enabling them to recreate and investigate multicellular aspects of AD pathology in a human-relevant system.

      Their findings show that microglia help clear amyloid-β deposits, but they also promote inflammatory responses. Activated microglia recruit CD8<sup>+</sup> T cells by releasing the chemokines CCL4, CCL5, and CXCL10, which signal through the receptors CCR1/CCR5 and CXCR3. Pharmacological inhibition of CCR5 or CXCR3 prevents T-cell recruitment and alters autophagy pathways in a microglia-dependent manner.

      Strengths:

      The study presents a versatile human organoid platform for investigating neuron-immune interactions in Alzheimer's disease. It highlights the critical role of microglia-driven recruitment of CD8<sup>+</sup> T cells in sustaining neuroinflammation and identifies CCR5 and CXCR3 signaling pathways as promising therapeutic targets for neuroinflammatory conditions.

      This study is interesting and presents novel findings supported by state-of-the-art approaches, including single-cell RNA sequencing, a three-dimensional cerebral organoid model, and co-culture systems involving two distinct immune cell populations.

      Weaknesses:

      Several aspects of the study require clarification and further improvement. For example:

      (1) Figure 1H is missing statistical analyses.

      (2) The scRNA-seq analysis shows a reduction in the proportion of cells occupying transcriptional states associated with later pseudotime values, which the authors interpret as evidence that Aβ treatment inhibits neuronal maturation. However, the data presented do not appear sufficient to support this conclusion. An alternative explanation is that Aβ preferentially affects the survival of more mature neuronal populations, leading to their depletion, consequently, an apparent enrichment of cells at earlier pseudotime states. Therefore, the observed pseudotime shift does not necessarily demonstrate impaired maturation per se. The authors should revise the interpretation of these results in the first paragraph and either provide additional evidence supporting a maturation defect or discuss alternative explanations such as selective loss of mature neurons.

      (3) A similar concern applies to the scRNA-seq data presented in Figure 3. The authors interpret the shift toward later pseudotime states in the presence of microglia as evidence of enhanced neuronal maturation. However, the data do not exclude alternative explanations. For instance, microglia may preferentially promote the survival of more mature neuronal populations or protect them from cell death, thereby increasing their relative abundance in the dataset. Consequently, the observed pseudotime distribution cannot be taken as direct evidence of enhanced maturation. The authors should revise their interpretation accordingly and discuss the possibility that the observed effect reflects differential survival rather than accelerated neuronal maturation.

      (4) In Figures 4A-E, the authors should report the levels of the secreted proteins in pg/mL instead of relative values, as this would better reflect the actual amounts produced. In Figure 4H, the inhibitor-treated control T-cell samples should be included. Furthermore, it should be explicitly stated that the inhibitor-treated data points currently shown refer to T cells cultured in the presence of myeloid Aβ.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      (1) Addressing the allogeneic confound

      To determine whether observed T cell migration reflects chemokine-driven recruitment rather than allogeneic recognition, the authors should perform one or more of the following: (a) repeat transwell migration assays using HLA-matched donors for T cells and iPSC lines; (b) include a blocking condition using anti-HLA class I antibody to suppress allogeneic recognition and test whether migration is reduced; (c) compare migration toward conditioned media alone (without cells) versus co-culture conditions to establish whether secreted factors are sufficient to drive migration independently of direct cell contact. If HLA-matched material is not currently available, the authors could, at a minimum, use conditioned media transfer experiments to dissociate chemokine-mediated from contact-mediated effects.

      We agree this is an important limitation. We have not performed HLA-matched migration assays, anti-HLA class I blockade, or conditioned-media-only migration experiments. We note that in our transwell assay design (Fig. 4G–H), T cells are seeded in the upper chamber and organoids in the lower chamber, separated by a porous membrane; while this precludes direct T cell–organoid cell contact, live organoid/microglial cells are present throughout the assay rather than their conditioned medium alone, so we have not directly tested part (c) as the reviewer describes it.

      We would also note that the CD8<sup>+</sup> T cells used in this assay were derived from a single healthy donor, while the organoids and iMGLs were derived from a separate iPSC line (DYR0100); the same T cell donor and the same organoid/microglial line were used across all conditions (CTR, Aβ42, Aβ42+iMGL). The T cell–organoid pairing is therefore allogeneic, but identical in every condition. Any contribution of allogeneic recognition to baseline migration should, in principle, be present equally across conditions and would not by itself account for the increased migration specifically toward the Aβ42 and Aβ42+iMGL conditions relative to CTR.

      (2) Direct validation of CCL5 as the responsible ligand

      To substantiate the claim that microglia-derived CCL5 is responsible for T cell recruitment, a CCL5-neutralising antibody should be added to the transwell assay. Similarly, a CCL4-neutralising antibody should be tested independently. This would allow the authors to attribute the migration effect to specific molecules rather than to the overall conditioned environment and would substantially strengthen the mechanistic interpretation.

      We appreciate this comment and agree that ligand-neutralization experiments would substantially strengthen the mechanistic interpretation. We have not performed these experiments in the current study but will consider including CCL5- and CCL4-neutralizing antibody conditions in future follow-up work. We have revised the Results/Discussion to make clear that our receptor-blockade data (Fig. 4H) establish that CCR5/CXCR3/CCR1 signaling on T cells is necessary for recruitment, but do not by themselves attribute this effect to CCL4 or CCL5 specifically, as opposed to other chemokines present in the conditioned environment.

      (3) Cell-type annotation validation for single-cell data

      The authors should add a supplementary figure showing a dot plot or heatmap of canonical marker gene expression across all annotated clusters, cross-referenced to at least one published human brain atlas or human organoid single-cell reference dataset. Module score analysis using published cell-type gene signatures (e.g., Velmeshev et al. 2019, for neuronal subtypes or established microglial signature sets) would further validate the annotations. The specific software tool and reference dataset used for annotation should be explicitly named in the Methods section.

      We thank the reviewer for this suggestion. Canonical marker gene expression supporting our cluster annotations is provided in Supplementary Figure S1 (violin plots of marker genes across annotated clusters.

      (4) Statistical testing for cell-type proportion comparisons

      Figures 1H and 3E should be reanalysed using a compositional statistical framework. The authors are encouraged to use the propeller method (Phipson et al., Bioinformatics, 2022) or scCODA (Büttner et al., Nature Communications, 2021), both of which are designed for this type of comparison in single-cell data. Individual organoid-level proportion values should be shown as overlaid data points to make biological variability is visible.

      We agree and have reanalysed both comparisons with scCODA (Büttner et al., 2021), using cell-type counts aggregated per library (n = 2 per condition). Because scCODA estimates are conditional on a reference population, we specified migrating neurons as reference — the only population with a near-unity fold change (1.19×) and no credible change under any alternative reference. The results are shown in Supplementary Table 1.

      We note that scCODA reports posterior inclusion probabilities rather than P values, and have removed P-value notation from all proportion comparisons. Figures 1H and 3E now display composition for each individual library as separate stacked bars, so that between-replicate variability is directly visible.

      (5) Functional validation of microglial-promoted neuronal maturation

      To support the claim that microglia promote neuronal maturation, at least one functional or morphological measurement attributable specifically to the microglia co-culture condition should be provided. Suggested approaches include: quantification of neurite length or branching complexity by automated image analysis comparing organoid slices with and without microglia; or synaptic puncta density measurements (already used elsewhere in the manuscript) comparing Aβ42 and Aβ42+iMGL conditions.

      Thanks a lot for pointing this out. We agree that trajectory inference alone cannot support a claim that microglia promote neuronal maturation, and we regret that we are unable to provide the requested measurement: synaptic puncta quantification in this study was performed only for the CTR and Aβ42 conditions, and the material required to extend it to Aβ42+iMGL is no longer available. We have therefore revised the interpretation rather than defend the original claim.

      We now describe the effect as a shift in organoid cell-type composition and transcriptional state toward more differentiated populations, rather than as microglia-driven neuronal maturation. The Results text has been changed from "…indicating that microglia promote neuronal maturation and partially reverse the Aβ42-induced immature state" to:

      " Pseudotime analysis showed that microglial co-culture shifted cells toward higher pseudotime values compared with Aβ42 alone (Fig. 3F–G), consistent with a shift in organoid cell-type composition toward more differentiated populations (Fig. 3E) and a partial reversal of the Aβ42-associated skew toward progenitor states.”

      (6) Chemokine secretion follow-up after T cell addition

      To begin closing the proposed feedback loop, the authors should measure CCL4 and CCL5 levels (and ideally a broader cytokine panel) in conditioned media from the Aβ42+iMGL+T condition and compare them with those from Aβ42+iMGL. If T cells amplify microglial activation (as shown by calcium imaging), one would predict increased chemokine output. Including this measurement would substantially strengthen the feedback loop claim.

      We would first clarify the scope of our claim. The feedback loop described in the manuscript operates at the level of cellular activation state: microglia-derived chemokines recruit CD8<sup>+</sup> T cells (Fig. 4A–E, 4G–H), and recruited CD8<sup>+</sup> T cells in turn amplify microglial activation (Fig. 4L). Each step is supported by direct measurement, and we do not claim that T cells increase microglial chemokine output or drive a further round of recruitment.

      We agree that measuring chemokine secretion after T cell addition would test an important extension of this model — whether T cell-driven amplification of microglial activity translates into increased chemokine output and thus a self-sustaining recruitment cycle. We are unable to perform this experiment within the revision period, as the tri-culture conditioned media were not retained.

      We would also note that this measurement is not straightforward in bulk conditioned media. CD8<sup>+</sup> T cells are themselves major producers of CCL4 and CCL5, releasing preformed CCL5 from cytotoxic granules within hours of activation, so an increase in the Aβ42+iMGL+T condition could not be attributed to microglia. A rigorous test would require cell-type-resolved output — intracellular cytokine staining, single-cell profiling of the tri-culture, or physical separation of the two populations — and we now identify this explicitly as the next step.

      (7) Time-course data for the protective-to-pathological transition

      The dual functionality narrative requires temporal data to be credible. The authors should consider measuring Aβ clearance, pseudotime distribution, and chemokine secretion at multiple time points after microglial addition (e.g., 6, 24, and 48 hours) to determine whether the protective and inflammatory outputs are sequential or whether they co-occur from the outset.

      We agree that a single 48-hour timepoint cannot determine whether protective and inflammatory microglial outputs are sequential or concurrent, and we are unable to add a time course within the revision period.

      We have therefore moderated our interpretation. The Discussion previously stated that "microglial activation is not a binary state but a spectrum, where sustained Aβ stress drives the transition from a protective to a pathological, T-cell-recruiting state." This has been revised to: "This duality indicates that microglial activation is not a binary state: within the Aβ42 environment, clearance and neuroprotective functions are detectable alongside inflammatory, T-cell-recruiting outputs at the same timepoint." The temporal claim implied by "transition" has been removed, as our data establish co-occurrence at 48 hours rather than a sequence.

      Recommendations for writing and presentation

      (8) Abstract correction

      CXCL10 must be removed from the mechanistic description of T cell recruitment in the abstract, as Figure 4E shows no significant change in CXCL10. The abstract should also moderate the language around "establishing a feedback loop" to reflect that the loop was observed and partially characterised rather than mechanistically closed.

      CXCL10 has been removed from the mechanistic description in the Abstract, as Fig. 4E shows no significant change in its secretion. CXCR3 has been retained, as pharmacological blockade reduced T cell migration (Fig. 4H), but is now presented as a receptor-level finding without an identified ligand. We have also moderated the concluding clause, which now describes a neuroimmune circuit in which recruited T cells amplify microglial activation, rather than stating that a feedback loop is established. The Abstract sentence now reads: Using this platform, we demonstrate that microglia mediate amyloid-β clearance and shift organoid cell composition toward more differentiated states, but also become inflammatory and recruit CD8<sup>+</sup> T cells through CCL4/CCL5 signaling via CCR1, CCR5, and CXCR3, forming a neuroimmune circuit in which recruited T cells further amplify microglial activation.

      (9) Resolve the day 90 / day 60 inconsistency

      The discrepancy between "day 90" in the Results text (line 88) and "day 60" in the Figure 1G legend must be corrected throughout the manuscript.

      "Day 90" in the Results text (line 88) has been corrected with “day 60”.

      (10) Rewrite the scRNA-seq library preparation methods

      The methods section (lines 357-360) must be rewritten to describe the actual experimental conditions used in this study. The passage referring to cholesterol-treated and semaglutide-treated organoids on day 30 must be removed entirely.

      The methods section has been now revised as: For isolation of iPSC-derived forebrain cells, cells were collected from CTR and Aβ42-treated organoids at day 60, and from Aβ42-treated organoids with and without a 48-hour iMGL co-culture (Aβ42 and Aβ42+iMGL). Two biological replicates were included in each group. Three organoids were pooled within each replicate and washed three times with pre-chilled PBS. Single-cell suspensions were prepared by incubating with 0.5 mg/mL papain for 30 min at 37 °C in a water bath. Suspensions were filtered through a 70 µm cell strainer (BD Falcon, 352350). After centrifugation at 500 g for 5 min, the cell pellet was resuspended in PBS + 0.01% BSA.

      (11) Report the number of organoids per scRNA-seq replicate

      The Methods section should explicitly state how many organoids were pooled per biological replicate for each single-cell sequencing experiment and how many replicates were included per condition.

      The Methods section has been revised to state explicitly the number of organoids pooled per biological replicate and the number of replicates per condition for each single-cell experiment, as described in our response to comment (10). Two biological replicates were included per condition, each prepared from 3 pooled organoids.

      (12) Attribute iPSC lines to specific experiments

      A table or supplementary note should specify which cell line (H9, DYR0100, or DXR0109B) was used for each experiment and figure. If different lines were used interchangeably within the same figure, this should be stated and any resulting variability discussed.

      All organoid data presented in this manuscript were generated from a single line, DYR0100; the H9 and DXR0109B lines were not used for any experiment reported here. We have removed them from the Methods to avoid ambiguity, and the Methods now state that DYR0100 was used for all organoid experiments. No experiment or figure combines material from different lines.

      (13) Moderate the use of "human-specific"

      Throughout the manuscript, claims of human specificity should be restricted to contexts where a direct comparison with rodent data has been performed or cited. When the platform uses only human cells, the appropriate phrasing is "human-derived" or "in a human cellular context" rather than "human-specific mechanisms."

      We have replaced "human-specific" throughout with "human-derived" or "in a human cellular context," at four locations: the Abstract, the final paragraph of the Introduction, the second paragraph of the Discussion, and the legend of Fig. 4O.

      (14) Revise the "first demonstration" claim

      The claim to provide the "first human-specific mechanistic demonstration" (line 218) is not substantiated and should be removed or substantially qualified.

      This claim has been revised.

      (15) Immunofluorescence panel legibility

      Protein label text in Figures 1B-E and 3B should be rendered in a contrasting colour (e.g., white with a black outline, or placed on a coloured background tab) so that they are readable against the fluorescence image background. Scale bars should be present and consistent across all panels within a figure.

      Protein label text in Figures 1B–E and 3B has been re-rendered in a contrasting colour so that it is legible against the fluorescence background. Scale bars are present in all panels, and their dimensions are stated in the corresponding figure legends.

      (16) Remove or justify the Animals section in Methods

      If no mouse data are presented in the paper, the Animals section should be removed. If mouse experiments were performed and the data are available, a corresponding figure or supplementary figure should be included.

      Animals section description has been removed from Methods.

      Corrections & Clarifications

      (17) The following must be corrected before resubmission:

      (a) Replace "(ref)" placeholders on lines 46 and 63 with full citations.

      (b) Replace "(cell reports 2023)" on line 48 with a properly formatted citation. This appears to refer to Feng et al., Cell Reports 42, 113313 (2023), which is already reference 9 in the list - it should simply be cited as such.

      (c) Reference 14 (Feng et al., STAR Protoc, glioma organoid protocol) does not support the CCL5-CCR5 claim for which it is cited and should be replaced with an appropriate reference.

      (d) Reference 20, cited in the text (line 56), does not exist in the reference list. The intended citation must be identified and added.

      (e) Reference 3 (Michell-Robinson et al.) is listed but not cited in the text. It should either be cited where appropriate or removed from the list.

      We have carefully reviewed the manuscript and corrected the incomplete and incorrect references.

      (18) GEO accession numbers

      The manuscript states that bulk RNA-seq data have been deposited at GEO but does not provide an accession number. The accession number must be included in the Data Availability section.

      Accession numbers have been added to the Data Availability section: bulk RNA-seq data are deposited under GSE339404 and single-cell RNA-seq data under GSE339602. Both datasets are publicly accessible.

      (19) Single-cell RNA-seq data availability

      The single-cell RNA-seq data are not mentioned in the Data Availability statement. These data should also be deposited in a public repository (GEO or a single-cell-specific repository such as the Human Cell Atlas data portal), and the accession number should be provided.

      Mentioned in comment (18).

      (20) Zenodo DOI

      The Code Availability section states that code has been deposited at Zenodo, but no DOI is provided. The Zenodo DOI must be included.

      Zenodo DOI has been added in the Methods: Single-cell RNA-seq data have been deposited at GEO under accession GSE339602 and bulk RNA-seq data under accession GSE339404; both are publicly accessible as of the date of publication. Microscopy data are available at Zenodo (DOI: 10.5281/zenodo.21686712). All other raw data, including cytokine array images, and all original code are available at https://github.com/FengYilinElaine/2-3D-AD-oranoids.

      (21) Ethical approval for human blood collection

      The manuscript states that blood was collected from healthy donors at Zhangzhou People's Hospital but does not mention institutional ethical approval for this collection or informed consent procedures. A statement confirming ethical approval (with approval number) and donor-informed consent must be added to the Methods section in accordance with eLife's policies on human subjects research.

      Ethical approval for this study was granted by the First Affiliated Hospital of Zhengzhou University (2021-KY-0875-003) and Tsinghua Shenzhen International Graduate School (2024-F125). It has been added to the Methods.

      (22) Microscopy data availability

      The manuscript states that microscopy data will be shared upon request. eLife's data policy requires that primary data supporting the figures be made publicly available at the time of publication. The authors should deposit representative raw imaging data (or processed calcium imaging traces) in an appropriate repository such as Figshare, Zenodo, or the Image Data Resource and provide the link in the Data Availability section.

      Mentioned in comment (20)

      Reviewer #2 (Recommendations for the authors):

      This study is interesting and presents novel findings supported by state-of-the-art approaches, including single-cell RNA sequencing, a three-dimensional cerebral organoid model, and co-culture systems involving two distinct immune cell populations.

      These innovative methodologies provide valuable insights into the mechanisms under investigation. Nevertheless, several aspects of the study require clarification and further improvement.

      The authors should address the points in the public review and the following additional points:

      (1) Throughout the manuscript, the figure legends contain conclusions and interpretations of the data. These statements should be removed from the figure legends and incorporated into the Results section, while the legends should be restricted to describing the experimental conditions and the data displayed.

      Revised manuscript and legends fixed the problem.

      (2) The reference list and in-text citations appear to be incomplete. In several instances, the manuscript contains placeholder citations (e.g., "Ref") instead of full references. The authors should carefully review and complete all citations.

      We have carefully reviewed the manuscript and corrected the incomplete and incorrect references. All placeholder citations have been replaced with the appropriate references, and the reference list and in-text citations have been checked for completeness.

    1. Author response:

      Summary of changes:

      (1) Framing of the sign test results. Throughout the manuscript we have clarified that the sign test provides direct evidence that the implicated gene sets are under lineage-specific selection, while the connection of this selective signal to any specific human phenotype is inferential and would require experimental validation. We also now emphasize that some sign test results are expected to be false positives, as indicated by the FDR.

      (2) FDR and cis:trans quantification. We have added explicit statements that (i) the cis dominance is consistent across a range of FDR thresholds (FDR < 0.25, 0.20, 0.10, 0.05, 0.01), (ii) the mean proportion of divergent sites explained by cis-regulation is 91%, and (iii) using the changepoint detection method, we identified 9159 cis-DMRs and 2046 trans-DMRs in total for downstream TF motif and SNV analysis. A power analysis comparing sensitivity to detect cis vs. trans effects is provided as author response image 1.

      (3) Clarification of regulation groups, including pure cis, pure trans, conserved, cis × trans and cis + trans. We have added explicit definitions of these categories in the Results.

      (4) Cis-gene direction-of-effect definition. We have clarified in the text that cis-regulated genes are defined as those where the direction of allelic difference is consistent between hybrid and parental samples. We note that the scatter plots in Figure 2B as well as Figure 2 supplemental figures plots the per-sample average percent difference in methylation. Cis genes appearing to have opposite direction-of-effect along the y=x diagonal on the scatter plot were due to a difference between this average, used only for visualization, and the values used for analysis in our statistical model. For values close to zero, average log2FC or per cent difference can flip sign even when the model correctly identifies the site as cis-regulated. The regulation classification is based on a statistical model and not the direction of average difference, so there will naturally be some small deviation around the axes when visualizing the results as a scatter plot.

      (5) New limitations. We have added four new limitations to the Discussion: (i) absence of an outgroup species; (ii) TFBS-disrupting mutations as an alternative cis mechanism; (iii) the need for experimental validation of SNV-methylation and TF-methylation links; and (iv) the scope of cell types examined.

      (6) Quantitative reporting. We have replaced "substantial" with specific numbers throughout.

      (7) Additional supplemental resource. A list of cis–cis regulated promoters and their associated genes has been added as Supplemental File 8.

      (8) Minor corrections. Missing citation for Hallgrímsdóttir et al. (2024) added; "Preprint at" removed from published paper citations; sequencing coverage reported in Methods.

      eLife Assessment:

      This study presents an important examination of the role of cis-acting versus trans-acting genetic variation on DNA methylation divergence between humans and chimpanzees, including its consequences for gene expression. By differentiating fused interspecies tetraploid cell lines into multiple cell types, the study provides compelling evidence for the importance of cis-acting changes, but incomplete evidence that these changes are of importance for adaptive trait evolution in humans. This work will be of interest to biologists and evolutionary anthropologists studying the evolution and genetics of gene regulation, particularly in primates.

      We appreciate the assessment and agree that the evidence for adaptive trait evolution is indirect. We would like to clarify what the sign test does and doesn’t establish. By rejecting a rigorous neutral null model, the sign test provides strong evidence for lineage-specific selection on DNA methylation divergence. Since the coordinated directional divergence we observe is not expected under neutral evolution, we are confident that the data are evidence of selection. However, the sign test does not identify the specific traits that selection acted upon; the connection between the signal of selection and any phenotype is speculative. Accordingly, we have now revised the manuscript to describe the sign test results as evidence of selection while keeping the interpretation of specific traits explicitly speculative. We also added discussion of the limitations on the trait-level inference (such as the absence of an outgroup, reliance on clinical HPO ontologies, etc.).

      Reviewer #1 (Public review):

      Ma et al. use human-chimpanzee tetraploid cells across different cell types to identify the genetic causes and then transcriptomic consequences of divergence in DNA methylation. They conclude that the evolution of DNA methylation is driven primarily by cis-regulatory changes, and that the evolution of CpG sites contributes to cis-regulation, while transcription factor expression underlies some trans changes. They then argue that divergence in DNA methylation is associated with changes in gene expression and may contribute to human phenotypes.

      We thank Reviewer 1 for a detailed summary of our work.

      The tetraploid model is able to provide compelling evidence that most regulatory evolution occurs due to cis-regulatory changes. My only concern is that the extent of trans-changes may be overstated, as almost all are eliminated by changing from a nominal p-value criterion to even a 25% false discovery rate.

      We agree that trans-effects are more sensitive to FDR thresholds than cis-effects, and we have addressed this directly. This is a well-recognised limitation of existing cis/trans classification frameworks, and we acknowledge this limitation in the discussion and have added suggestions in experimental set-up to mitigate it. To address the reviewer's concern directly, we have added a formal power analysis quantifying the relative power to detect cis and trans effects as a function of read depth as well as biological noise (dispersion). We now explicitly state in the Results that the cis dominance over trans is consistent across a range of FDR cutoffs (FDR < 0.25, 0.20, 0.10, 0.05, 0.01; Figure 2—figure supplement 1–2), and we note that the greater FDR-sensitivity of trans-DMRs likely reflects systematically smaller effect sizes rather than false positives. We have added a power analysis in Author response image 1 that formally compares our sensitivity to detect cis vs. trans effects. We also note that DMR-level analyses recover both cis and trans effects at meaningful FDRs, consistent with the idea that trans effects are real but requires more replicates as well as a higher sequencing depth to make significant calls at the same level as cis changes at the individual CpG level.

      Author response image 1.

      Power analysis of cis and trans effects detected by the beta-binomial GLM framework. For each combination of effect size, per-unit read depth, and overdispersion (φ), we simulated a genome of 10,000 units — either individual CpG sites or regions/DMRs — comprising 2,000 true-effect units and 8,000 null units. The simulation is unit-agnostic: a "unit" represents a single CpG when modeling the per-CpG analysis and an aggregated region when modeling the regional (DMR-level) analysis, with read depth interpreted as the per-CpG coverage or the region-level (aggregate) coverage, respectively, and effect size as the corresponding per-CpG or region-level H–C methylation difference.

      Effects were classified using the same two-model scheme as the main analysis. A unit was called cis if the hybrid allelic (H–C) test was significant and the allele-by-generation interaction was not significant, and trans if the interaction was significant and the hybrid allelic test was not significant; all tests were Benjamini–Hochberg–corrected across the genome at the stated FDR threshold. Each unit was simulated with the full six-measurement design (two parental samples and four hybrid alleles from two hybrids), both models were fit, each set of p-values was BH-corrected across the genome, and "power" is the fraction of true units that land in the correct class.

      Cis-effect units were simulated with an equal H–C difference in both parents and hybrid (zero true interaction); trans-effect units with a parental H–C difference and no hybrid allelic difference (full-magnitude interaction); null units with no difference in either parents or hybrid. Sequencing depth was treated as a fixed design parameter: every sample at every simulated unit was assigned the same total read depth (the value on the y-axis of the heatmaps), corresponding to per-CpG coverage for the site-level analysis or aggregate per-region coverage for the regional analysis.

      We estimated the beta-binomial overdispersion (φ) directly from the data for each cell type used in this study: DA = 0.024, CNCC = 0.016, IPSC = 0.013, SKM = 0.014, and HEP = 0.011 (median = 0.014). To span this empirical range and to assess robustness to higher-than-observed dispersion, we evaluated power at φ = 0.015 (approximating the empirically observed median), 0.05, and 0.10; the latter two represent substantially more conservative (higher-noise) scenarios than any cell type in our data. Because power declines monotonically with φ, the φ = 0.015 row reflects the sensitivity expected under realistic conditions, while the higher rows bound the worst case. For each unit, a methylation probability was drawn from a beta distribution whose mean equals the unit's true methylation level and whose dispersion is set by the overdispersion parameter φ, and the number of methylated reads was then drawn from a binomial with that probability and the specified total depth. Consequently, the reported power describes the sensitivity expected at a given uniform per-unit (per-CpG or per-region) depth, spanning 10× to 200×, and is interpreted as the proportion of true-effect units assigned to the correct class.

      The follow-up analyses are incomplete with major gaps. The authors focus on single potential mechanisms for cis- and trans-changes, but it is not clear to what degree these mechanisms explain the extent of cis and trans changes. There are also other mechanisms which are not investigated, such as the importance of TF binding sites for cis-regulatory evolution.

      We agree that CpG-disrupting SNVs and TF binding motifs are just two out of many possible mechanisms, and we have added explicit acknowledgements of this in the text. Our goal was not to investigate all possible mechanisms, but rather to focus on two that showed promising results. For cis-regulation, we now state that TFBS mutations and other sequence variants could also contribute. We agree that further mechanistic investigation is an important direction for future work, and we have noted this explicitly in the Discussion.

      Next, the authors seek to show that differences in DNA methylation are functionally relevant... I worry that this result could be confounded by larger effect sizes for cis-changes than trans effects.

      We agree that larger cis-regulatory effect sizes could contribute to this result, and have now mentioned this in the Discussion: “This finding suggests that the repressive effects of species-specific methylation are strongest when both layers of regulation are driven in cis, perhaps because cis-regulated methylation changes tend to have larger effect sizes than trans-regulated changes.”

      Finally, the authors make a case for lineage-specific selection on DNA methylation that is connected to human traits. This evidence was not convincing. In fact, it is even said that these tests cannot be interpreted as evidence of lineage-specific selection (lines 399-401), so I am confused why these results are framed as testing for selection.

      We appreciate this comment but want to clarify. Lines 399–401 in the original manuscript state that the dental pulp stem cell (DPSC) sign test results specifically should not be interpreted as evidence of lineage-specific selection, because DPSCs use parental rather than hybrid cell lines. This caveat applies only to DPSCs. For all other cell types (iPSC, DA, CNCC, SKM, HEP), which use hybrid cell lines that control for trans-acting confounders, the sign test does indeed provide evidence of non-random directional bias inconsistent with neutral evolution, thereby constituting evidence of lineage-specific selection. We have added a clarifying sentence to make this distinction explicit: "For all other cell types (iPSC, DA, SKM, HEP, CNCC), which use hybrid cell lines, the sign test results provide direct evidence of lineage-specific selection on the implicated gene sets, as the hybrid system controls for trans-acting confounders."

      To be clear about the scope of the claim: the sign test directly demonstrates that the implicated gene sets are under lineage-specific selection. What remains inferential is the connection between this selective signal and any specific human phenotype, which would require experiments or further validation to establish; we have revised the framing throughout to keep this distinction explicit.

      Reviewer #1 (Recommendations for the authors):

      (1) Line 96: How many iPSC lines were used for each species? When a replicate is mentioned (e.g., Figure 1B), are those technical or biological replicates?

      We have added the iPSC line counts to both the Results and Methods sections: two human and two chimpanzee iPSC lines were used. Replicates shown in Figure 1B are biological replicates (independent differentiation experiments from the same iPSC lines).

      (2) Line 98: How many donors for the DPSCs?

      We have added DPSC donor counts to the Methods: two human and two chimpanzee donors.

      (3) Line 103: PCA and other analyses combined data from WGBS and RRBS cell types. Some clarification about how this was done (e.g. restricting to RRBS sites?) would be useful in the main text as well as an acknowledgement of potential biases. And

      (4) Line 103: Related, what is the number of CpG sites considered?

      We have added a clarifying sentence to the Results: cross-cell-type analyses including Figure 1B heatmap and Figure 1C PCA analysis were restricted to CpG sites covered in all samples (i.e., the intersection of all covered sites, after phasing the hybrid samples), totaling 561,762 shared CpG sites. Within-cell-type PCA analysis in Figure 1—supplemental figure 1 was restricted to CpG sites shared across samples of the same cell type, which contains 31,802,196 sites for CNCC samples, 26,163,237 sites for DA, 29,787,850 sites for DPSC, and 1,006,674, 935,636 and 952,835 sites for IPSC, SKM and HEP, respectively. We acknowledge that this restriction to the intersected CpG sites result in PCA performed on sites covered by both WGBS and RRBS, which are most frequent in CpG-dense regions.

      (5) Line 103: For Figure 1B, it would be useful to first mention how human/chimp reads were parsed and for how many CpG sites this was possible.

      We have added a brief description of the allele-parsing approach (SNPsplit using species-specific SNV positions). For hybrid WGBS samples (DA and CNCC), on average, 48.2% ± 0.2% of all aligned reads are unassignable using SNPs between human and chimpanzee genome, 25.9% ± 0.2% of the reads are specific to human, and 25.1% ± 0.2% of reads are specific to chimpanzee. For hybrid RRBS samples (IPSC, SKM and HEP), on average, 88.4% ± 0.3% of all aligned reads are unassignable using SNPs between human and chimpanzee genome, 5.3%±0.1% of the reads are specific to human; 5.3%±0.1% of reads are specific to chimpanzee. We have added information above to the main text. Per sample splitting reports containing the exact number of reads assignable to each of human and chimpanzee are provided as a comprehensive table at Supplemental File 1. The lower assignment rate in RRBS is expected, and we have performed two additional analyses to demonstrate why. First, the reduced representation strategy concentrates coverage in CpG-dense promoters that are highly conserved between human and chimpanzee and therefore SNV-poor, while the short MspI fragments that dominate these libraries frequently fail to reach an informative SNV even when one is nearby. Quantifying this directly: among the 16,845,376 CpG positions covered by the union of all unphased hybrid RRBS libraries, 65.1% contain a human–chimpanzee SNV within ±50 bp (the reach of a typical RRBS read), compared with 90.8% within ±150 bp (the reach of a typical WGBS read pair) — a 1.40-fold difference in SNV accessibility at the very same CpGs. Second, we compared the aligned-length distributions of allele-resolved and unassigned reads across all ten hybrid libraries (Author response image 2). In the four WGBS libraries the two distributions are indistinguishable, confirming that read length is not driving mappability. In contrast, for all six RRBS libraries, allele-resolved reads are consistently longer than unassigned reads, with the effect reproducible across every cell type and replicate.

      Author response image 2.

      Aligned read length determines allele-assignment success in RRBS but not in WGBS. Aligned read lengths were extracted from the Bismark-aligned BAM files produced by phasing all ten hybrid bisulfite libraries: four WGBS libraries (CNCC and DA, two replicates each; left) and six RRBS libraries (HEP, iPSC and SKM, two replicates each; right). For each library, reads assigned to either the human (genome1) or chimpanzee (genome2) alleles were pooled into a single phased set (blue) and compared with the reads that could not be phased (grey); distributions were computed from subsampled reads and are shown as boxplots (box, interquartile range; line, median; whiskers, 5th–95th percentiles). In the WGBS libraries, phased and unassigned reads have effectively identical length distributions (median 150 bp for both; means 147.4–147.8 vs 142.1–143.1 bp), indicating that read length does not drive mappability in WGBS. In the RRBS libraries, which are dominated by short MspI fragments, phased reads are consistently longer than unassigned reads across every cell type and replicate (medians 70–75 vs 49–50 bp; means 80.5–85.7 vs 58.6–60.6 bp, ~1.4-fold). Because a read can be assigned to a parental allele only if it spans an informative human–chimpanzee SNV, these results show that the short fragment length characteristic of RRBS — together with its enrichment for SNV-poor, evolutionarily conserved CpG-dense promoters — accounts for its lower allele-resolution rate relative to WGBS.

      (6) Line 103: Hybrid/parental line isn't noted in the PCA. Is this just the parental samples?

      We clarify that Figure 1C shows both parental and hybrid samples, and we have updated the figure caption for Figure 1C to note that both hybrid and parental samples are plotted in the PCA. The parent/hybrid stratifications are shown in Figure 1—figure supplement 1 and referred to in the main text.

      (7) Line 149: No citation # is given for the Hallgrimsdottir paper.

      Corrected. Citation number 50 (Hallgrímsdóttir et al., 2024) has been added.

      (8) Line 167-169: Some explicit test here would be useful. Is this more than we'd expect just because the majority of CpG sites have conserved methylation levels? How much more do divergent CpG sites cluster than expected by chance?

      We agree that an explicit test of clustering would be informative, and we want to be clear about what our analysis does and does not establish. The changepoint algorithm is not a test of non-random clustering: it detects shifts in the local composition of regulatory classifications along the genome and segments each chromosome into locally homogeneous stretches. Its purpose here is enrichment rather than inference, because it selects regions in which neighboring CpG sites share both a regulatory classification and a consistent direction of species bias, so that the downstream motif-enrichment and CpG-SNV proximity analyses operate on interpretable units rather than on mixtures of mechanisms. Because the segmentation is not compared against a null model, it cannot by itself establish that divergent sites co-localize more than expected given that 83–93% of all sites are conserved. We have therefore revised the text so that Figure 2D reads as a descriptive summary of the neighbourhood composition of each regulation group, and removed any implication that the co-localization has been tested against a chance expectation. Asking whether divergent sites cluster more than expected is a genuinely different question from the one our DMR-calling addresses and answering it well would require a dedicated null model. We think this is a worthwhile analysis and a natural extension of this framework, but it is separate from the claims we make here, and we have not attempted it in this revision.

      (9) Line 186-187: It should be made clear that you looked to cis, trans, and cis + trans DMRs independently.

      We have revised this sentence to make explicit that cis-DMRs, trans-DMRs, and cis+trans DMRs were identified independently using the changepoint detection method applied separately to each regulatory class.

      (10) Line 190-192: Some quantification of the degree to which cis effects exceed trans effects would be useful. What proportion of total divergence (e.g. mean and s.d.) is explained by cis factors?

      We have added this quantification: “At FDR < 0.05, cis-regulation accounted for a mean of 91% of divergent sites and trans-regulation a mean of 4.5% across cell types, and cis remained the dominant category at every FDR cutoff tested (FDR < 0.25–0.01; Figure 2C, Figure 2—figure supplement 1–2, Supplemental Files 1–2).”

      (11) Line 194-196: It should be made clear that motif enrichment was done in the human genome, right? Are the results consistent if motif enrichment was done in the chimpanzee genome?

      We have clarified in the Methods that HOMER motif enrichment was performed using the human genome (hg38) as background. Repeating the analysis using the chimpanzee genome as background is a valuable future direction; we acknowledge this has not been formally tested.

      (12) Line 208: For TFs other than FOXM1 and FOXA2, is TF expression generally associated (positively or negatively) with trans DMRs favoring the chimpanzee or human lineage? An idea of the distribution would be useful.

      We plotted the distribution of differential TF expression for those with predicted binding sites enriched in Hu>Ch trans-DMRs versus Hu<Ch trans-DMRs in DA and CNCC. In neither cell type do the two distributions show a clear separation of directional shift. TF expression differences are broadly overlapping regardless of whether the associated trans-DMR favors the human or chimpanzee lineage. We speculate the lack of separation reflects multiple trans-acting inputs shaping methylation divergence such that single TF expression does not predict it. Aggregating across TFs with potentially opposing effects could further contribute to this observation as well (Figure 3—figure supplement 1). FOXM1 and FOXA2 are individual cases where a suggestive relationship was visible rather than evidence of genome-wide pattern.

      Author response image 3.

      Distribution of differential expression of TFs with predicted binding sites enriched in trans-DMRs. Density distribution of TF expression difference in human versus chimpanzee parental samples. There is a lack of separation between expression of TFs with predicted binding sites enriched in Hu>Ch trans-DMRs versus Hu<Ch trans-DMRs, in both DA and CNCC.

      (13) Line 211-212: Stats are needed.

      This statement is intended as a qualitative description rather than a quantitative statement. With only 4 cell types per comparison (Figure 3B), we do not have enough statistical power to establish a significant correlation, therefore we present this result as an exploratory observation rather than a statistically significant finding. We have therefore removed "consistent with this expectation," reframed the FOXM1 and FOXA2 results as descriptive observations from individual factors, and added an explicit statement that they are exploratory and hypothesis-generating rather than evidence of a genome-wide pattern.

      (14) Figure 3C: Direction is not given. It should be made clear that this is a gain/loss in humans.

      We have updated the Figure 3C caption to explicitly label the three SNV categories as: CpG gains in humans (human allele creates a CpG), CpG losses in humans (human allele disrupts a CpG), and no CpG change.

      (15) Figure 3C: Most cell types have a bias towards increased DNA methylation when there are no nearby CpG sites (gray bars). Why? Is this a consequence of a reference bias?

      We thank the reviewer for raising this. The grey bars correspond to methylation levels of conserved CpG sites near SNVs with no CpG-altering substitution and serve as the genome-wide background/control category, against which the substitution-containing categories are compared. Their modest skew toward higher methylation reflects a global offset shared by all categories rather than a substitution-specific effect. We suggest two non-exclusive explanations for this baseline offset: a genuine genome-wide difference in the distribution of human- versus chimpanzee-biased methylation, and/or a possible contribution of reference genome mapping bias arising from alignment to the human genome. Importantly, this does not affect the conclusions drawn from Figure 3C. Because the genome-wide offset is shared across all categories, the substitution-attributable signal is reflected in the difference between the CpG-gain/loss categories and the no-change (grey) baseline, and any genome-wide baseline shift — biological or technical — cancels in that comparison. We therefore interpret the grey-category asymmetry as a background property and explicitly do not attribute it to the substitutions themselves. Future work such as analyzing with reads mapped to the chimpanzee or a masked consensus genome or restricting to mappability- and coverage-matched regions could directly quantify any reference-bias contribution, and we note these as promising directions.

      (16) Line 258-269: Figure 3D is not referenced in the text.

      We have added a reference to Figure 3D in the relevant paragraph of the Results: “To test this, we compared the genomic distance between each DMR and its nearest CpG SNV. Consistent with our model, we found consistently shorter distances for cis-DMRs than trans-DMRs across all cell types examined: Median distances to the nearest CpG SNV were 24 ± 6 bp for trans-DMRs vs. 11 ± 2 bp for cis-DMRs (Figure 3D; Mann-Whitney p < 0.001 for all comparisons) [65].”

      (17) It is unclear why Figure 4A-C focus exclusively on cis-regulated promoters. Is this for biological or technical reasons?

      Both. Biologically, cis-regulated promoters are the most interpretable for assessing cell type-specificity, because cis effects are allele-intrinsic and not confounded by differences in trans-acting environments across cell types. Technically, trans-regulated promoters show methylation differences that depend on the trans-environment, making cross-cell-type comparisons less straightforward.

      (18) Line 371: How many DMRs are being considered?

      We have added the total number of DMRs (promoters) considered in the sign test analysis: 6,283.

      (19) Line 371-372: What is the ASM/ASE concordance test? I thought you were restricting the analysis to genes with a negative association between ASM and ASE (lines 366-367), so this needs to be clarified.

      We have clarified this in the text. The two-step procedure works as follows: (1) a binomial sign test is applied to all genes with promoter ASM to identify gene sets with directional bias in methylation; (2) separately, a binomial sign test is applied to the subset of genes where ASM and ASE show a negative (repressive) relationship. Gene sets that pass both steps are reported as candidates. The "ASM/ASE concordance test" refers to step 2. We have revised the text to make this two-step logic clearer.

      (20) Line 379: It may be worth mentioning that these are the DMRs which are most likely to be functionally relevant in shaping expression levels.

      We have added this sentence: " This subset represents cases where methylation changes are most likely to have a simple and direct repressive effect on transcription, filtering out more complex regulatory scenarios where methylation and expression changes may be uncoupled or subject to competing regulatory influences."

      (21) Line 387: The test here needs to be clearer. Does a significant result mean an enrichment of differences in that gene set, or a bias in the ratio of Hu/Ch differences?

      We have clarified: a significant result from the binomial sign test indicates a statistically significant bias in the ratio of human-biased to chimpanzee-biased changes within a gene set, relative to the genome-wide background ratio. It does not test for enrichment of the number of differences, only for non-random directionality.

      (22) Line 403: Why the focus on expression, when the rest of the paper is focused on the methylation patterns?

      Gene expression is the most direct functional readout of promoter methylation changes. The two-step sign test uses expression data in the second step precisely because it allows us to identify cases where methylation divergence has a demonstrable downstream consequence on transcription, which is the canonical mechanism by which promoter methylation affects phenotype. We have added a brief justification of this rationale to the text.

      (23) Line 456: Not clear where there is actually evidence of lineage-specific selection.

      We have added an explicit sentence in the Discussion describing what the evidence consists of: "Specifically, the evidence rejecting a neutral null model of cis-regulatory evolution consists of statistically significant directional bias in both promoter methylation and gene expression within functionally coherent gene sets, assessed using a two-step binomial sign test with permutation-based FDR correction." This constitutes direct evidence that the implicated gene sets are under lineage-specific selection; the separate question of which specific human phenotypes that selection shaped remains inferential and is framed as such throughout.

      (24) Line 457-459: I think this line needs to be further explained: "Our use of hybrid cell lines was critical to this discovery, as it allowed us to isolate cis-acting regulatory changes from confounding trans-acting and environmental effects." Specifically, it's not apparent why cis-regulation is important for demonstrating evidence of selection.

      We have added an explanation: "Isolating cis-acting changes is critical because the sign test requires that each promoter represents an independent observation; in hybrid cells, each allele's methylation is determined by its own cis-regulatory sequence, making observations across promoters genuinely independent and thus satisfying the assumptions of the binomial test."

      (25) Line 460-465: The concluding claims throughout this paragraph appear to be overstated.

      We have revised the concluding paragraph of the Results and the Discussion conclusion to soften the language.

      (26) Line 487: Provide the actual numbers instead of saying "substantial".

      We have replaced "substantial numbers of allele-specifically methylated promoters" with the actual count: 6,283 allele-specifically methylated promoters across all cell types.

      (27) Line 502: I question this interpretation. While it could be that there is a shared mechanistic basis, it could also be that the cis effects tend to be larger than the trans effects, providing additional power to identify strong correlations.

      We agree and have added this alternative explanation explicitly to the Discussion (see response to public review comment above).

      (28) Line 510: But the results section states that it's not possible to interpret these as lineage-specific selection.

      The caveat at lines 399–401 applies specifically to DPSCs, not to hybrid cell types. We have revised the text to make this distinction unambiguous.

      (29) Line 601: What coverage was the methylation data?

      We have added sequencing coverage and the number of CpG sites assayed below “Bisulfite-seq library preparation, sequencing and mapping” section in Methods. WGBS libraries achieved a mean coverage of 9.68× per CpG site, covering 43.6M unique CpG positions in CNCC (hybrid) and 43.4M in CNCC (parental), 41.9M in DA (hybrid) and 38.8M in DA (parental). RRBS libraries achieved a mean coverage of 5.02× per CpG site, covering 5.0M, 4.8M, and 4.5M unique CpG positions in the hybrid HEP, IPSC, and SKM libraries respectively, and 3.3M, 3.4M, and 3.2M in the corresponding parental libraries. The total number of CpG sites (union) of all WGBS samples is 48,994,320 sites, and the union of all CpG sites of RRBS samples is 7,289,251. The union of all samples (including WGBS and RRBS) is 49,049,052. We have also included coverage information per sample as a table in Supplemental File 1.

      (30) Line 820: citation shouldn't include "preprint at".

      Corrected. "Preprint at" has been removed from all published paper citations in the reference list.

      Reviewer #2 (Public review):

      This manuscript investigates the causes and consequences of human-specific DNA methylation divergence relative to chimpanzees... This study provides a valuable dataset and a compelling framework for understanding how local sequence variation contributes to epigenetic and transcriptional divergence, with likely broad impact in comparative and evolutionary genomics.

      We thank Reviewer 2 for this positive assessment and for the constructive suggestions.

      Although the authors identify transcription factors associated with differential methylation, it is unclear what proportion of differentially methylated CpGs or DMRs can be attributed to these factors. Providing a quantitative estimate would help assess the relative contribution of trans-acting regulation.

      We agree that a quantitative estimate of the proportion of differentially methylated CpGs or DMRs attributable to these transcription factors would be informative in principle. In practice, however, such an estimate is challenging to produce reliably: predicted binding sites are not all occupied or functional, individual DMRs are typically influenced by multiple trans-factors, and we lack the per-site functional data needed to assign methylation differences to specific TFs with confidence. More importantly, even if we could generate such a number, an association-based estimate would not establish that these factors causally drive the observed methylation differences. We have added a note to the main text clarifying that our analysis identifies candidate trans-acting factors associated with differential methylation rather than quantifying their causal contribution.

      The analysis of CpG-disrupting mutations is interesting but raises two concerns. First, other classes of variants—such as transcription factor binding site-disrupting mutations—could also influence local methylation patterns and are not considered here. Second, the causal direction remains ambiguous: CpG-disrupting mutations may result from methylation-associated mutational processes (e.g., C->T transitions at methylated CpGs) rather than being the primary drivers of methylation divergence.

      We have addressed both concerns in the revised manuscript. On the first point, our goal was not to suggest that CpG-disrupting variants are the only causes of local methylation divergence. We now explicitly acknowledge in the Results that TFBS mutations and other variant classes could also contribute to cis-methylation divergence and represent an important avenue for future investigation. On the second point: while CpG-disrupting mutations are indeed expected to be enriched in highly methylated regions, they would be expected to associate with methylation level rather than methylation divergence, and thus cannot explain the patterns we observe.

      Regarding the discussion comparing the distance between CpG-disrupting SNVs and trans-DMRs, without information on the absolute or relative distance distributions, it was difficult to assess the magnitude of the observed differences. Moreover, trans-DMRs, by definition, are not driven by local (cis) variation, and the lack of proximity to CpG-disrupting SNVs is expected. Clarifying what additional insight this analysis provides beyond this expectation may improve this section.

      We agree that the lack of proximity of trans-DMRs to CpG-disrupting SNVs is expected. We have revised the text to clarify that this analysis serves as an affirming result: it is consistent with the fact that cis-DMR are under local sequence-driven regulation, and that the CpG-disrupting SNV mechanism is more closely associated to cis-DMRs than trans-DMRs. The quantifications for distance distributions are shown in Figure 3D, and we have added a sentence noting the median distances for trans-DMRs vs. cis-DMRs: 24 ± 6 bp vs. 11 ± 2 bp.

      One potential extension would be to examine whether the same cis-acting SNVs are consistently associated with methylation differences across multiple cell types.

      We thank the reviewer for this suggestion and have performed this analysis below. For each of the three regulatory region classes (promoters, enhancers, CTCF binding sites), we intersected CpG SNVs (±100 bp window) with cis-classified DMRs (pure_cis or cis_plus_trans at BH-corrected FDR < 0.05) across the five cell types (CNCC, DA, HEP, IPSC, SKM), and counted the number of cell types in which each SNV overlapped a cis-DMR. To assess significance, we compared this distribution to a permutation null in which, for each cell type, we randomly sampled the same number of regions from that cell type's pool of tested-but-conserved regions of the same class (1,000 permutations); SNVs were restricted to those falling within the tested universe across cell types.

      Local methylation effects of CpG SNVs were shared across cell types substantially more than expected by chance in all three region classes. The observed mean number of cell types sharing per SNV-in-cis-DMR was 1.244 vs. 1.077 ± 0.006 in the null for promoters, 1.133 vs. 1.042 ± 0.001 for enhancers, and 1.171 vs. 1.061 ± 0.002 for CTCF binding sites (all p < 0.001). Fold-enrichment scaled sharply with the degree of sharing: at the highest sharing level (cis-DMR in all five cell types), observed counts exceeded the permutation null by ~3,500-fold for promoters, ~800-fold for CTCF, and ~700-fold for enhancers. The slightly stronger consistency signal at promoters relative to enhancers is consistent with the more constitutive activity of promoter elements across cell types. These results indicate that the same cis-acting variants tend to drive methylation divergence across multiple cell types, supporting a shared mechanistic basis for cis-methylation divergence. We have added the figure in the main text as Figure 3—figure supplement 2.

      Regarding their two-step sign test analysis, because enrichment-based approaches can sometimes overemphasize statistical significance without reflecting effect size, I wonder if incorporating the magnitude of methylation change would provide additional information.

      We agree. The magnitude of methylation change (effect size) for each gene and gene set is now provided in Supplemental File 7 alongside the directional bias statistics. We have added a sentence to the Results pointing readers to this resource.

      Strength:

      I recommend that the authors provide a list of cis-cis-regulated promoters and their associated genes, which would be a valuable resource for the field.

      We have added this list as Supplemental File 8.

      Reviewer #3 (Public review):

      Ma et al. use human-chimpanzee tetraploid cells to examine species differences in DNA methylation... Both identified SNVs and transcription factors are good candidates for future experimentation. Further, they find that cis-DMRs are more highly correlated with cis-expressed genes than trans-DMRs with trans-expressed genes, providing evidence that methylation and expression are linked genome-wide.

      We thank Reviewer 3 for this summary and for the detailed recommendations.

      Weakness

      (1) Strengthening their cis/trans analysis, including: (a) only showing or analyzing genomic regions that pass FDR correction; (b) clarifying how cis genes are defined (Figure 2B shows some genes labeled as cis where the direction-of-effect differs between hybrid and parent cells); (c) assessing how well powered they are to perform each analysis.

      (a) Figure 2B has been updated to show regulatory classifications of promoter regions in cranial neural crest cells (CNCCs) at FDR < 0.05. Scatter plots and bar plots for all cell types at the level of individual CpG sites have been moved to Figure 2—figure supplement 1, and the corresponding promoter-level plots for all cell types other than CNCCs to Figure 2—figure supplement 2. We have clarified in the Figure 2—figure supplement 1 caption that nominal p-values are used to preserve the full dynamic range of the data, whereas FDR-corrected thresholds are applied for visualization of promoter scatter plots as well as all formal inference and for reporting significant candidate loci. FDR-corrected results are presented in Figure 2—figure supplements 1–2, and we have added explicit statements in the Results confirming that the cis: trans ratio is stable across FDR thresholds.

      (b) We have clarified the definition of cis-regulated genes in the text: cis-regulated genes are defined as those where the direction of allelic difference is consistent between hybrid and parental samples for both methylation and expression. We have verified that this definition is applied consistently throughout the manuscript and downstream analyses.

      (c) We have clarified the FDR correction approach for the sign test in the Methods: FDRs are estimated by permutation (10,000 permutations), and we report results at FDR < 0.25 for the two-step test with supporting evidence from the methylation-only sign test (nominal p < 0.05). We acknowledge that this is a relatively liberal threshold. The sign test itself provides direct evidence that the implicated gene sets are under lineage-specific selection; what we have toned down is the downstream interpretation, framing the link between these gene sets and specific human phenotypes as inferential and requiring experimental validation rather than as confirmed.

      (d) We agree that experimental validation would strengthen the mechanistic claims. We have added this explicitly to the Limitations section: "definitive demonstration of causality requires targeted experimental perturbations such as base editing (for CpG-disrupting SNVs) or TF knockdown/overexpression experiments (for trans-acting TFs)."

      (2) Softening claims about human evolution or human specificity for several reasons: (a) Their comparison lacks tetraploid controls (e.g. human-human tetraploids and chimp-chimp tetraploids) or experimental follow-up in diploid cells, making it hard to be certain that observed effects are not due to ploidy. (b) There are no outgroup species included in the analysis. (c) The use of no or very loose FDR corrections with the sign test makes it difficult to draw conclusions. (d) Experimental data to link SNVs to changes in cis methylation or identified transcription factors to changes in trans methylation would be needed to validate the authors' predictions.

      (a) The concern about ploidy effects is noted. We note, however, that the primary evidence for cis-regulation comes from allele-specific methylation within the same tetraploid nucleus, where both alleles experience identical ploidy and trans-environments. Ploidy effects would be expected to affect both alleles equally and would therefore not produce the allele-specific differences we observe. We acknowledge that single-species tetraploid controls would provide additional confidence and represent a valuable future experiment.

      (b) We have added the absence of an outgroup species as an explicit limitation in the Discussion.

      (c) We have clarified the FDR correction approach for the sign test in the Methods: FDRs are estimated by permutation (10,000 permutations), and we report results at FDR < 0.25 for the two-step test with supporting evidence from the methylation-only sign test (nominal p < 0.05). We acknowledge that this is a relatively liberal threshold and have emphasized this by adding a new sentence: “However, as indicated by the FDR, we do expect some fraction of these candidate gene sets to be false positives.”

      (d) We agree that experimental validation would strengthen the mechanistic claims. We have added this explicitly to the Limitations section: "definitive demonstration of causality requires targeted experimental perturbations such as base editing (for CpG-disrupting SNVs) or TF knockdown/overexpression experiments (for trans-acting TFs)."

      Reviewer #3 (Recommendations for the authors):

      (1) Why are dental pulp stem cells so different from the other cell types transcriptionally (e.g. Figure 1C)? Is this due to being primary cells vs. stem-cell-derived cells?

      The transcriptional distinctiveness of DPSCs is most likely attributable to their status as primary cells rather than iPSC-derived cells. Primary cells retain the epigenetic and transcriptional signatures of their tissue of origin and have not undergone reprogramming, whereas iPSC-derived cell types share a common pluripotent origin that may reduce inter-cell-type transcriptional distance. Additionally, DPSCs are mesenchymal stem cells with a distinct developmental lineage and were obtained from adult donors rather than differentiated in vitro, which may further contribute to their distinct profile. We have added a brief note to the Results acknowledging this.

      (2) I am concerned about how cis genes are defined. In Figure 2B, there are genes labeled as cis, where the direction-of-effect differs between hybrid and parent cells. I believe cis should only include genes with the same direction-of-effect between hybrid and parent cells, as illustrated in Figure 2A. This fix should propagate through the ensuing figures and results.

      We have clarified the definition of cis-regulated genes in the text (see response to Weakness 1b above). The classification framework assigns a site to "cis" when the allele effect test is significant in hybrids and the System × Allele interaction term is not significant, meaning there is no detectable change in the allelic difference between the hybrid and parental systems. Sites where the allelic difference genuinely differs between systems — that is, where the interaction term is significant — are classified as cis × trans (interactive) or cis + trans (additive) rather than pure cis, depending on whether the two systems disagree in direction or only in magnitude.

      We note that Figure 2B plots parental and hybrid methylation differences as the per-sample average difference in fractional methylation, which is used for visualization only. Points labeled cis that fall on the opposite side of the y = x diagonal are an artifact of this averaging: where the underlying difference is close to zero, the coverage-weighted per-sample average can flip sign even though the beta-binomial model, which fits the read counts directly and accounts for coverage and overdispersion, finds no significant interaction. The regulatory classification is based on the model, not on the sign of the averaged difference, so a small amount of scatter around the diagonal is expected. We have verified that this definition is applied consistently throughout the manuscript and downstream analyses and have clarified the caption of Figure 2B to make this explicit.

      (3) Are you equally powered to detect cis and trans effects?

      At the single-CpG level, the two hypotheses do differ in statistical power, but at the regional level this difference is mitigated by the higher effective read depth, and we now state this explicitly in the revised manuscript.

      The first hypothesis in our classification framework tests allele-specific methylation directly, whereas the second hypothesis includes an interaction term that evaluates whether allelic differences shift between the parental and hybrid systems. Because the interaction test is inherently less powerful, it requires greater sequencing depth and, ideally, additional replicates to yield comparably confident estimates and to assign sites to certain classification categories with significance. As a consequence, at the single-CpG level, trans effects are more sensitive to FDR thresholds than cis effects of equivalent nominal significance, which reduces our power to detect them. At the regional level, however, as well as in CpG-level analyses with high-coverage samples, this disparity in power between cis and trans largely disappears.

      This is the technical component of the issue. From a biological standpoint, cis effects are also intrinsically easier to detect than trans effects: estimates of trans effects necessarily incorporate not only trans-acting molecular mechanisms but also environmental and technical noise, so cis estimates will always be cleaner. This is a well-recognized limitation of existing cis/trans classification frameworks, and we acknowledge this limitation in the discussion and have added suggestions in experimental set-up to mitigate it. To address the reviewer's concern directly, we have performed a formal power analysis quantifying the relative power to detect cis and trans effects as a function of read depth (See Author response image 1).

      (4) Are the results shown for SNVs in CpGs in Figure 3C only for cis-DMRs or for all DMRs? If the latter, please show cis-DMRs and trans-DMRs separately and explain why trans-DMRs show the same pattern as cis-DMRs. In addition, I would expect that the CpG that contains an SNV leading to CpG loss or gain would be the most affected in terms of methylation status, rather than CpGs within 25bp vs. 50bp vs. 100bp. It would be helpful to see that plot as well.

      We thank the reviewer for the opportunity to clarify. Figure 3C is not an analysis stratified by cis-DMRs or trans-DMRs. Rather, it examines local methylation changes at conserved CpG sites located within 25 bp, 50 bp, and 100 bp of a CpG-disrupting SNV. The purpose of this analysis is to test a specific mechanistic hypothesis: that a CpG-disrupting mutation may influence the methylation status of nearby, intact CpG sites in cis. The analysis is therefore agnostic to cis/trans-DMR classification, as it asks a different question, namely whether sequence disruption at one CpG propagates locally to neighboring CpGs.

      We note that Figure 3D addresses a related but distinct question, showing that cis-acting sequence changes more broadly (not restricted to CpG-disrupting mutations) are more strongly associated with cis-DMRs than with trans-DMRs. Together, Figures 3C and 3D support complementary aspects of the cis mechanism: the local propagation of methylation changes around disrupted CpGs (3C) and the broader association of sequence variation with cis-DMRs (3D).

      Regarding the reviewer's second point: we agree that the CpG site directly disrupted by the SNV would itself be the most affected, by definition, since the CpG dinucleotide is destroyed (in the case of CpG loss) or newly created (in the case of CpG gain). Because methylation cannot be measured at a CpG that no longer exists (or has only just been created on one allele), this site cannot be included in a comparative methylation analysis across alleles or species. The 25/50/100 bp windows were therefore chosen specifically to test the local effect on conserved, measurable CpGs surrounding the disruption. We have clarified this rationale in the revised text/figure legend.

      (5) The finding that cis-DMRs and cis-expressed genes are more correlated than trans-DMRs with trans-expressed genes is nice to see. What is a potential explanation for why the patterns across the genomic interval surrounding the TSS are so different across cell types, and even positively correlated near the TSS in dopaminergic neurons? Why do you not see a difference between cis and trans in CNCCs? In addition, it would be nice to see the correlation between cis-DMRs and trans-expressed genes, and vice versa, as a control for these plots.

      We have added the suggested control analysis. For the cis-DMR/trans-expressed-gene and trans-DMR/cis-expressed-gene sets in both DA neurons and CNCCs, the correlations around the TSS are less consistently negative than for the cis-DMR/cis-expressed-gene set. In both cell types, cis-methylation and cis-expressed genes show the strongest opposing (negative) relationship to one another, which supports the specificity of the cis–cis coupling reported in Figure 4G. Regarding why the correlation profiles across the TSS-flanking interval differ so markedly across cell types—including the positive correlation near the TSS in dopaminergic neurons—and why the cis–trans distinction is less pronounced in CNCCs, we are not able to offer a confident explanation. The variation may reflect cell-type-specific regulatory architecture, but a great deal remains unknown about how methylation and transcription are coupled in a cell-type-specific manner, and our four cell types do not allow us to distinguish among the possible explanations. We think this is an open and interesting question, and that analyzing additional cell types with matched WGBS and gene expression data would be the most informative way to establish how general these patterns are and what drives the between-cell-type variation. We have noted this explicitly in the main text.

      Author response image 4.

      Spearman correlation of expression and methylation for CNCC and DA for subsets of genes with cis-regulated methylation and trans-regulated expression (orange), as well as genes with trans-regulated methylation and cis-regulated expression (blue). Two kb surrounding each transcription start site (TSS) is shown, split into 10 bins of 200 bp where individual CpG sites are pooled and averaged as fractional methylation values and correlated with expression values of the neighboring genes (in TPM).

      (6) The use of the sign test to identify pathways with the same direction of effect is a great approach. However, I am concerned with the use of no or very loose FDR corrections (e.g. FDR < 0.25 in line 372 and no FDR correction in line 374). Combined with Figure 6, where many of the signals appear to be weak or driven by a few genes (e.g. highly arched eyebrow and poor speech), it makes it difficult to draw robust conclusions. It is notable that the strongest signal is seen in DPSCs, which the authors note contains experimental confounds. We also think that the authors should tone down their biological interpretations, particularly for stem cells. For instance, COLEC11 is involved in neural crest cell migration but is identified from the iPSC analysis and not the CNCC analysis. Why not?

      We have added a sentence to emphasize the possibility of some false positive sign test results (“However, as indicated by the FDR, we do expect some fraction of these candidate gene sets to be false positives”), and we have toned down the biological interpretations accordingly.

      We want to clarify that the sign test directly demonstrates that these gene sets are under lineage-specific selection. We have clarified that the test does not establish a definitive link between these gene sets and specific human phenotypes; that link is inferential and would require experiments or further validation, and we have toned down the biological interpretations accordingly.

      Regarding COLEC11: in response to this comment, we directly examined COLEC11 expression and methylation in CNCCs and found that it is in fact significant in this cell type. In CNCC hybrid cells, COLEC11 shows significant chimpanzee-biased allele-specific expression (log2 fold change [human/chimpanzee allele] = –2.45; DESeq adjusted p = 0.005), together with significant human-biased methylation (fractional methylation [human – chimpanzee] = 14%; adjusted p < 0.001). The direction of this divergence is therefore consistent with IPSC. The reason COLEC11 did not surface at the pathway level in CNCCs is that other genes in the same pathway contribute to the directional signal for that cell type; we would not expect every individual gene to emerge in the cell type where its pathway is most relevant. We have added a note making this point and cautioning against over-interpreting any single gene example.

      (7) We appreciate that the authors provide a careful list of limitations of their study. In addition to the limitations listed, the authors should also include that experiments would be needed to validate that SNVs disrupting or creating CpGs affect methylation.

      We have added this to the Limitations section: “definitive demonstration of causality requires targeted experimental perturbations such as base editing (for CpG-disrupting SNVs) or TF knockdown/overexpression experiments (for trans-acting TFs).”

      (8) We also caution the authors in describing their findings as "human-specific" because there is no outgroup in this study.

      We agree and have added the absence of an outgroup as an explicit limitation in the Discussion.

      We thank all three reviewers again for their thorough and constructive engagement with our work. We believe the revised manuscript is improved as suggested.

    1. Author response:

      The following is the authors’ response to the original reviews.

      The goal of the study was to demonstrate the role of the two thresholds in learning, i.e. the role of metaplasticity with a learning rule that is both as simple as possible, but also biologically-based (hence the use of the detailed SPN model, as well). The goal was not to solve the FBP and NFBP with a different rule. However, the text likely gives that impression. Therefore, in addition to addressing the reviewers’ comments, the text has been substantially revised to reflect the following:

      Main results

      (1) Metaplasticity enables synapses that undergo both LTP and LTD to ultimately express just one plasticity outcome (either LTP or LTD).

      (2) Metaplasticity in the LTP threshold allows LTD to be expressed, and vice versa. (That is, the threshold regulating one plasticity process allows the expression of the opposite plasticity process.)

      Reason for using the FBP and NFBP

      The reason why the FBP and NFBP are particularly useful to demonstrate the thresholds’ roles is that the patterns in the tasks share features. (For example, in the FBP, the feature ‘strawberry’ is shared between both ‘red strawberry’ and ‘yellow strawberry’.) The synapses for these shared features experience precisely such competing LTP and LTD processes where the role of metaplasticity becomes evident. Specifically, the role of the LTD threshold is visible in shared synapses that need to be strengthened during learning (such as the shared ‘strawberry’ synapses in the FBP), while the LTP threshold’s role is visible in shared synapses that need to be weakened (there are no such synapses in the FBP, but there are in the NFBP, which is why it is needed in this article). In addition, feature binding is relevant for the striatum (now described in the introduction).

      In the first version of the article there are sentences that are likely confusing and misleading regarding the goal of the study, and these have been removed (lines 98-100 in the tracked changes file).

      The revised article now contains 4 new main figures and 15 new figure supplements prompted by the reviewers’ comments, thus expanding the scope of the study and hopefully clarifying its content, the mechanisms, and the conclusions.

      Finally, the question whether this rule can solve the NFBP with excitatory synapses alone is being addressed in a new, ongoing study, as written at the end of the Discussion section in the first version of this article. The new study tests 100+ SPN models (71 dSPN and 34 iSPN models differing in ion channel composition, with two different morphologies), different locations of the synaptic clusters along the dendrites (from proximal to distal), and two different learning regimes (suprathreshold – where the neuron initially spikes for all patterns, and subthreshold – where the neuron is initially silent for all patterns, as in this study) containing both clustered and distributed synapses in the same setup. Where necessary, preliminary results from this study are attached in the responses.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      This computational modelling study addresses the important question of how neurons can learn non-linear functions using biologically realistic plasticity mechanisms. The study extends the previous related work on metaplasticity by Khodadadi et al. (2025), using the same detailed biophysical model and basic study design, while significantly simplifying the synaptic plasticity rule by removing non-linearities, reducing the number of free parameters, and limiting plasticity to only excitatory synapses. The rule itself is supervised by the presence or absence of a binary dopamine reward signal, and gated by separate calcium-sensitive thresholds for potentiation and depression. The author shows that, when paired with a strong form of dendritic non-linearity called a "plateau potential" and appropriate pre-existing dendritic clustering of features, this simpler learning mechanism can solve a non-linear classification task similar to the classic XOR logic operator, with equal or better performance than the previous publication. The primary claims of this publication are that metaplasticity is required for learning non-linear feature classification, and that simultaneous dynamics in two separate thresholds (for potentiation and depression) are critical in this process. By systematically studying the properties of a biophysically plausible supervised learning rule, this paper adds interesting insights into the mechanics of learning complex computations in single neurons.

      As mentioned in the introductory response above, the goal of the article was not to solve the NFBP, but to study the role of metaplasticity. The text has now been substantially revised to reflect that. One of the primary claims that “metaplasticity is required for learning non-linear feature classification, and that simultaneous dynamics in two separate thresholds (for potentiation and depression) are critical in this process” is now removed from the abstract. Instead, the abstract now focuses on the main results regarding the role of metaplasticity, as well as the results which arose from addressing the reviewers’ comments. However, I guess I should note that to be able to study the role of metaplasticity using the FBP and the NFBP, it was first necessary to have a rule that solves these tasks – that allows to later observe the effects of systematically fixing or modifying parameters in the rule. Another aspect which may have added to the confusion about the study’s goal may be due to the NFBP being a complex task requiring supralinear dendritic integration. Because of this, plateaus have received significant attention in the article, possibly diverting from the main focus. This is also now clarified in the article.

      Strengths:

      The simplified form of the learning rule makes it easier to understand and study than previous metaplasticity rules, and makes the conclusions more generalizable, while preserving biological realism. Since similar biophysical mechanisms and dynamics exist in many different cell types across the whole brain, the proposed rule could easily be integrated into a wide range of computational models specializing in brain regions beyond the striatum (which is the focus of this study), making it of broad interest to computational neuroscientists. The general approach of systematically fixing or modifying each variable while observing the effects and interactions with other variables is sound and brings great clarity to understanding the dynamic properties and mechanics of the proposed learning rule.

      It would indeed be great if this rule facilitates similar studies in other neuron types. The rule requires at least qualitatively accurate calcium dynamics, which at the moment are not widely available for other neuron types (but will likely appear in the future).

      Weaknesses:

      General notes

      (1) The credibility of the main claims is mainly limited by the very narrow range of model parameters that was explored, including several seemingly arbitrary choices that were not adequately justified or explored.

      The parameter range has now been expanded to address all comments below.

      (2) The choice to use a morphologically detailed biophysical model, rather than a simpler multicompartment model, adds a great deal of complexity that further increases uncertainty as to whether the conclusions can generalize beyond the specific choices of model and morphology studied in this paper.

      Regarding the plasticity rule and the role of metaplasticity, the conclusions should hold if the calcium dynamics of other (simpler or detailed) neuron models is qualitatively similar (i.e. shows the same monotonicity of “stronger synaptic input – stronger calcium”, and not something like Figs. 12A, B for which the rule was not tested).

      As to whether the NFBP can be solved, that is being addressed in the new study with 100+ neuron models (71 dSPN models and 34 iSPN models, and two morphologies: one for the dSPNs and another for the iSPNs). So far, the results show that the important ingredient is the threshold nonlinearity provided by the plateau potential (both dSPNs and iSPNs exhibit this nonlinearity, irrespectively of where the synaptic cluster is located, see Author response image 1).

      Also, plateaus can be evoked in passive SPN dendrites (as stated in the methods in lines 916-919, by “turning off” ion channels in the computational model as in Fig. S7 of Du et al. (2017) (see list of references provided)). Although plateaus are somewhat modified by active conductances, the main behavior important for the NFBP is given by NMDARs. The most striking contributions of the other ion channels in SPNs are the low resting potential around -85 mV, delayed first spike under current injection and strong inward rectification. Basically, SPNs require more input to be stimulated compared to other neurons that lack these properties. So, other neurons with NMDAR-dependent nonlinearities should in principle be able to solve the same task, but perhaps needing less inputs (provided dendritic integration is sufficiently supralinear – see response to comment (2) under Reviewer #2 (Recommendations for the authors)).

      (3) The requirement for pre-existing synaptic clustering, while not implausible, greatly limits the flexibility of this rule to solve non-linear problems more generally.

      In my view, the limitation of this rule is that there is no mechanism for structural plasticity with which clusters could be “grown”. For example, Hedrick et al. 2022 demonstrate that during learning in the motor cortex, existing functional clusters are “enlarged” by growing new spines. Devising a biologically realistic rule for structural plasticity is a separate research project, which would be very interesting to do.

      In any case, to solve the NFBP with excitatory synapses alone, supralinear voltage elevations are necesssary (Tran-van-Minh et al. 2015). When it comes to NMDAR-dependent supralinear integration, clustering is basically necessary, within a smaller, e.g. 20 micron dendritic stretch, or more loosely, within a single dendritic branch (Losonczy and Magee, 2006; Branco et al. 2010). Also, synaptic clustering is quite present across different brain regions (such as the sensory and motor cortices, pallium, striatum, hippocampus, brainstem, the developing cortex, and across species, e. g. see the introduction of Kirchner and Gjorgjieva, 2021), so I suppose it is not that implausible. Inputs from motor cortex to striatum are also clustered (Hwang et al. 2022).

      (4) In order to claim that two thresholds are truly necessary, the author would have to show that other well-known rules with a single threshold (e.g., BCM) cannot solve this problem. No such direct head-to-head comparisons are made, raising the question of whether the same task could be achieved without having two separate plasticity thresholds.

      Although the goal of the study was not to solve the NFBP, this is a very interesting question related to the question “what is the use of having two separate thresholds for plasticity”? I have added simulations in which the rule is modified to use a single calcium threshold instead, showing that the FBP, NFBP, and reversal learning are solved just as well (Fig. 12 and Figure 12 – figure supplements 1 – 4). The results show that two calcium thresholds allow for separate control over the LTP and LTD processes (lines 687-706).

      Specific notes

      (1) Regarding the limited hyperparameter search:

      (a) On page 5, the author introduces the upper LTP threshold Theta_LTP. It is not clear why this upper threshold is necessary when the weights are already bounded by w_max. Since w_max is just another hyperparameter, why not set it to a lower value if the goal is to avoid excessively strong synapses? The values of w_max and Theta_LTP appear to have been chosen arbitrarily, but this question could be resolved by doing a proper hyperparameter search over w_max in the absence of an upper Theta_LTP.

      Thank you for raising this question – it is closely related to the very important question of when to stop updating the weights. Before providing the response, I should clear up any confusion made due to an error in notation. In this study, , and , meaning that during learning the weights can increase up to twice (up to 100% of) the initial value, and can decrease down to 1% of the initial value. Currently, it says w<sub>max</sub> = 2, and w<sub>min</sub> = 0.01, which is a mistake, and possibly a reason why the chosen values seem arbitrary.

      The reason for introducing the upper threshold θ<sub>LTP</sub> is most easily seen in the parameter scan for w<sub>max</sub> done in the absence of θ<sub>LTP</sub> (Figure 4 – figure supplement 4) – it is very difficult to choose a value for w<sub>max</sub> with which all three tasks will be solved (FBP with linear integration, i.e. distributed synapses, the FBP with supralinear integration, i.e. clustered synapses, and the NFBP). Put differently, if there is a range of w<sub>max</sub> values which solves all three tasks, it is very narrow. So, θ<sub>LTP</sub> is introduced to solve all three cases without specially tuning w<sub>max</sub>.

      The following is a description of the results in Figure 4 – figure supplement 4, which is also present in the article in lines 383-396. The reason why a single preset value for w<sub>max</sub> does not work is that distributed synapses sum only linearly at the soma, while clustered synapses sum supralinearly. This means that to trigger somatic spiking, the distributed synapses need to be strengthened more compared to clustered synapses. Concretely, this means that a is needed to solve the FBP with linear integration (distributed synapses), but it is already too strong to solve the NFBP (Figure 4 – figure supplement 4, column four: top panel shows that FBP with linear integration is solved, while the bottom panel shows the average performance for the NFBP is right at the border – pink line aligns with the dashed line). On the other hand, is enough in the FBP with clustered synapses and the NFBP to trigger glutamate spillover and a plateau potential, which drives somatic spiking (Figure 4 – figure supplement 4, column two). However, it is not enough to solve the FBP with linear integration. Larger values for w<sub>max</sub> increase the performance on the FBP with linear integration, but lower the performance on the NFBP due to spiking for the irrelevant patterns (especially visible once ). As said, in this parameter scan, only the value solves all three tasks, with borderline performance on the NFBP (it is arguable whether the borderline performance means the NFBP is solved). This suggests that if a range of values for w<sub>max</sub> exists which solves all three tasks, it is very narrow.

      With the settings used in the study, the w <sub>max</sub> threshold for triggering glutamate spillover is a number between 1.2 and 1.3 with many decimals – 1.230769231. A possibility could be to program spillover to always occur at , but this is also not a general solution. For example, other dSPN models from the model library in Lindroos et al. (2021) have different excitability, and that would mean a different, specific value of w<sub>max</sub> would be needed for each neuron model.

      θ<sub>LTP</sub> is thus a solution that prevents “over-excitation” in a dendrite. The logic is that synapses in a cluster do not need to be as strong as distributed synapses to be effective in exciting the neuron. θ<sub>LTP</sub> ensures that once plateaus appear, synapses are not strengthened further. This allows using the same value across all scenarios, i.e. avoiding tuning of w<sub>max</sub> or tuning the number of synapses representing the features. (Also, preliminary results show this works well in the new study which tests all dSPN and iSPN models in the model library.) As for the value of θ<sub>LTP</sub>, it can be set anywhere in the “blank” region in Fig. 2C<sub>3</sub> where the supralinear jump in [Ca]<sub>NMDA</sub> occurs. What is important is that [Ca]<sub>NMDA</sub> evoked by a plateau should be above θ<sub>LTP</sub> – then no more strengthening will occur once plateaus can be evoked.

      (b) The author does not explore the effect of having separate learning rates for theta_LTP and theta_LTD, which could also improve learning performance in the NFBP. A more comprehensive exploration of these parameters would make the inclusion of theta_max (and the specific value chosen) a lot less arbitrary.

      I am not sure I have understood this comment properly, but hopefully this response addresses it adequately. In fact, the computer code does use separate variables for the learning rates for θ<sub>LTP</sub> and θ<sub>LTP</sub>, but for simplicity, they are set to the same value. In this response I have included some simulations in which they are set to different values (Author response image 2), but to understand their effect it is better to read the response to the comment under c) first. The metaplasticity rates determine how fast the synaptic weights are stabilized, i.e. how long the time window is where the synapses are “flexible”. When the thresholds reach the calcium amplitudes, the weights are “locked”.

      If the metaplasticity rates are too low, the weights take a longer time to stabilize and solving the tasks takes a long time (Figure 4 – figure supplement 10 from the response to c). If they are too high, weights are quickly stabilized and, in the case of weakened synapses, prematurely so, leading to worse performance on the NFBP due to spiking for the irrelevant patterns. (Figure 4 – figure supplement 11).

      One can use different values for the metaplasticity rates, as in the examples in Fig. 2 , and this affects the speed of learning. A large η<sub>θLTD</sub> = 20 quickly prevents the LTD process (Figs. 2D<sub>1</sub>, D<sub>2</sub>), causing faster synaptic strengthening, but also quickly limiting weakening (Figs. 2B<sub>1</sub>, B<sub>2</sub>) – as a result, after learning, the neuron spiked for an irrelevant pattern (Fig. 2A<sub>1</sub>). Conversely, a large η<sub>θLTD</sub> = 20 quickly prevents the LTP process (Figs. 2C<sub>3</sub>, C<sub>4</sub>), prolonging synaptic strengthening and allowing faster weakening (Figs. 2B<sub>3</sub>, B<sub>4</sub>) – as a result, the NFBP is solved, but takes a longer time. However, this does not remove the need for using an upper threshold θ<sub>LTP</sub>. If I have not understood the comment properly, please let me know so I can address it further.

      (c) Figure 4 Supplements 3-4: The author shows results for a hyperparameter search of the learning rule parameters, which is important to see. However, the parameter search is very limited: only 3 parameter values were tried, and there is no explanation or rationale for choosing these specific parameters. In particular, the metaplasticity learning rates do not even span one order of magnitude. If the author wants to claim that the learning rule is insensitive to this parameter, it should be explored over a much broader range of values (e.g., something like the range [0.1-10]).

      Thank you for bringing this up! I have expanded the parameter scan for both the learning rate η (Figure 4 – figure supplements 7 and 8) and the metaplasticity rate η<sub>θ</sub> (Figure 4 – figure supplements 10 and 11) to cover three orders of magnitude (when taken together with the results already present in the article in Figure 4 – figure supplements 6 and 9).

      Figure 4 – figure supplements 7 and 8: The learning rate η was was tested with the values 0.1 and 20. This shows a known result in other plasticity rules, which is that if the learning rate is too fast or too slow, learning is not successful or is too slow. For η = 0.1, learning takes very long (around 2000 patterns for FBP with linear integration), and for the NFBP is at the borderline score (Figure 4 – figure supplement 7E). As the LTD thresholds rise, they will prevent the slowly decreasing synaptic weights from decreasing sufficiently. For η = 20, the weight updates are too large and no pattern is stored because calcium quickly falls below the thresholds as a result of such large weight updates (Figure 4 – figure supplement 8E). This leaves some intermediate range of learning rates that “works”. (The three values {0.4, 0.85, 1.7} that were tested in Figure 4 – figure supplement 6 are roughly a factor of 2 apart.) Results are described in more detail in lines 409-414 of the revised article.

      Figure 4 – figure supplements 10 and 11: The metaplasticity rate η<sub>θ</sub> was tested with the values 0.2 and 20. This further demonstrates the role of metaplasticity as a “lock” on the learning process. η<sub>θ</sub> determines how fast the weights stabilize (i.e. how long they remain flexible for learning). With the value η<sub>θ</sub> = 0.2 the weights take a longer time to stabilize, because it takes a long time for the thresholds to reach the calcium amplitudes (Figure 4 – figure supplement 10). This affects the learning time on the NFBP only. In contrast, with the value η<sub>θ</sub> = 20, the thresholds quickly reach the calcium amplitudes, and quickly stabilize the weights. While the neuron does learn to evoke plateaus, the weakened synapses are stabilized too early, resulting in spikes for the irrelevant patterns and lowering the performance on the NFBP. (Figure 4 – figure supplement 11). Results are described in more detail in lines 415-429 of the revised article.

      (2) Regarding the similarity to BCM, the author would ideally directly implement the BCM learning rule in their model, but at the least the author could have shown whether a slight variant of their rule presented here can be effective: for example having a single (plastic, not fixed) Cadependent threshold that applies to both LTP and LTD, with a single learning rate parameter.

      - As mentioned above, this is also a very interesting question, related to the important question of “what is the use of having two separate calcium thresholds?”. I have added simulations according to your second suggestion – using a single calcium threshold that applies to both LTP and LTD. A single threshold can solve the FBP, NFBP, and reversal learning equally well (Fig. 12 and Figure 12

      - Figure Supplements 1, 2). This indeed raises the question what are two separate thresholds useful for? Figure 12 – figure supplement 3 shows that when keeping the single calcium threshold fixed, none of the shared synapses stabilize. Comparing this to Figs. 5 and 6, where the LTP and LTD threshold are kept fixed one at a time, it shows that having two separate thresholds allows separate control over the LTP and LTD processes.

      I also tried an implementation of the BCM rule using a nonlinear (quadratic) function in the metaplasticity rule for updating the threshold:

      where c<sub>norm</sub> is a normalization constant set to 80 μM for [Ca]<sub>NMDA</sub> and 20 μM for [Ca]<sub>L-type</sub> (close to the maximal concentrations achieved throughout the article). In the BCM rule, a nonlinear function is necessary to prevent runaway growth (or collapse) of the weights. So, in principle, w<sub>max</sub> and θ<sub>LTP</sub> should be unnecessary with this quadratic metaplasticity rule. However, even though the weights seem to stabilize (around a high value), they are too strong and plateaus are triggered for all patterns (see Author response image 3). It is possible that only a narrow range of parameters in the quadratic function will allow weights to stabilize at appropriate values, similarly to the narrow range in w<sub>max</sub> in the absence of θ<sub>LTP</sub> (as described for comment 1a) above).

      Below are some questions about how to “correctly translate” the BCM rule from its formulation for rate-coded inputs to a formulation for sparsely-coded inputs which are used in this article. I did not address these questions in detail. The following is meant for readers who might be interested in pursuing these questions.

      Questions when translating the BCM rule for rate-coded inputs to a rule for sparsely-coded inputs:

      The similarity of this study’s rule to BCM is only qualitative – a sliding threshold was added that follows an indicator of synaptic activity (in this study it is the amplitude of the calcium concentration). The original BCM rule is defined for rate-based synapses, and its threshold θ is a nonlinear function of the average (synaptic) activity:

      where p and c<sub>0</sub> are positive constants, and c) is the average activity. The threshold θ is updated as the average activity c) changes (the averaging being done over a time interval) [1]. Changes in the rate-coded inputs drive changes in c) continuously, thus changing θ over time.

      (1) What should be chosen as the average activity c̅ ?

      In the BCM model, the average activity, and consequently the threshold θ, are global for the whole neuron (which is represented just by its firing rate), meaning that θ is the same for all synapses. In a morphologically realistic neuron model, what should be the average activity? Especially in the case of supralinear integration occuring in a dendrite, one could also consider average activities in dendrites. In the dSPN model, the calcium concentration decays by the time the next pattern arrives, so one probably needs another, low-pass filtered variable of the calcium concentration (or voltage), with a much longer time constant than that of the calcium decay. (I have chosen to slide the thresholds towards the amplitude of the calcium evoked by a pattern, which could be viewed as an approximation of such a long-lived variable. This is one possible “translation” of this aspect of the BCM rule.)

      (2) How to update the chosen indicator of activity c̅?

      Assuming an adequate indicator is chosen (different from the calcium amplitude that I have chosen), how should it be updated when using sparsely-coded inputs? Should it evolve continuously, or only when the sparsely-coded inputs are active? If updated continuously, it should not decay very fast when synapses are inactive (not activated by a pattern), while still change fast enough to detect changes in synaptic weight occuring due to learning. (I have chosen to slide the thresholds towards the evoked calcium amplitude only when synapses have been activated, so this is also one way of “translating” this second aspect.)

      (1) which in the BCM article is replaced with the average over the input’s probability distribution

      (3) What nonlinear function to use to update the threshold?

      The BCM rule allows any function with p > 1, but how fast the synapses stabilize will likely depend on c<sub>0</sub>, the normalization constant in the nonlinear function, and the power p. The role of the nonlinear function is to ensure stability of the synaptic weights (prevent runaway growth), meaning no θ<sub>LTP</sub> nor w<sub>max</sub> should be needed. However, achieving high performance on all three tasks might still require a specific tuning of these parameters, as w<sub>max</sub> does if no θ<sub>LTP</sub> is used. That is, these parameters will need to be chosen such that the threshold quickly goes up once a plateau appears, so weights are not allowed to strengthen further. Having in mind that there is a very narrow range in w<sub>max</sub> where all three tasks are solved, there might similarly be only a narrow range in c<sub>0</sub> and p.

      Since the goal of the article was to study the role of the two thresholds (not to optimize the rule’s parameters on the three tasks), I have only tried a quadratic function for the metaplasticity rule, and did not search for a region of parameters that could work.

      (3) This paper is extremely similar (and essentially an extension) to the work of Khodadadi et al. (2025). Yet this paper is not mentioned at all in the introduction, and the relation between these papers is not made clear until the discussion, leaving me initially puzzled as to what problems this paper addresses that have not already been extensively solved. The introduction could be reworked to make this connection clearer while pointing out the main differences in approach (e.g., the important distinction between "boosting" nonlinearities and plateau potentials).

      The last paragraph in the introduction now makes this comparison, highlighting the differences in approach, and mainly emphasizing that the goal of the two studies is different. The open question that this study addresses is to pinpoint the roles of the two calcium thresholds (present in dSPNs) in learning. Also see the response to the similar comment (1) from Reviewer #2 (Public review): Weaknesses.

      (4) The introduction is missing some citations of other recent work that has addressed single-neuron non-linear computation and learning, such as Gidon et al (2020); Jones & Kording (2021).

      Thank you for mentioning this. Since the first version of the article caused confusion regarding the goal of the study (which is to study metaplasticity), I avoided focusing on nonlinear computation in the introduction, and instead added these references to the Discussion (in line 850 the section regarding nonlinear computation).

      (5) Figure 1: The figure prominently features mGluR next to the CaV channel, but there is no mention of mGluR in the introduction. The introduction should be updated to include this.

      Thank you for noticing this. It is now included in the introduction in lines 50-53.

      (6) Could the author explain why there is a non-monotonic increase/decrease in the [Ca]_L in Figure 2B_4? Perhaps my confusion comes from not understanding what a single line represents. Does each line represent the [Ca] in a single spine (and if so, which spine), or is each line an average of all the spines in a given stim condition?

      Thank you for noticing this, that information was missing from the figure caption. The line is from a single spine which is placed at a random location on a randomly chosen dendrite. Because each line comes from a different trial with a different number of synapses, the spine it corresponds to is in a different location, resulting in different voltage and different calcium signals when using distributed synapses. (Clustered synapses are placed at approximately the same somatic distance, despite being on a randomly chosen dendrite, so this effect does not appear in Figs. 2C<sub>3</sub>, C<sub>4</sub>). The figure caption has been updated accordingly.

      (7) Row 124 (page 4): L-type Ca microdomains (in which ions don't diffuse and therefore don't interact with Ca_NMDA) is a critical assumption of this model. The references for this appear only in the discussion, so when reading this paper, I found myself a bit confused about why the same ion is treated as two completely independent variables with separate dynamics. Highlighting the assumption (with citations) a bit more clearly in the results section when describing the rule would help with understanding.

      Thank you for pointing this out! This assumption is now clearly stated with citations in lines 174176 when characterizing the plateaus in SPNs, and lines 205-207 when describing the rule (in addition to the existing description in the Methods).

      (8) Row 149 (page 5): The current formulation of the update rule is not actually multiplicative. The fact that the update is weight-dependent alone does not make it a multiplicative rule, and judging by equation (1) it appears to simply be an additive rule with a weight regularization term that guarantees weight bounds. For example, a similar weight-dependent update is also a core component of BTSP (Milstein et al. 2021; Galloni et al. 2025), which is another well-known *additive* rule. An actual multiplicative rule implies that the update itself is applied via a multiplication, i.e. w_new = w_old * delta_w

      For an example of a genuinely multiplicative rule, see: Cornford et al. 2024, "Brain-like learning with exponentiated gradients"). Multiplicative rules have very different properties to additive rules, since larger weights tend to grow quickly while small weights shrink towards 0.

      Thank you for explaining the difference between “additive” and “multiplicative”. I have removed the word “multiplicative” from the description of the rule, as it is not necessary. (In the first version of the manuscript I followed the nomenclature by Gütig et al. (2003), which refers to the weight-dependent update as a multiplicative rule, while an additive rule has no weight dependence in the equation for Δw, which is Eq. 2 in Gütig et al. (2003).)

      (9) Equation 1 (page 5): Shouldn't the depression term be written as: (w_min - w)? This term would be negative if w is larger than w_min, leading to LTD. As it is written now, a large w and small w_min would just cause further potentiation instead of depression.

      Yes, a minus sign is missing in front of the depression term. Thank you for noticing this! It is now corrected.

      (10) In the introduction, the teaching signal is described in binary terms (DA peak, or DA pause), but in Equation 1, it actually appears to take on 3 different values. Could the author clarify what the difference is between a "DA pause" and the "no DA" condition? The way I read it, pause = absence of DA = no DA

      Yes, the “no DA” condition should say “baseline DA”. The DA signal does indeed take three different values. In the striatum, there is a baseline tone of dopamine. The DA peaks are transient increases from this tone, and the DA pauses are transient decreases. The basal dopamine level is now introduced in line 113 of the introduction, so that Eq. 1 should be clearer. In the computer code, DA is in effect a ternary signal, with three values, +1 for DA peak, -1 for DA pause, and 0 for baseline DA.

      (11) Figure 3: In these experimental simulations, DA feedback comes in 400ms after the stimulus. The author could motivate this choice a bit better and explain the significance of this delay. Clearly, the equations have a delta_t term, but as far as the learning algorithm is concerned, it seems like learning would be more effective at delta_t=0. Is the choice of 400ms mainly motivated by experimental observations? On a related note, is it meaningful that the 200ms delta_t before the next stimulus is shorter than the 400ms pause from the first stimulus? Wouldn't the DA that arrives shortly before a stimulus also have an effect on the learning rule?

      These time windows were chosen purely to keep the simulations as short as possible (since a computing cluster was used to run many trials). In reality, two patterns would probably arrive after a longer time window, as an animal should reach for the pattern (and in the case of these fruit patterns, eat it) which would last on the order of seconds. However, the calcium signals that trigger plasticity in these simulations are shorter than that (Figs. 2B<sub>3,4</sub>, 2C<sub>3,4</sub>), and only the amplitude of the signal is used to trigger plasticity. This gives an opportinity to not have to wait for several seconds between two patterns arrive (as might occur in reality), but shorten that interval and so shorten the simulation time. (This is now stated in lines 245-247 in the Results section where the rule is described, pointing to the Methods for more detials.)

      Hence, the dopamine feedback is given at 400 ms after a pattern appears because the calcium amplitudes would have surely occurred by then (even if a plateau were evoked, see Figs. 2B<sub>3,4</sub>, 2C<sub>3,4</sub>). Similarly, the next pattern is given at 600 ms because the calcium signals would have decreased to baseline by then. (This is already explained in the Methods section in lines 1101-1117). The key implicit assumption here is that the calcium amplitude is somehow remembered by the synaptic circuitry. In experiments, dopamine feedback up to 2 seconds after synaptic stimulation can cause LTP, so it is OK to assume this (Yagishita et al., 2014). However, dopamine signaling before synaptic stimulation has no effect (Yagishita et al., 2014). (This assumption is now clearly stated in the Methods in lines 902-906.)

      Lastly, in this rule, if the dopamine feedback coincides with the pattern, then whatever calcium levels were reached at that time would be used to check whether the thresholds are crossed, and these will most likely not be the maximal calcium levels (these are reached some time later, as seen in Figs. 2B<sub>3,4</sub>, 2C<sub>3,4</sub>).

      One last note is that from your comment I got the impression that you may have understood Δt to be the time until dopamine feedback is provided. It is not, it is simply the time step in the simulation (already stated in line 211; now an additional explanation is added in lines 211-214, just in case).

      (12) Figure 4C: How is it possible that the theta_LTP value goes higher than the upper threshold (dashed line)? Equation 3 implies that it should always be lower.

      This is also just a choice of implementation: θ<sub>LTP</sub> evolves independently of θ<sub>LTP</sub>, reflecting an implicit assumption that different molecular machinery implements θ<sub>LTP</sub> and θ<sub>LTP</sub>. This assumption is similar to the findings in Figs. 4, 5 in Ngezahayo et al. 2000, where in weakened synapses the voltage threshold for LTD can increase (to -20 mV) above the voltage threshold for LTP (at -30 mV). (This assumption is now explicitly written out in lines 316-322.)

      (13) Row 429 (page 11): The statement that "without metaplasticity the NFBP cannot be solved" is overly general and not supported by the evidence presented. There exist many papers in which people solve similar non-linear feature learning problems with Hebbian or other bio-plausible rules that don't have metaplasticity. A more accurate statement that can be made here is that the specific rule presented in this paper requires metaplasticity.

      Yes, that is what is meant with that statement – that this specific rule requires metaplasticity. The text has been corrected. Thank you for noticing this.

      (14) The methods section does not make any mention of publicly available code or a GitHub repository. The author should add a link to the code and put some effort into improving the documentation so that others can more easily assess the code and reproduce the simulations.

      The link to the code is given in the Data availability statement. However, this statement might not appear in the manuscript files that you are receiving (it is available online and in the article PDF downloadable from eLife), so I am providing the link here, as well. The Readme.md file now describes the code, and how to reproduce figures in the article.

      https://github.com/danieltrpevski/Plasticity/tree/metaplasticity

      Reviewer #2 (Public review):

      Summary:

      The manuscript proposes interesting synaptic plasticity rules grounded in experimental data. Its main features are:

      (1) plasticity depends on local calcium concentration driven by presynaptic activity and is independent of somatic action potentials,

      (2) the rules incorporate metaplasticity, and

      (3) they demonstrate how a single neuron could address the feature-binding problem at the dendritic level.

      The work extends a previous study (https://doi.org/10.7554/), to which the author also contributed.

      The author models two calcium thresholds (LTP/LTD) from two different calcium sources (NMDA/VGCC), and these thresholds are flexible (metaplasticity rule, similar to BCM), which is claimed to be necessary for successful learning of both FBP and NFBP (linear and nonlinear feature binding problem with 1 or 2 patterns). The role of each threshold seems to be opposite and complementary. One extra condition has been added: an upper threshold for LTP. This threshold serves to stop synaptic strengthening once synapses are strong enough to evoke a plateau. With that, synapses are not strengthened to the maximal value, avoiding strong supralinear integration for irrelevant patterns.

      This is summarizes the learning rule well. What I should probably add is that, as mentioned in the introductory response, the article’s first version may cause some confusion about the study’s goal. The goal was to study the role of metaplasticity in the two thresholds, not to solve feature binding in particular. Nevertheless, feature binding is a very useful task to demonstrate the roles of each threshold because the patterns share features: the synapses for the shared features experience both LTP and LTD, and metaplasticity is necessary to express (or to converge to) just one plasticity state (either LTP or LTD). More specifically, the threshold for one plasticity process (e.g. LTD) is necessary to express the opposite process (e.g. LTP). However, to be able to study metaplasticity using feature binding, a prerequisite is to have a rule that can solve it. (So, in that sense, it was first necessary to show that the rule solves the tasks before exploring the roles of metaplasticity. The article has been revised to clearly state this.)

      Strengths:

      The current model implements not only local synaptic plasticity but also metaplasticity and solves the FBP at the dendrite level. Another strong aspect of the model is that metaplasticity in the LTD threshold protects strengthened synapses from weakening. In this way, as the author mentioned, metaplasticity is able to protect learned patterns from being forgotten or weakened and prevent irrelevant patterns from being stored. This is a nice modelling example of metaplasticity being helpful in preventing the catastrophic interference or forgetting (as has been explicitly discussed in a recent article https://doi.org/10.1016/j.). The author might want to briefly mention or emphasize this aspect of the model, which might be interesting also for the AI community.

      This is a great suggestion, thank you! I have instead emphasized a related aspect of the model: that it can solve the plasticity-stability dilemma (when taking away the closed-loop implementation of metaplasticity). I did not focus on catastrophic forgetting, because in machine learning it has a slightly more specific meaning: forgetting that occurs in sequential learning of different tasks. Instead, I exemplified the plasticity-stability dilemma using reversal learning (the reward policy is switched in the middle of the simulation), which can be viewed as a special case of sequential learning of opposite tasks. So, strictly speaking, there is no demonstration that metaplasticity prevents catastrophic forgetting (in the more general sense), but there is a demonstration that it retains (stabilizes) what has been learned (within the same task). The latter does suggest that metaplasticity could help prevent catastrophic forgetting, as well.

      Weaknesses:

      (1) What is novel in the current paper as compared to Khodadadi et al. eLife 2025? That is not completely clear and should be made clearer. Is it only a minor difference related to the fact that the new learning rule has metaplasticity in both calcium thresholds and is simpler? This seems to be just an incremental increase in knowledge/methods. Can the author defend his paper against this point from the „devil's advocate"? How is the conclusion of the author in the abstract that „metaplasticity in both thresholds is necessary" reconcilable with his previous publication (Khodadadi et al. eLife 2025), in which only metaplasticity in one threshold was successful in solving the nonlinear feature binding problem?

      Thank you for raising this question, since the answer was not clear in the first version. The study may be an incremental increase in methods, but is (in my view) a solid increase in knowledge, giving concrete new insights into metaplasticity (an area that is still comparatively little understood). The two main conclusions are:

      (1) In synapses that are exposed to both the LTP and the LTD process, metaplasticity is necessary to ultimately express just one of them (converge to either LTP or LTD).

      (2) Metaplasticity in the threshold regulating one plasticity process is necessary for expressing the opposite process (metaplasticity in the LTD threshold is necessary for expressing LTP, and vice versa).

      The article has been substantially revised to clearly state these main conclusions (as well as the study’s goal), while a full list of all conclusions is given in points 1-7 the Discussion.

      The conclusion in the abstract that „metaplasticity in both thresholds is necessary" is stated too generally, and it was meant to refer to this rule only. I have now removed it from the abstract, since the study’s goal was not to solve feature binding. Instead, the focus is on the two conclusions above as well as other conclusions obtained from expanding the study with reversal learning and using a single threshold (prompted by the comments from yourself and reviewer #1).

      Lastly, the differences compared to Khodadadi et al. 2025 (eLife) are:

      (1) Yes, the rule is simpler and has metaplasticity in both calcium thresholds, instead of just one in Khodadadi et al. 2025 that operates according to a different mechanism (where the threshold, along with the entire LTP plasticity kernel, moves in a direction opposite of the calcium signal).

      (2) Plateau potentials are used here, versus the “boosting” nonlinearities in Khodadadi et al. 2025.

      (3) The most detailed calcium diffusion model to date for SPNs is implemented in this study (by Dorman et al. (2018)). This was a necessary addition to avoid non-monotonous increases in calcium (shown in Fig. 13A, B). No calcium diffusion between neuronal compartments is implemented in Khodadadi et al., 2025. This is indeed a small methodological difference, but not trivial to implement.

      The relation to Khodadadi et al., 2025 is now stated both in the introduction in lines 137-144, and at greater length in the discussion in lines 856-870.

      Perhaps I should note that the two learning rules (this one and that in Khodadadi et al. 2025) developed in parallel, this one being based on formulations similar to Gütig et al. 2003 by adding metaplasticity, while the rule in Khodadadi et al. 2025 was inspired from the ideas in Schiess et al. (2016) and Urbanczik and Senn (2014) (see list of references provided). The two studies have different goals (and in that sense one was not meant to be an extension of the other):

      - Khodadadi et al. (2025) studies whether the NFBP can be solved by SPNs,

      - this article studies the role of metaplasticity in the two calcium thresholds that exist in dSPNs; it uses feature binding as a task because the role of metaplasticity is exposed precisely by the shared features in the task (they cause shared synapses to undergo competing LTP and LTD, and metaplasticity is necessary to direct synapses into just one outcome); importantly, feature binding is also relevant for the striatum (now described in the introduction in lines 126-136)

      Finally, to obtain the conclusions in this study about the roles of the two thresholds, it was necessary to devise a suitable rule. They cannot be obtained neither with the rule in Khodadadi et al. 2025, nor with any other rule, because none have a formulation with two separate thresholds for LTP and LTD. Phrased more generally, one needs a new/different rule (new/different assumptions) to obtain new/different conclusions, even if the new rule may be related to existing ones. That said, a rule with a single threshold would have reached conclusion 1. above, as is now shown in the article in Fig. 12 and Figure 12 – figure supplements 1 – 4, but SPNs have two thresholds, prompting the use of a rule with two thresholds. Also, although not demonstrated with the cascade model (by Fusi et al. (2005) and its extensions), conclusion 1. should be obtainable with it, and is implied by the dynamics of the cascade model (which uses one threshold to control transitions between strong and weak synapses). More on the cascade model is given below and in the revised article.

      Hopefully that provided a clearer answer. If you have more questions, please let me know so I can try to clarify further.

      (2) As far as I can judge without testing the model, metaplasticity causes thresholds to monotonically increase during systematic pattern presentation, which stabilizes weights and allows pattern separation. Due to the closed-loop nature of the current implementation, where metaplasticity only happens if plasticity happens, this also effectively locks patterns in place. However, flexible learning is an essential mechanism for survival. Imagine a mutation event takes place and bananas suddenly become red and/or strawberries turn yellow. It seems that the current model would be unable to adapt to these new patterns even if rewards were to be shifted. While out of the scope of the study, due to its importance, I feel that pattern shifting/relearning should at least be briefly discussed. How could the model be improved to allow relearning?

      This is a very important question, and I think it is in fact within the scope of the study, so it is now addressed using reversal learning as a task (the reward policy is switched in the middle of the simulation, after the FBP and NFBP are learned). As you pointed out, the closed-loop formulation of metaplasticity effectively locks the patterns in the dendrites, and reversal learning cannot be solved (Fig. 9). On the other hand, if the conditions for metaplasticity are relaxed by allowing any calcium levels to trigger metaplasticity (i.e. no longer have a closed-loop formulation requiring that [Ca]<sub>NMDA</sub> or [Ca]<sub>L-type</sub> be above their thresholds), reversal learning in both the FBP and NFBP is solved (Fig. 10 and Figure 10 – figure supplements 1 – 3). (Note that [Ca]<sub>NMDA</sub> or [Ca]<sub>L-type</sub> still need to be above their thresholds for plasticity to occur.)

      Recommendations for the authors:

      Reviewing Editor Comments:

      While the reviewers were very positive, they highlighted limitations on the strength of evidence. Addressing these points could help revise this assessment.

      Reviewer #1 (Recommendations for the authors):

      (1) Framing the problem as "feature binding" is easy to understand, but it's a slightly narrow view of learning in general. Some mention of how NFBP relates to the XOR problem in the introduction would help you relate your solution to the much broader class of computational problems, since XOR is a more fundamental computational primitive. Non-linear feature learning is very general and relates to all machine learning problems and to computations that occur across every brain region.

      Since the goal of the study was not to solve the NFBP or feature binding (but to study metaplasticity), the relation of the NFBP to the XOR is put in the Discussion instead (to avoid further confusion about the study’s goal). Nevertheless, this connection is clearly made in the introduction of the new study that uses 100+ SPN models.

      (2) Since the requirement for clustered synapses is one of the main limitations of this learning rule, it would help if there were some discussion of how clustering might occur (e.g., whether there are any other related learning rules or mechanisms that might promote clustering, or if you are assuming that this has to occur entirely through developmental wiring).

      This is now discussed in lines 817-827 and related to developing a learning rule that would incorporate structural plasticity.

      (3) Page 5, row 157: Another potentially relevant citation here is Bittner et al. 2017, showing that a dendritic plateau potential in silent CA1 neurons drives place field formation without any prior spiking activity.

      Thank you, that is indeed a very relevant citation here! It is now added in line 222.

      (4) Figure 4C: It would be helpful to add a sentence in the figure legend explaining what the dashed lines represent (even though you also mention it in the main text).

      Added, thank you!

      (5) Across all figures, the author should consider using color combinations that are more colorblindfriendly (e.g., cyan/red). As a R/G colorblind person, I find it slightly difficult to see which line is which in the panels that compare scores in the NFBP.

      The panels showing the NFBP scores have been changed throughout the article, and all other figures have been checked. If there are any more difficult color combinations, please let me know.

      (6) The conventional, widely used abbreviation for dopamine is "DA", not "Da".

      Now changed.

      (7) A few typos I spotted in the paper:

      (a) Row 117 (page 3): missing parenthesis around citation

      (b) Row 173 (page 5): "uner" --> under

      (c) Row 248 (page 7): repeated sentence "...are first seen above..."

      (d) Row 255 (page 7): "NBFP" --> NFBP

      These are now fixed, thank you for reporting them!

      Reviewer #2 (Recommendations for the authors):

      (1) How are synapses distributed in the nonlinear integration case? Are pattern combinations branch-specific, or are features distributed randomly across the whole dendritic tree? Does this matter in any way? In any case, it should be clarified.

      Yes, they are branch-specific. In the NFBP, the feature combinations from Figure 3 – figure supplement 1 (and later from Figure 10 – figure supplement 1) are placed on two dendrites, chosen at random from 8 dendrites, in a 20-micrometre dendritic stretch starting around 120 micrometers away from the soma. 12 different trials are run for each feature combination, meaning that 12 randomly chosen pairs of dendrites were tested for each feature combination. In the FBP, the clusters are placed in one dendrite chosen at random from 8 dendrites, at the same distance from the soma as in the NFBP. This information is now added in the caption of Fig. 3.

      The idea behind placing clusters on the same dendrite is that, after learning, two strong clusters will produce a plateau (e.g. ‘red’ and ‘strawberry’), while one strong and one weak cluster will not (e.g. ‘yellow’ and ‘strawberry’), as in Figs. 3C<sub>2</sub>, 3C<sub>3</sub> (with the weights shown in Figs. 4B<sub>2</sub>, 4B<sub>3</sub>). For this the clusters need to be in the same branch, so that two features are “bound” together “into” a larger, plateau-evoking cluster. Also, a strong and a weak cluster should evoke a sufficiently lower somatic amplitude so that any additional noise will not cause somatic spiking. This is assured by the large voltage jump in the plateau (the all-or-none quality of the plateaus, Fig. 2D<sub>1</sub>).

      If the clusters are distributed randomly on different dendrites, it might or it might not work. Fig. 10 of Oikonomou et al. (2012) shows that dendritic spikes (that individually do not evoke somatic spiking) summate sublinearly at the soma in pyramidal neurons: weak + weak cluster = no spiking (Fig. 10A); strong + strong = no spiking (Fig. 10B); but also strong + strong = spiking (Fig. 10C). To reliably solve the NFBP, a large enough supralinearity is necessary instead, so one should test how the soma integrates dendritic spikes/plateaus in SPNs. As the goal of this study was not to solve the NFBP, this is left for the future (perhaps within the new ongoing study focusing on the NFBP).

      (2) To produce dendritic plateau potentials, the model (as in the previously published model - Trpevski et al. 2023) implements glutamate spillover activating extrasynaptic NMDARs. This is an interesting mechanism, but is there empirical evidence supporting this way of generating plateau potentials? Are synaptic NMDARs not sufficient? If not, which experiments support the role of nonsynaptic ones?

      This is still an ongoing area of research, indicating that glutamate spillover is regulated by reuptake from glial cells, which could even reverse function and excrete glutamate (Rusakov and Stewart, 2021; Malarkey and Parpura, 2014).

      Except for the experiments from Szapiro and Barbour, 2007 showing that climbing fibers in the cerebellum signal to molecular-layer interneurons exclusively through glutamate spillover, there are no other “in-vivo-like” experimental conditions which show that spillover activates extrasynaptic NMDARs (eNMDARs). The strongest other in vitro data come from the following experiments:

      (1) Chalifoux and Carter (2011), where glutamate reuptake by transporters was blocked with TBOA, which promoted NMDA spikes evoked by synaptic stimulation, suggesting that glutamate spillover activates eNMDARs. A similar experiment was done in Suzuki et al. (2008), where, in addition, synaptic NMDARs were blocked, leaving only eNMDARs available to trigger plateaus.

      (2) Glutamate iontophoresis, which ejects glutamate directly into the extrasynaptic space, activates plateaus once the iontophoretic current is strong enough (Oikonomou et al., 2012), with or without blocking glutamate reuptake (Suzuki et al. 2008).

      (3) Repetitive synaptic stimulation is thought to produce glutamate spillover (Suzuki et al. 2008; Oikonomou et al., 2012). For example, two synaptic shocks trigger NMDA spikes, while 5 synaptic shocks trigger plateaus in pyramidal neurons (Oikonomou et al., 2012).

      On the other hand, studies that employ glutamate uncaging at spines, which should activate eNMDARs much less, evoke NMDA spikes instead (Losonczy and Magee, 2006; Branco et al. 2010). Compared to plateaus, these have much smaller amplitudes, and the size of the supralinearity (the voltage jump) is much smaller than in the plateaus obtained with glutamate iontophoresis (compare Fig. 3 in Losonczy and Magee, (2006), Fig. 3B in Branco et al. (2010) to Fig. 4C in Oikonomou et al. (2012), Fig. 6 in Oikonomou et al. (2014)).

      The reason why glutamate spillover was implemented is precisely this robust all-or-none quality of the plateaus, i.e. the large jump in somatic voltage (Fig. 2D<sub>1</sub>) after a threshold level of stimulation (when the stimulus intensity increases in equal amounts). Without spillover, plateaus are graded in amplitude (and duration, Fig. 2B<sub>1</sub> in Trpevski et al. (2023)), and the NFBP cannot be solved (Fig. 6 in Trpevski et al. (2023)).

      (3) The check for dependence on initial conditions of theta_LTP/LTD is missing. Especially for the conditions of the thresholds being fixed. How do you decide what fixed value to use? How about having a corresponding limit for weights and not for thresholds? Why is there still an increase in threshold going on even when weights reach the maximum?

      The initial conditions for θ<sub>LTP</sub> and θ<sub>LTD</sub> are also an important question. The idea behind starting with low values of the thresholds (or fixing them to low values) is to make the synapses flexible for learning. One can view metaplasticity’s role as a “lock” on the weights, locking them once learning is done, and unlocking them (making them flexible) when something needs to be learned. Which signals determine when to lock or unlock the weights is what the metaplasticity rule implements, and is insufficiently understood experimentally. In any case, it makes sense to start with flexible synapses (low thresholds) at the beginning of learning; otherwise, no/little learning will take place (Figure 9 – figure supplement 2, the panels for “thresholded” metaplasticity). Throughout the article I choose the initial values of the thresholds to be lower than the calcium evoked by weakened synapses, ensuring that any calcium signal will trigger plasticity (but higher values also work).

      Instead of doing a scan over the initial conditions of θ<sub>LTP</sub> and θ<sub>LTD</sub>, I chose to show the following:

      (1) An example with initial threshold values higher than the calcium amplitudes: these “lock” the weights (Figure 9 – figure supplement 2, panels for “thresholded” metaplasticity) from the start and no learning can occur.

      (2) An example initialized with high values for the thresholds, but where metaplasticity can be triggered by any calcium amplitudes (no closed-loop in the metaplasticity rule, Figure 9 – figure supplement 2, panels for “relaxed” metaplasticity): here the thresholds adapt and learning can take place afterwards.

      This is supposed to illustrate a mechanism that can “unlock” weights. A scan over the initial conditions of θ<sub>LTP</sub> and θ<sub>LTD</sub> will give the lowest calcium level that the thresholds can be initialized to so that “thresholded” metaplasticity will work. But it is not important to know these precise values to obtain the conclusions in the article, which is why I did not do such a scan. (The above is treated in the article in the section on reversal learning, lines 569-577 and 628-633.)

      Also, when the rule is used for learning, it is not meant to have fixed thresholds, as synapses cannot stabilize and nothing will be stored (Figs. 5, 6, and 8). Fixing the thresholds to a low value was meant to show what happens without any metaplasticity (or if metaplasticity were “dysfunctional”). If in reality a mechanism exists to fix the thresholds to a low value or a high value, fixing would be temporary (until necessary to keep the weights flexible or locked, respectively). 

      I am probably not understanding this part of the comment: “How about having a corresponding limit for weights and not for thresholds?” There are two limits, the maximal and minimal weights in the rule w<sub>max</sub> and w<sub>min</sub>, and are initialized to random values within the interval [0.3, 0.35], but this is probably not what you mean.

      When the weights reach their maximum, the thresholds still increase because they have not reached the calcium amplitudes evoked by the maximal weights. (This is most visible with supralinear integration, where strengthened weights evoke plateaus Fig. 4C<sub>2</sub>-C<sub>4</sub>.) The thresholds move towards the calcium amplitudes with a rate η<sub>θ</sub>, which if made very high (as in Figure 4 – figure supplement 11), will make the thresholds rise as fast as the weights. But this is not good, as it will “lock” the learning processes in the synapses too soon (i.e. shorten the window where they are flexible). Neither is a too low η<sub>θ</sub> good, as then the synapses are flexible for a very long time and learning of the NFBP is prolonged (Figure 4 – figure supplements 10B<sub>3</sub>, 10B<sub>4</sub>, 10E<sub>3</sub>, learning simulations last longer than in Fig. 4).

      (4) Calcium modelling: The author writes that the largest voltage plateaus do not correspond to the largest calcium amplitude because of the plateau's voltage approaching the NMDAR reversal potentials, which might be a problem for the plasticity rule. To solve this, the author tried to implement a monotonic increase of calcium with increasing plateau by implementing axial calcium diffusion and buffering. My question is, is the monotonic increase realistic? Is not the NMDAR reversal effect, described above, a realistic scenario in dendrites?

      It seems to be realistic. The closest experiment that I know of is in Fig. 2C<sub>2</sub>, D<sub>2</sub> in Oikonomou et al. (2012), where 2 synaptic shocks produce an NMDA spike, and 5 shocks produce a plateau. The calcium dye shows a higher response from the plateau, suggesting a higher calcium amplitude (with a monotonic increase). Moreover, in the detailed calcium model for SPNs by Dorman et al. (2018), larger synaptic clusters produce monotonically higher calcium amplitudes. These two pieces of evidence suggest the calcium amplitudes are not affected by the membrane voltage approaching to the reversal potential. Most likely, this happens because of strong intracellular calcium buffering.

      Similarly, the experiments in Figs. 5 and 8 in Losonczy and Magee (2006) with glutamate uncaging at spine heads show a monotonic increase in calcium dye flourescence as the cluster size is increased. However, these experiments evoke NMDA spikes, which might not have approached the NMDAR reversal potential as closely as plateaus do (so, it is theoretically possible that monotonicity does not hold if a plateau were evoked, although it seems unlikely). This is now added to the Methods in lines 957-961.

      (5) Function: What is the actual function of the SPN, and how does it relate to FBP/NFBP learning? SPNs are involved in motor control/decision making and generally in sensorimotor tasks. Rather, use an example for that than a visual stimulus, though I understand it is more easily illustrated. Is feature binding what SPNs do and have to solve?

      It is not known yet what SPNs do precisely. The initial action selection role of the basal ganglia is currently being challenged or replaced by a role in movement initiation and/or invigoration (with action selection being done by the cortex, see e.g. Thura and Cisek (2017)). In any case, SPNs receive convergent input from sensory, motor, limbic and associative areas, as well as thalamic and neuromodulatory inputs (with topographical projections indicating functional specialization). In that sense, feature binding is particularly relevant for the striatum, as diverse features from different areas would arrive there. The basal ganglia participate in non-motor loops as well, so the striatum may have a role in initiation and termination of cognitive processes such as planning and attention, and in regulating emotional and motivated behavior (Purves et al. 2018).

      The role of the striatum and the relevance of feature binding is now stated in the introduction in lines 126-136, and a task with features more suited for the striatum is given in Figure 1 – figure supplement 1 (inspired from similar tasks in Bernklau et al. (2024)). I have kept the example from the visual system in the main text simply because it is widely used throughout the literature and easily recognizable, while clearly stating that other features would be involved in the striatum and pointing to the example in Figure 1 – figure supplement 1. Hopefully this will make a good compromise between ease of reading and relevance to the striatum.

      (6) The population of striatal projection neurons can express dopamine D2 receptors and not only D1 receptors. SPNs with different receptors thus undergo synaptic plasticity according to different rules. Would that lead to similar results? A combination of both populations?

      This is also being tested in the new study, and preliminary results indicate the answer is “yes” (see Author response image 4). Contrary to the dSPNs, the indirect-pathway SPNs (iSPNs), which predominantly express D<sub>2</sub> receptors, are thought to be involved in suppressing competing or related movements. The learning rule is almost the opposite to dSPNs: to trigger LTP, a dopamine pause is needed, and to trigger LTD a dopamine peak is needed (Fig. 4B and Shen et al. (2008)). So, with such a rule, iSPNs will store the irrelevant patterns and spike to them, and be silent to the relevant patterns (which indeed happens after learning in Author response image 4F<sub>2</sub>, F<sub>3</sub>). This aligns well with their role to suppress movements – reaching for the irrelevant patterns will be suppressed, while reaching for the relevant patterns will be disinhibited (the indirect pathway inhibits movement initiation). 

      (7) Other synaptic plasticity & metaplasticity models (possible comparison or discussion): https://pubmed.ncbi.nlm.nih./ https://linkinghub.elsevier.(https://link.springer.com/ For example, in the last model, there is only one modification LTP/LTD threshold, but it is different from the voltage threshold (which would be comparable to calcium thresholds in the current paper - see the voltage threshold different from the modification threshold here: https://doi.org/10.1371/). The modification threshold favors LTP or LTD - depending on the previous spiking activity of the cell and effectively works as an anti-Hebbian firing rate „homeostasis" mechanism. How is the firing rate homeostasis maintained in the current paper/model? Can you explain how this model is related to the previous models of Benuskova and Abraham, and also Clopath (there was also a metaplasticity version of the Clopath model), in terms of firing rate stability? The current model implements not only local synaptic plasticity but also metaplasticity, which is a nice feature, and seems to not only solve the FBP but also maintain firing stability. Is the stability of firing a consequence of the hard bounds for synaptic weights, or is it also a consequence of plasticity and metaplasticity? I like that each synaptic weight is changed independently based on local calcium concentration, with its own LTP and LTD thresholds.

      I will first describe what happens to the firing rate in this model, and then compare with the references you mentioned. In the FBP with linear integration, yes, the firing rate stability is only maintained because of the hard bounds for synaptic weights (Figure 4 – figure supplement 5A<sub>1</sub>, the neuron goes into depolarization block without w<sub>max</sub>). Without w<sub>max</sub>, the weights would grow until [Ca]<sub>NMDA</sub> saturates in the spine (which does not happen for most spines within the simulation time in Figure 4 – figure supplement 5B<sub>1</sub>).

      In the FBP with supralinear integration and the NFBP, the weights are prevented from increasing by the upper threshold for LTP, θ<sub>LTP</sub>. If θ<sub>LTP</sub> and w<sub>max</sub> are gone, synapses also grow without bound (Figure 4 – figure supplement 5B<sub>2</sub>). Regardless of how high the synaptic weight becomes, firing rate stability is ensured by the plateau potential, as the maximally achievable voltage is limited by the NMDAR reversal potential (Figure 4 – figure supplement 5A<sub>2</sub>, a somatic depolarization block does not happen as in Figure 4 – figure supplement 5A<sub>1</sub>). This is part of the plateaus’ function to provide dynamic range compression, as shown experimentally in Figs. 3E, 4D and 12 in Oikonomou et al. (2012). (Of course, such high weights are unrealistic, but they happen in the model without w<sub>max</sub> and without θ<sub>LTP</sub>). This is now described in the text in lines 397-407.

      Regarding the other studies, the second link did not work, so I will refer to Jedlicka et al. (2015), Clopath et al. (2010) and Zenke et al. (2013). (The rule in Jedlicka et al. (2015) is the same as in Benuskova and Abraham, (2007) but with a more detailed neuron model.) In these studies, there is a threshold representing a (weighted) average of the postsynaptic activity (postsynaptic voltage or spiking). In Clopath et al. (2010) and Zenke et al. (2013) it modulates only the amount of LTD, while in Jedlicka et al. (2015) it modulates the amounts of both LTP and LTD that occur due to plasticity. The threshold is global for a neuron (i.e. all synapses use the same threshold), and allows for heterosynaptic effects that compensate increased excitation from synaptic strengthening with stronger weakening in depressed synapses (thus maintaining stable firing rates). (However, the rule in Jedlicka et al. (2015) and Benuskova and Abraham, (2007) has only one threshold, there is no separate voltage threshold. Indeed, the threshold is a low-pass filtered variable of the input spike train, so is similar to calcium concentration.)

      There are no such effects in the current learning rule. Some compensatory effects are visible when comparing supralinear integration with and without an upper threshold θ<sub>LTP</sub>, as e.g. in Fig. 4B<sub>2</sub> and Figure 4—figure supplement 3B<sub>1</sub>. With θ<sub>LTP</sub>, synapses do not increase to w<sub>max</sub>, and without it, they do. As a consequence, the weakened synaptic cluster is weakened less when using θ<sub>LTP</sub> (‘yellow’ synapses in Fig. 4B<sub>2</sub>), and more without θ<sub>LTP</sub> (‘yellow’ synapses in Figure 4—figure supplement 2B<sub>1</sub>). The increased weakening in the latter case is because the strengthened ‘strawberry’ synapses have reached w<sub>max</sub>, and contribute to spiking for the irrelevant pattern (‘yellow strawberry’). As a result, the weakened ‘yellow’ synapses have to decrease more so no spiking for the irrelevant pattern occurs. In effect, the increased strengthening in the ‘strawberry’ synapses drives increased weakening in the ‘yellow’ synapses. However, this is a result of the task structure, i. e. that the patterns share features, and not from the learning rule.

      The above is briefly explained in the Discussion in lines 778-786.

      (8) The last sentence in the discussion is a bold claim: SPN can completely solve NFBP alone. Is that statement too strong, or is it a sign of multiple different mechanisms implementing the same function (i.e., degeneracy)?

      The sentence was not meant to be a bold claim. It currently says:

      “This indicates that ... SPNs might completely solve the task ... Whether this is true will be explored in another study …”

      I have now toned this claim down, as the purpose was only to point to the new study that explores this question (using with 100+ SPN models, in two learning regimes and varying cluster location). Nevertheless, the preliminary results in the new study suggest that SPNs can indeed solve the NFBP (if the plateaus are all-or-none), so I agree that it is a sign of multiple mechanisms implementing the same function.

      Figures/Table:

      (1) Figure 2: The layout of the figure is confusing. B shows distributed input as in upper A, and C shows clustered input as in lower A. This should be illustrated better (e.g., as in Figure 3 or 4). The term cluster size is confusing as well because it also refers to the distributed inputs; better use the number of synapses here. The color choice is difficult, as similar colors are chosen for cluster size and for differentiating linear and nonlinear integration in D.

      Thank you for the detailed comments! The figure has been reworked accordingly.

      (2) Figure 4: C What are dashed lines?

      They indicate the upper threshold for LTP, θ<sub>LTP</sub>.Thank you for noticing this, it is now added in the figure caption, and in other figures where it was missing.

      (3) Figure 5 and Figure 6: B is missing.

      These figures have been reworked to match the revision of the text describing the role of metaplasticity in the shared synapses. Now, the FBP is described first, followed by the NFBP, so the figures have been merged with their figure supplements (where the FBP results used to be in the first version).

      (4) Figure 4 Supplement 1: What do the colors and regions mean in B3? Why show here and not for others?

      The main text in lines 311-312, 331-333, and 358-359 refers to these regions when explaining the dynamics of the calcium, the thresholds and the weights (e.g. the pink region shows that [Ca]<sub>L-type</sub> in the ‘strawberry’ synapses evoked by ‘yellow strawberry’ is much lower than the calcium threshold for ‘strawberry’, protecting these synapses from weakening). They are simply highlighted with different colors, so readers know precisely where to look when reading the main text. The figure caption has been updated to state this.

      Also, the figure caption says that the same regions exist in all panels, although they have not been highlighted. I could have chosen any panel to mark these regions, and I chose B<sub>3</sub> because it looked like it had the least visual clutter.

      (5) Table 1: Typo for LTD

      Now fixed.

      (6) Line 21: „thehsold"

      Now fixed.

      (7) Line 50: Closing parentheses missing.

      Now fixed.

      (5) Line 55: "All metaplasticity models so far have only one modifiable threshold". This is not true as it stands. Multiple sliding thresholds have been proposed before:

      - experimentally by Ngezahayo et al. (2000)

      - multiple pathways reviewed by Abraham (2008)

      - multiple structural LTP thresholds observed experimentally by Ueda et al. (2022)

      - models of synaptic states and cascade models can be considered to employ multiple thresholds (depending on state); e.g., Fusi et al. (2005)

      Thank you for providing these references! The sentence has been changed (it was supposed to refer only to computational models), and the studies have been added in the text where appropriate.

      Importantly, Fusi et al. (2005) is now being discussed throughout the text, as it contains important results and conclusions about metaplasticity which are used as comparison. (In the first version of the article I did not include it because I was not sure about the interpretation of the thresholds – strictly speaking there is only one plasticity threshold (q, determining whether a synapse will switch sign), while the other is a metaplasticity threshold (p, determining whether the synapse will change its metaplastic state). However, the precise number of thresholds is not as important, as the study’s results are relevant to compare with.)

      (9) Lines 117/118: Missing parentheses around reference.

      Fixed.

      (10) Line 140: "a small difference". I feel like "small" is a bit of an understatement here, as from what I can see, the differences are almost a magnitude -- see blue/black traces in Figure 2B4 vs. 2C4.

      Thank you for noticing this. It was meant to refer only to the amplitude of the somatic voltage when the cluster size is small (in Fig 2D<sub>1</sub>). The text has been clarified now.

      (11) I think it's unnecessary to rewrite Eq. 1 in Eq. 3.

      I decided to keep this.

      (12) Lines 181-183: It would probably still be useful to show that NFBP can't be solved by distributed inputs.

      It is now shown in Figure 4 – figure supplement 1, and briefly described in the text in lines 298300.

      (13) Line 210: Typo, double "(the"

      Fixed, thank you.

      (14) Lines 248-249: Typo, double partial sentence.

      Now fixed.

      (15) Line 760: The year in the „STDP rule endowed with the BCM sliding threshold accounts for hippocampal heterosynaptic plasticity" should be corrected to 2007. Also, all other references should be checked for mistakes and missing pages, etc. (see e.g., also line 882).

      Thank you for noticing this! The references have been checked.

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      Author response image 1.

      Plateau potentials (A1, B1) and their somatic amplitudes in dSPNs (A) and iSPNs (B) when the location of the synaptic cluster is varied. Distally evoked plateaus have a smaller somatic amplitude in both dSPNs and iSPNs, bust still exhibit a nonlinear jump in the somatic voltage. In (A2, B2) all 71 dSPN and 34 iSPN models were tested, color coded with respect to their excitability to a synaptic cluster of 10 synapses.

      Author response image 2.

      Two learning simulations on the NFBP where different metaplasticity rates for LTP and LTD were used. (Top) The metaplasticity rate for LTD is higher, stopping the LTD process prematurely (D1, D2), resulting in less weakening of the synapses (B1, B2) and spiking for one irrelevant pattern (A1). (Bottom) The metaplasticity rate for LTP is higher, preventing frequent synaptic strengthening(C1, C2). As a result, it takes a longer time for synapses to strengthen and trigger plateaus (B3, B4).

      Author response image 3.

      Learning on the NFBP with a nonlinear (quadratic) metaplasticity rule, which implements the BCM rule. (A) Somatic and dendritic voltage before and after learning. (B-D) Evolution of synaptic weights (B), LTP (C) nad LTD thresholds (D). Weights in (B) seem to stabilize around a high value once the LTP threshold reaches the maximal [Ca]NMDA; however, the value is too high and triggers plateau potentials for all patterns.

      Author response image 4.

      Learning to solve the NFBP in one dSPN and one iSPN model. (A, B) Schemes describing the requirements for cortico-striatal synaptic plasticity in dSPNs (A) and iSPNs (B). (C) Dopamine peaks are emitted from the midbrain after the relevant patterns, and dopamine pauses after the irrelevant patterns. (D) Stimulation protocol. (E, F) A single learning simulation in a dSPN (E) and an iSPN (F) model. Before learning the neurons spike to all patterns (due to additional feature-unspecific distributed inputs, shown with the third panels in E3, F3). After learning, the dSPN spikes only for the relevant patterns (E2) and the iSPN only for the irrelevant ones (F2). (E3, F3) The evolution of clustered and distributed synptic weights (In dendrite 1 of the iSPN, the synapses for 'red' experienced some strengtheneing after being weakened, but this does not seem to affect learning in this example.) The neurons in th enew study receive less background synaptic input than in the current article, and additional distributed synapses are needed along with a plateau for somatic spiking, making for a more challenging learning scenario.

    1. Author response:

      The following is the authors’ response to the original reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      In this study, the authors elegantly combined latent variable models (i.e., HMM, GPFA and dynamical system models) with a calcium imaging observation model (i.e., latent Poisson spiking and autoregressive calcium dynamics (AR)).

      Strengths:

      Integrating a calcium observation model into existing latent variable models improves significantly the inference of latent neural states compared to existing approaches such as spike deconvolution or Gaussian assumptions.

      The authors also provide an open-source access to their method for direct application to calcium imaging data analysis.

      Weaknesses:

      As acknowledged by the authors, their method is dependent on the quality of calcium trace extraction from fluorescence videos. It should be noted that this limitation applies to alternative strategies.

      While the contribution of this study should prove useful for researchers using calcium imaging, the novelty is limited, as it consists of an integration of the calcium imaging model from Ganmor et al. 2016 with existing LVM frameworks.

      Reviewer #2 (Public review):

      Summary:

      This compelling study proposes a framework to implement latent variable models using population level calcium imaging data. The study incorporates autoregressive dynamics and latent Poisson spiking to improve inference of latent states across different model classes including HMMs, Gaussian Process Factor Analysis and nonlinear dynamical systems models. This approach allows for a more seamless integration of existing methods typically used with spiking data to apply on calcium imaging data. The authors test the model on piriform cortex recordings as well as a biophysical simulator to validate their methods. This approach promises to have wide usability for neuroscientists using large population level calcium imaging.

      Strengths:

      The strengths of this study are the flexibility in the choice of models and relatively easy adaptation to user-specific use cases.

      Weaknesses:

      The weakness of the study lies in its limited validation of biological calcium imaging data. Calcium dynamics in a task-specific context in a sensory brain region might be very different from slower dynamics in a region of integration. The biophysical properties of the data would also be dependent on the SNR of the imaging platform and the generation of calcium indicator being used.

      Reviewers 1 and 2 correctly point out that our method depends on the quality of the upstream calcium trace extraction. As they noted, these traces can vary based on the specific indicator used, the signal-to-noise ratio (SNR) of the recording, and the region of the brain being imaged (such as sensory vs. integrative areas). As Reviewer 1 rightly mentions, this is a universal challenge that applies to alternative strategies as well, rather than a limitation unique to our framework. To address these points, we have added a paragraph to our Discussion section.

      Reviewer #3 (Public review):

      Summary:

      S. Keeley & collaborators propose a computational approach to infer time-varying latent variables directly from calcium traces (for instance, obtained with 2p imaging) without the need for deconvolving the traces into spike trains in a preliminary, independent step. Their approach rests on 1 of 3 families of latent models: GPFA, HMM and dynamical systems - which they augment with an observation model that maps latent variables to fluorescence traces. They validate their approach on simulated and real data, showing that the approach improves latent variable inference and model fitting, compared to more traditional approaches (although not directly compared with the 2-step one; see below). They provide a GitHub repository with code to fit their models (which I have not tested).

      Strengths:

      The approach is sound and well-motivated. The authors are specialists in latent variable models. The manuscript is succinct, well-written, and the figures are clear. I particularly liked the diversity of latent models considered, in particular latent models with continuous (GPFA) vs.

      discrete (HMM) dynamics, which are useful for characterizing different types of neural computations. The validation on both simulated and real data is convincing.

      Weaknesses:

      One advantage … is that one can inspect the quality of the deconvolution step independently from the latent variable inference step. For instance, if the inferred latent variables are not interpretable, how can one determine whether this is due to a poor choice of latent model (e.g., HMM with too few states), or a poor fit of the observation model (e.g., wrong parameters for the calcium dynamics)?

      We agree with the reviewer that integrating the calcium likelihood introduces additional parameters that require careful diagnostics. However, for the vast majority of imaging datasets, there is no simultaneous electrophysiology to verify the deconvolution step. If the final latent states are not interpretable, it remains impossible to determine whether the error originated in the initial spike inference from deconvolution or the subsequent model fitting.

      Our framework addresses this by maintaining the raw fluorescence as the fixed observation. We suggest for those using this model to employ cross-validation using this data to select model parameters. We outline how to do this below, but because the data itself does not change with each model fit, you can compare P(data | λ) across any model configuration. In contrast, different deconvolution methods change the data itself (the spiketimes) making comparison across models impossible.

      Could the authors comment on whether their approach allows for instance to compare different forms of latent models (e.g., HMM vs. GPFA) in terms of model evidence, cross-validated log-likelihood or other model comparison metrics?

      We thank the reviewer for highlighting this. In short: yes. Because our framework integrates the calcium observation likelihood with various latent variable models, we can assess held-out prediction P(data | λ) irrespective of the specific latent structure.

      However, because fitting the LVM requires inferring the latent state z to determine the firing rate λ, proper cross-validation across models involves holding out both neurons and timepoints. A principled approach—which our framework supports—is as follows:

      (1) Train both the latent states z and the model parameters (e.g., the mapping from latent space to observations) on a training portion of the recording.

      (2) On a held-out test segment, withhold a subset of "test" neurons and infer the latent states using only the "held-in" neurons.

      (3) Calculate the likelihood of the observed fluorescence for the test neurons given the inferred rates.

      We clarify this procedure in the revised manuscript. While a comprehensive benchmarking across all possible LVM architectures is beyond the scope of this study, we provide the statistical infrastructure for users to perform such comparisons. Furthermore, we would like to emphasize that while predictive likelihood is a rigorous metric for model selection, the primary utility of these LVMs often lies in the interpretability of the latent states themselves, which can remain biologically informative even if cross-validated performance is not the sole optimization target.

      While it certainly makes sense that models accounting for the full transformation of latent => spikes => fluorescence data should outperform the two-step (1) deconvolution => (2) latent variance inference approach, the amount of improvement is not clear. A direct comparison … would be useful

      We thank the reviewer for this point. Figure 4 was designed to address this comparison directly. By using a biophysical simulator, we generated a pseudo-realistic spiking network with ground-truth latent trajectories governed by a Gaussian Process. This allowed us to explicitly compare our unified approach against the traditional deconvolution-then-Poisson-GPFA pipeline. While a first-order (AR1) calcium likelihood did not show improvement over the two-step deconvolution method in recovering the ground-truth latents, the second-order (AR2) process demonstrated an improvement. Because there are no ground-truth parameters in the model, we use the reconstruction error of the latent values as our primary metric for recovery. These results suggest that when the observation model sufficiently captures the underlying calcium kinetics, the unified approach offers a more accurate estimation of the neural state.

      It would be useful to discuss the possible extension of the approach to other types of data that … have different observation models.

      We thank the reviewer for this helpful comment. We agree that the general framing of the likelihood has potential use in a wider range of data modalities.

      Specifically, all sensors (aside from some voltage sensors) have a rise and decay time in line with our model. Thus the autoregressive (AR) nature of the calcium likelihood we utilize makes the current implementation particularly well-suited for a broad range of fluorescence-based sensors with similar temporal profiles. The specific use and extension would depend heavily on the biological target of the sensor. For example Glutamate, dopamine, and similar indicators can be thought of as having a similar underlying Poisson firing model, as the release of these products is tied to neural firing. Other sensors that might relate to other biological processes, such as hemodynamics (via imaging or ultrasound) or broader neuromodulation (Norepinephrine imaging with nLight) might be more continually varying and therefore would require changing the Poisson with an appropriate alternative, for example a Gaussian Process or similar.

      Voltage imaging is the one exception that may require more complex observation models. However, the challenge in voltage imaging is not the ability to identify individual spikes, but more that the speed and scope of imaging is inherently limited by the speed of the voltage process and signal-to-noise ratios induced by the low quantum efficiency and membrane-bound nature of these indicators. If imaged well, single spikes would be clearly visible and the two-stage likelihood would not be necessary—one could simply use the spike times in a Poisson model just as with electrophysiology. We have added a paragraph in the discussion highlighting these points.

    1. Author response:

      Reviewer #1 (Public review):

      In this work, Frey and colleagues have carried out a very large study of α-synuclein polymorphism as a function of aggregation conditions and sample preparation. They provide valuable insight into the many critical factors affecting α-synuclein polymorphism, thereby illuminating the need for detailed reporting in the literature as well as both rigorous and detail-oriented protocols when working with this protein. Indeed, their observations are in line with the difficulties of reproducing structural outcomes across different laboratories and experiments. The authors must be complemented on their openness about the difficulties experienced and the thoroughness of their work. Efforts like these are going to be crucial to achieve an understanding of the unparalleled structural plasticity of α-synuclein amyloid fibrils. It is particularly notable that the authors have managed to optimize protocols to form single-polymorph aggregation reactions with high reproducibility.

      In this work, the authors focus on the influence of α-synuclein purity in aggregation reactions. They find that using reverse-phase HPLC to purify the protein significantly alters the aggregation behaviour. It is interesting, and rather uncommon in the field, to use reverse-phase HPLC as a final purification step, rather than SEC, which is commonly used in many laboratories. It would be useful to compare this new protocol even more directly and extensively with the commonly used SEC protocol. When mentioning their previously published work, it should be mentioned explicitly how the protein was purified in these previous studies.

      On the point of protein purification, the authors lyophilize their protein prior to storage. In their work, they also find that pre-aggregation oligomer formation alters the aggregation pathway of α-synuclein. While they demonstrate that this can be solved by appropriate filtration, it should be discussed why the lyphilizaiton step was not reconsidered/omitted given that this process is known to facilitate oligomer formation. Do the authors have experience with aggregation studies using α-synuclein that has not undergone lyophilisation and are able to comment on the influence of this step in the protocol?

      We will include details in our revised version on how samples were prepared in our previously published work. However we do not plan to do a comparison between SEC and HPLC as final purification steps because these are truly orthogonal separation methods. SEC is the gold standard for oligomer removal but not particularly useful for removing degradation products of similar size (which we believe to affect aggregation outcomes). In our hands, the highest purity and reproducibility come from HPLC-purified material followed by a stringent oligomer removal. Because oligomers in the solubilized sample are a concern, SEC as a final post-solubilization/pre-aggregation step might be ideal. However, as we mentioned in the manuscript, SEC dilutes the sample to the point that much of the sample is too dilute for our purposes (aggregation without seeds) and adding an additional concentration step would risk promoting the formation of new oligomers in the concentration device. That is why we resorted to using a 100 kD MWCO filter to remove oligomeric species.

      We considered skipping the lyophilization step and dialyzing the HPLC-purified sample into the buffer of choice but stuck with lyophilization because it provides an easy control over the protein concentration in the solubilized sample.

      To clarify the logic in this choice of sample preparation steps, we will add a section to the revised manuscript listing/explaining our suggested protocols for preparing alpha-synuclein samples for reproducible aggregation experiments.

      The authors make note of several degradation products affecting their aggregation reactions, which is why they employ a much more thorough purification protocol. However, they also point out that some of the degradation products found at the end of their reaction could form during the reaction itself. Unfortunately, they never investigate this further. In particular, it would be very useful to know if different aggregation conditions (pH, salt, agitation) lead to different and characteristic degradation patterns. HPLS/mass spec of the supernatant at the end of each aggregation reaction would have been a very insightful thing to do.

      In retrospect, we agree that this could have been important from the standpoint of understanding how in situ degradation during the aggregation at 37º C could also play a role in polymorph selection. We have begun to save frozen aliquots of our aggregation samples for subsequent MS analyses of the interesting samples in order to be able to address this in the future. However, it was outside the scope of our original search for the PD polymorph.

      With respect to degradation products, in this work a NΔ4-variant is produced to mimic a disease-relevant degradation product and indeed it is found to alter the structural outcome even at low relative concentrations (5%). Have the authors investigated the minimal fraction of the NΔ4 variant necessary to still influence the structural outcome of the predominant WT protein? This type of analysis could have significant relevance to disease-related analysis, where several variants (truncations and PTM variants) are present in trace amounts.

      We did not try lower than 5% because it was our goal to test if impurities at this level (which usually go undetected) could influence the aggregation outcomes. We think that directly relating the precise impurity level in these in vitro experiments to in vivo aggregation would be difficult due to the many factors we do not yet understand that appear to guide in vivo polymorph selection.

      While on this topic, the authors note that in several of their type 5 fibrils, they find unresolved peptide fragments in their cryo-EM structures. Can the authors speculate if these fragments are indeed peptide degradation products or residues wrapping around the fibril originating from the fibril-incorporated protein?

      We will add this speculation to the revised manuscript. The unassigned peptide density most likely originates from the C-terminal residues of the intact chains rather than from a degradation product. The levels of degradation products observed by MS in our other samples were far too low to account for the amount of peptide that would be required for >50% of the fibrils in sample 23 to contain this extra density. Furthermore, in the 5A polymorph the extra peptide density is sometimes present (e.g. sample 52) and sometimes absent (e.g. sample 3), despite the fact that in both samples the coexisting type 5 polymorphs (5m and 5B, respectively) have the peptide bound. Therefore, it appears that subtle differences between 5A polymorphs determine the presence or absence of this density, whereas for 5m and 5B it is consistently present.

      In this work, the authors have performed an extensive study of α-synuclein polymorphism. However, despite generating what is likely the largest single data set of fibril structures, they perform very little quantitative analysis of their data. It would be interesting to analyse the relative abundance of fibril polymorphs produced in each reaction. Perhaps from the particle-picking data it could be estimated the relative abundance of each polymorph as well as non-resolved fibrils to generate a more nuanced view of polymorphism beyond overall classifications of the resolved structures. Indeed, from such data it could also be studied if certain protofilaments are more prone to pair in asymmetric fibril structures over others or if fibril asymmetry can be attributed to random pairing of protofilaments in accord with their abundance. This latter point is particularly interesting for the type 1 fibrils. Perhaps, the propensity of α-synuclein to form specific symmetries could also be estimated.

      We agree that Cryo-EM datasets contain considerable information that could potentially be used to better understand polymorph populations. We have previously used particle counts as an approximate measure of polymorph abundance; however, the biases introduced during particle picking and subsequent curation are substantial, and we therefore do not consider these counts sufficiently reliable for quantitative comparison of polymorph populations.

      Regarding the symmetry of paired filaments, it is clear that the overwhelming preference of all filaments is to pair as symmetric dimers. Among the in vitro polymorphs, type 1 is the most commonly observed to form an asymmetric dimer, either with itself or with the new type 7. However, the number of observations is too small to establish that this represents a statistically meaningful preference. Types 2 and 3 have also been observed to pair in asymmetric fibrils. Overall, we do not think that our dataset is large enough to add statistical weight to previous observations.

      The authors note that pH is a strong factor in determining polymorph selection. This does indeed appear to be the case, but other parameters do not appear to show any clear trend. Have the authors investigated the influence of aggregation parameters (agitation, duration) on structural outcomes systematically or quantitatively, such as with principal component analysis? Indeed, they also find that some fibril types that otherwise are not compatible at the same pH appear to co-exist when the shaking parameter is modified. Are the authors then confident in the claim that pH is a deterministic parameter?

      We did not systematically vary the agitation but in two cases where it was either intentionally or accidentally varied, we found surprising polymorph outcomes. We felt that these observations were worth reporting, but on their own they do not constitute a thorough study. We would rather conclude that pH is a strong selector and can be deterministic under certain conditions: pure sample, no seeds, continuous or intermittent moderate agitation. We will revise the manuscript to make this clearer.

      It is evident from this and other work that amyloid aggregation is highly sensitive to kinetic effects. It is therefore curious that the effect of protein concentration and reaction time has not been systematically investigated. The authors have some data studying dilution series (Figure 6A) and different reaction times (reaction 56&57). Could the authors comment on the effects of these two parameters, and might there be more information touching upon this that could be highlighted in this work?

      We did not collect sufficient data to draw conclusions about the effects of protein concentration or aggregation time, and therefore do not think that a quantitative analysis of these parameters is justified by the present dataset.

      The authors state that this work likely underreports fibril polymorphisms in samples due to population size or data quality challenges. Could the authors, based on their extensive experience, try to quantify this statement?

      Precise quantification would be difficult. The literature has many mentions of amyloids that could not be solved by Cryo-EM due to a lack of twist. In our hands it is very common to have a small subset of non-twisted filaments in a sample and some samples appear to be exclusively non-twisted. Low-abundance or low-quality fibrils are also rather common in our data but also difficult to quantify. Nevertheless, we agree that it would be useful to place a lower bound on this estimate, and we will re-examine our datasets to determine whether this can be quantified in the revised manuscript.

      Additionally, the authors point out that the current framework for classifying α-synuclein fibril polymorphism is not sufficient to describe the real complexity of this protein system. However, they do not seem to address some of the recent literature aiming to solve such issues (see Scheres 2026, Connor et al. 2025, Milchberg et al. 2025 & Price et al. 2025).

      We agree that we should have discussed this literature in greater detail and will do so in the revised manuscript.

      Was any biophysical/biochemical analysis performed of the many structures produced here, such as CD spectroscopy, Proteinase K digestion, dye binding or FTIR, which could act as low-resolution structure identifiers and might help to retrospectively explain some findings in the older literature? Such data would be very useful for the vast majority of researchers, who do not have access to cryo-EM.

      We did not perform these analyses precisely because they are low resolution. Retrospectively, such analyses might have been useful for interpreting past data, but most of these methods (particularly Proteinase K resistance) are difficult to compare between laboratories and work best with side-by-side controls. This is why developing a facile method for polymorph identification is one of our main future research goals.

      Reviewer #2 (Public review):

      Summary:

      This manuscript describes insights gained during efforts to reproduce disease-relevant alpha-Synuclein (aSyn) fibrils using recombinant protein in vitro. It follows up on a similar article from this team published in 2024. Although the authors have not been able to produce fibrils with the structure of ex vivo fibrils isolated from patients, they share insights gained into which factors influence the formation of specific fibril polymorphs.

      Strengths:

      This is quite an unusual manuscript because it goes into minute detail about sample preparation that are usual just mentioned in the Materials and Methods sections of other manuscripts (if at all). This makes it very valuable for the scientific community working on exactly the problem of reproducing disease-relevant aSyn fibrils in vitro (which will be a major breakthrough in the field). The authors present an impressive array of cryo-EM fibril structures, some of which have not been described before.

      Weaknesses:

      A major concern with the manuscript is that its story and messaging are a bit murky. The authors describe a few new polymorphs, show that some polymorphs (type 1) have small variations, show that sample purity and fragmentation will influence polymorph formation, and present a helical-symmetry mystery. This all reads like a loose collection of findings without any major takeaway. Looking at Table 1, it still seems that the authors do not have a good control over any of these polymorphs. Are they able to make any of these polymorphs reliably? I think the impact of this work could be strengthened if it ended with a reliable protocol for the production of any of the polymorphs described.

      It is true that the initial results were a collection of findings compiled while searching for the PD polymorph. However, the trends that we saw in these data inspired us to pursue a more systematic approach which was used to show how impurities play a crucial role in polymorph selection even at low levels. We agree that the impact of the work will be enhanced by summarizing the protocols that can be used to obtain the types 1, 2, 3 and 5 polymorphs and will add this to the revised manuscript.

      A second major concern is the quality of the aggregation kinetics and their interpretation. Are these kinetics just done once per concentration? The figure caption talks about 'three independent samples' but it is unclear if this refers to the three different concentrations or NΔ4 percentages used, or true repetitions. Looking at the curves themselves, it seems that only one of the conditions was actually done in triplicate, which should be the minimum to draw conclusions. Further, it would have been helpful to characterize the kinetic data quantitatively. Finally, because there are only kinetic data for a fraction of the conditions tested, it is not clear what they add to the overall manuscript. My recommendation is to either remove the kinetics from the manuscript or substantially expand this section.

      In Figure 6A, the three curves represent three independent samples; in panels B–D, each curve similarly represents one independent sample. We will try to clear up the ambiguity in the revised version. We agree that the kinetic data have limited utility for determining kinetic parameters of the aggregation. The data were collected primarily to determine when the aggregation reactions were complete so that samples could be prepared for cryo-EM. Nevertheless, we think that the kinetic traces provide two qualitative observations that are relevant to the structural results: 1) In panels A and C of figure 6, the type 5 polymorphs are associated with shorter lag times, suggesting that they either nucleate faster, or as we propose, arise from a small amount of oligomeric protein in the original sample. 2) The longer lag phase associated with the NΔ4 construct was reproducible (panels B, C and D), suggesting that its intramolecular self-chaperoning effect is enhanced due to the increased positive charge in its N-terminal region. Future studies will determine whether this same electrostatic change also gives rise to enhanced secondary nucleation.

    1. Author response:

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      From a big picture viewpoint, this work aims to provide a method to fit parameters of reduced models for neural dynamics so that the resulting tuned model has a bifurcation diagram that matches that of a more complex, computationally expensive model. The matching of bifurcation diagrams ensures that the model dynamics agree on a region of parameter space, rather than just at specially tuned values, and that the models share properties such as qualitative features of their phase response curves, as the authors demonstrate. A notable point is the inclusion of extracellular potassium concentration dynamics into the reduced model - here, the quadratic integrate-and-fire model; this is straightforward but nonetheless useful for studying certain phenomena.

      Strengths:

      The paper demonstrates the method specifically on the fitting of the quadratic integrateand-fire model, with potassium concentration dynamics included, to the Wang-Buzsaki model extended to include the potassium component. The method works very well overall in this instance. The resulting model is thoroughly compared with the original, in terms of bifurcation diagrams, production of various activity patterns, phase response curves, and associated phase-locking and synchronization properties.

      Weaknesses:

      It is important to note that the proposed method requires that a target bifurcation diagram be known. In practical terms, this means that the method may be well suited to fitting a reduced model to another, more complicated model, but is not likely to be useful for fitting the model to data. Certainly, the authors did not illustrate any such application. Secondly, the authors do not provide any sort of general algorithm but rather give a demonstration of a single example of fitting one specific reduced model to one specific conductance-based model.

      We thank the reviewer for this critical assessment. It is true that we demonstrate our approach using as target the bifurcation diagram of a more realistic model. In principle, the method would be applicable to experimental systems if parameter space is sampled under appropriate experimental conditions, e.g., by recording at different extracellular potassium concentrations. However, this is challenging: generating reliable” experimental bifurcation diagrams” would require tightly controlled experimental repetitions under various conditions, particularly for reconstructing two-dimensional bifurcation diagrams. We hope that this work encourages the development of such methods. We have added a discussion of this point; see the paragraph starting at line 549.

      We have also included a general algorithm (Table I) and provide a second example illustrating the procedure (Supplementary Fig. S2).

      Finally, the main idea of the paper seems to me to be a natural descendant of the chain of reasoning, starting from Rinzel - continuing through Bertram; Golubitsky/Kaper/Josic; Izhikevich; and others - that a fundamental way to think about neuronal models, especially those involving bursting dynamics, is in terms of their bifurcation structure. According to this line of reasoning, two models are “the same” if they have the same bifurcation structure. Thus, it becomes natural to fit a reduced model to a more complicated model based on the bifurcation structure. The authors deserve credit for recognizing and implementing this step, and their work may be a useful example to the community. But the manuscript should have described and cited this chain of works to put the current study in the correct context.

      We have added a paragraph in the Discussion section (starting at line 517) to better situate the manuscript within the relevant literature and to explicitly acknowledge the chain of work.

      Reviewer #1 (Recommendations for the authors):

      Please see my public review. In line with my comments, I recommend that the authors either (a) provide a general algorithm for fitting at least a class of reduced models (i.e., those that satisfy some general assumptions) to a class of bifurcation diagrams, or (b) provide at least one more example of implementing their method. Step (b) would not need to be done to the same degree of thoroughness as the example they provided (e.g., the PRCs and synchrony need not be considered), but to me, this step would be very important if (a) is impractical. Otherwise, the paper should probably be rewritten to de-emphasize the message that this is a general method; instead, this should be a paper about specifically fitting the QIF (with potassium dynamics) to the Wang-Buzsaki model (with potassium dynamics).

      We provide a general algorithm for deriving a quadratic integrate-and-fire model with dependence on a biophysical parameter by fitting the bifurcation structure of a given class I conductance based neuron model near an SNL bifurcation induced by this parameter; see Table I.

      In addition, we provide a second example of the reduction procedure: motivated by Hesse et al. (Nature Communications, 10.1038/s41467-022-31195-6, 2022), we derive a QIF model that captures dependence on temperature instead of potassium concentration; see Supplementary Fig. S2.

      Not surprisingly, I also think it’s essential that the authors describe and cite the chain of works on thinking of neuronal models in equivalence classes based on bifurcation diagrams, and make clear that this paper builds on the ideas set forth in that chain.

      We thank the reviewer for this comment. As mentioned above, we have added a paragraph in the Discussion section, starting at line 517, to acknowledge this chain of work.

      Also, the authors should make clear that their method is not one for fitting a model directly to data, which will require rewriting at least the first paragraph of their Discussion section.

      We thank the reviewer for helping us make our manuscript clearer. To avoid confusion, we have clarified this point already in the Introduction (see lines 52-57) and have included a new paragraph in the Discussion (starting at line 549).

      Other specific corrections are:

      (1) Typos should be fixed, as the paper has several. The first line of the abstract has one (“concentrations” → “concentration”), for starters. “Original model” on pg. 3 is missing “be” in “can defined”. “ceases” → “cease” on pg. 13. “nerons” → “neurons” on pg. 19. “standart” → “standard” pg. 24.

      Done. Additional typos were also corrected.

      (2) The abstract mentions “consequences in networks” in its second sentence. This is misleading because studying network dynamics is not at all the main emphasis of the paper, but rather a corollary application of the main ideas, so some restructuring of the abstract is needed. Similarly, the final abstract sentence overstates somewhat what was done with studying synchronization and should be rewritten more precisely.

      We have restructured the abstract accordingly.

      (3) For readers who are interested in the ideas here but not familiar with the QIF model, it will be very difficult to follow the first paragraph of Results. Elementary aspects of QIF dynamics should be explained here (e.g., what is the saddle-node bifurcation), and a basic figure panel about this should be included in Figure 1.

      We added a supplementary figure (Figure S1) adapted from Izhikevich for readers who might not be familiar with the QIF model.

      (4) Bottom lines of page 3 should be reworded to make clear that the slow variables are averaged over each member of a family of fast subsystem limit cycles. Also, “one limit action potential cycle” is an awkward phrase.

      We rephrased this sentence (see paragraph starting at line 140).

      (5) Text under system (1) – why isn’t c mentioned? Also, references to Figure 3 should be to Figure 2 here. And authors should state what they mean by “target model” and be clear about whether it includes potassium dynamics and/or pump current.

      c scales the parabola corresponding to the branch of fixed points, given by c(I<sub>app</sub> − I<sub>SN,0</sub> − I<sub>pump</sub>) = −a(ν − ν<sub>SN</sub>)<sup>2</sup>. Consequently, it also affects the position of the homoclinic bifurcation: In the previous version of the manuscript, c was inadvertently omitted from the expression for the branch of fixed points; this has now been corrected. See paragraph starting at line 154.

      Figure references have been corrected.

      By target model, we mean the conductance-based model that includes potassium dynamics and a pump current, in our case System 4. We clarified this point at the beginning of the Results section (see paragraph starting at line 116). Throughout the manuscript, we now explicitly indicate when we refer only to its fast subsystem and whether the pump current is included. In particular, note that the parameter derivation shown in Figure 4 is performed on the fast subsystem of the target model, in the absence of the pump current. I<sub>pump</sub> can be considered as a potassium-dependent contribution to the applied current, and can be added a posteriori to the QIF model. See paragraph starting at line 162.

      (6) Next par: is the “saddle-node bifurcation” that with I<sub>app</sub> as bifurcation parameter? Please clarify.

      Yes, it is the saddle-node bifurcation with I<sub>app</sub> as bifurcation parameter. We have clarified this in the manuscript; see the paragraph starting at line 170.

      (7) Bottom pg. 5: does “beyond” mean above? below?

      We meant above (larger values of ). In the text, we have replaced “beyond” with “larger than”. See paragraph starting at line 178.

      (8) Formula for v<sub>r</sub> at top of page 6: Please specify what formula for I<sub>pump</sub> is being used here.

      The formula for I<sub>pump</sub> is given in Eq. 5d. We are using the same formula throughout the paper.

      Note that to clarify the reduction procedure, we derive QIF parameters to match the bifurcation diagram with respect to the applied current of the fast subsystem of the target model when I<sub>pump</sub> = 0. Reintroducing I<sub>pump</sub> produces the same horizontal shift in this bifurcation diagram for both the QIF and Wang–Buzsáki versions.

      We have restructured the paragraph starting at line 178 to clarify these aspects.

      (9) Three lines below this: I don’t understand what “matching...is appreciable” and “in the continuity of...” mean. Please revise and also explain why a closer matching of v<sub>r</sub> to the min voltages in Figure 4d was not used, and exactly how the v<sub>r</sub> that is shown was chosen.

      With “matching...is appreciable”, we meant that values assigned to v<sub>r</sub> should be close to the minimum voltage values reached during spiking. With ”in the continuity of...”, we meant that when .(SNIC case), we choose v<sub>r</sub> by extrapolating the linear fit performed on the values of v<sub>r</sub> assigned when , (homoclinic case).

      When , v<sub>r</sub> was chosen so that the homoclinic bifurcation occurs at the same value of applied current as in the fast subsystem of the target model. This is explained in the paragraph starting at line 178 (see Eq. 2). This criterion also allows the minimum voltage values reached during spiking to be captured reasonably well (compare the green dotted line and the purple solid line in panel e of Figure 4).

      We have rewritten the paragraph starting at line 186 to clarify these aspects.

      (10) Bottom page 6 - reference to Figure 3e should be 4e. Also, the text mentions the shrinkage of spike amplitude, but the figure shows that vth increases over most of the K+ range before decreasing, so a correction is needed.

      We corrected the figure reference.

      The maximal voltage of the limit cycles of the target model’s fast subsystem (upper purple curve in Figure 4e) increases slightly between and , by less than 1mV. It then decreases by about 27mV before the fold of limit cycles. The sigmoidal function vth () allows us to capture this substantial decrease in the QIF model. The small preceding increase is not captured. We reformulated the text to avoid confusion (see paragraph starting at line 209).

      (11) Figure 4d: Why is E<sub>K</sub> plotted here? It should be mentioned in the caption and text. More generally, the caption for Figure 4e should be expanded to mention what the purple curves are, what is the black curve for K < K<sub>SNL</sub>, and what the other structures shown are. Finally, the text describes that theSNIC/SNL/Hom is determined by the choice of v<sub>r</sub> relative to v<sub>SN</sub>, so it’s not clear what is I<sub>app,SNL</sub> in the caption - please clarify.

      In conductance-based models, higher weakens the potassium concentration gradient, thereby raising E<sub>K</sub>. The sodium and potassium reversal potentials typically bound voltage oscillations during spiking (see for example Chander and Chakravarthy, PLOS ONE, 10.1371/journal.pone.0048802, 2012), so the minimum voltage of spikes is expected to be higher when is larger. We plotted E<sub>K</sub> in Figure 4d to show that the increase of the reset voltage v<sub>r</sub> at larger reflects this effect in the QIF version of the model. We clarified this in the caption of Figure 4 and in the text (see paragraph starting at line 199).

      Purple curves show families of limit cycles, while black curves, including the one for , show families of fixed points. The green curve shows the linear fit of v<sub>r</sub> from panel d. All these have now been included in the legend.

      In the QIF model, the onset bifurcation (SNIC, SNL, or homoclinic) is indeed determined by the choice of v<sub>r</sub> relative to v<sub>SN</sub>. Figure 4e shows the bifurcation diagram of the fast subsystem of the conductance-based model (Wang-Buzsáki). This is a bifurcation diagram with respect to , for a fixed value of applied current. We chose to fix I<sub>app</sub> at its value at the SNL bifurcation, denoted I<sub>app,SNL</sub>. I<sub>app,SNL</sub> is near 0.22 (see Figure 3a).

      (12) Eqn. (2a): Shouldn’t v<sub>SN</sub> depend on potassium like I<sub>SN</sub> and I<sub>pump</sub> do? What is the formula for Ipump there? Why isn’t the RHS of (2b) dependent on v as in the original model? Please clarify.

      For simplicity, we did not include a potassium dependence for v<sub>SN</sub> in the QIF model. Instead, we set it to its value at the SNL bifurcation (Figure 4b). This is explained in the paragraph starting at line 199: “We notice that v<sub>SN</sub> and the normal form coefficient a are relatively conserved in this interval. We fix them to their value at [K<sup>+</sup>]<sub>o,SNL</sub>.”

      The formula for I<sub>pump</sub> is given in Eq. 5d. The potassium dynamics depends on the voltage via the reset rule in Eq. 3d. This allows us to capture the small increments in at each action potential in the original model (see for example Figure 6c,h). We have clarified these two points in the manuscript (see paragraph starting at line 223).

      (13) Figure 3: Please indicate the criticality of the Hopf bifurcations shown.

      The legend of Fig. 3 now indicates that the Hopf bifurcations are subcritical. The same clarification has been added to the following figures as well.

      (14) Bottom pg. 9: Why isn’t there an I<sub>pump</sub> term as in eqn. (6a)? Please clarify. 

      You are correct, the I<sub>pump</sub> term should be included in the equation for the averaged slow subsystem of the QIF model (see paragraph starting at line 243); it was accidentally omitted in the manuscript. Thank you for pointing this out.

      (15) Top pg. 11: It’s important to reference the slow averaged dynamics here, which allows K+ to increase. Also, this first paragraph should already explain that this averaged dynamics is only relevant along the family of FS periodic orbits, not during the recovery when the FS has a branch of stable equilibria.

      The averaged slow subsystem is indeed only relevant along families of limit cycles of the fast subsystem. Along families of equilibria, averaging is not necessary and the standard slow subsystem can be used. We now explicitly define this standard slow subsystem for both Wang-Buzsáki and the QIF model (see paragraphs starting at lines 241 and 628). In panels e and j of Figure 6, both systems are now represented.

      In the paragraph starting at line 273, we now refer to the averaged slow subsystem to explain the overall increase of during bursts (purple curves in Fig. 6e,j), and to the standard slow subsystem to explain the decrease of during quiescent phases (black curves).

      (16) Pg. 11, par 3: This is unnecessarily confusing. Please try to reword and clarify this paragraph.

      We have simplified this paragraph (starting at line 293). The key point is that the reduction to the averaged slow subsystem is not valid too close to the homoclinic bifurcation.

      (17) Pg. 13, end of Scenario 2: Is there any evidence this is a canard effect and not a noise effect? If so, please mention the evidence; otherwise, perhaps take this out.

      What happens there appears to be a noise-induced canard effect: in the beginning of the burst, the system follows a family of stable limit cycles of the fast subsystem, i.e. a stable object. However, at some point, noise induces a transition to a portion of trajectory where the system evolves near the saddle branch, i.e. a repelling object, for a substantial amount of time. Such phenomena have been thoroughly investigated in the literature, and can also be obtained in a deterministic way; see for example Marin et al. (Physical Review E 90, 042718, 2014). Bursting traces similar to the one in Figure 7c are observed experimentally (see, for example, Figure 4c of Marin et al.), which is why we considered it worth mentioning. We have revised the paragraph starting at line 332 to clarify this point.

      (18) I only see 4 curves in Figure 9a,c, but the legend has 5. Are two on top of each other? Please clarify.

      Yes, the curve for = 7.21mM lies beneath the curve for = 5.21mM. This has been clarified in the figure caption.

      (19) Text should note that the QIF iPRC does not develop a negative region at high K+ and high phase, as WB iPRC does.

      We have updated the paragraph starting at line 409 to mention this.

      (20) Pg. 16, line 4: “at the network scale” is cryptic - a more precise phrase would be preferable.

      We have reformulated the sentence to clarify its meaning (see paragraph starting at line 380).

      (21) Pg. 16, line 9: Reordering of words could make this clearer.

      Done (see paragraph starting at line 385).

      (22) Pg. 16: I am confused by line 14 because the big changes in the iPRC in Figure 9c do not align with the spike phase in Figure 9d. Please clarify what is meant here.

      In the QIF model, at a given phase, the iPRC is the inverse of the slope of the voltage trace as a function of phase. Flatter slopes in Figure 9d therefore correspond to larger iPRC values in Figure 9c. This is illustrated in Figure S5. We have revised the paragraph starting at line 393 to make this point clearer.

      (23) Pg. 16: Please clarify what is meant by a “delta synapse”.

      By “delta synapse,” we meant a configuration in which each spike induces an instantaneous voltage jump in the postsynaptic neuron, modeled using the Dirac delta distribution. We have replaced the term “delta synapse” with “pulse-coupled,” which is more commonly used in the literature, and have added a clarification at its first occurrence in the manuscript.

      (24) Discussion, line 2: Delete comma.

      Done.

      (25) Importantly, as noted above, the first par. needs to be rewritten since the presented method won’t work directly from data or from a target model for which most of the parameters, and hence the bifurcation diagram, are not known.

      As mentioned above, we have included a new paragraph in the Discussion, starting at line 549, to clarify this point.

      (26) Pg. 18: ”Originally” → ”Typically”, perhaps?

      Done.

      (27) Note the work of Marder et al. on temperature-related neural variability.

      We thank the reviewer for this comment. We have added two relevant references from the work of Marder and colleagues addressing temperature-dependent neural variability and ionic concentrations in our manuscript (see the sentence starting on line 537).

      (28) Pg. 20: Cut the ”Potassium dynamics and network models” subsection since it does not add anything substantive as written (or else expand it and include it in the subsection below).

      We have expanded this paragraph and incorporated it into the subsequent subsection, as suggested by the reviewer.

      (29) Finally, it’s a bit confusing that the authors refer to the potassium concentration as a slow variable yet have an instantaneous jump in this quantity at reset in their QIF model (i.e., instantaneous is VERY fast). Some explanation about this should be provided. Do they make the general assumption that ∆<sub>K</sub> is small, for example, such that this reset reflects the slow nature of K+ evolution (i.e., during the reset period, K+ would only change slowly, and hence by a small amount)?

      Yes, ∆<sub>K</sub> is chosen to be small, to capture the behavior of the original model (compare for example panels c and h of Figure 6). As a result, in the QIF model, in the same way as in the original model, despite the fact that the dynamics of includes a fast component, on average evolves slowly. By using the averaging method, we can determine whether overall increases or decreases.

      We clarified this in the manuscript, in the paragraph starting at line 243.

      Reviewer #2 (Public review):

      Summary:

      The authors derive an integrate-and-fire model to describe the dynamics of a more complex Wang-Buzsaki model and compare the two models. A detailed discussion of bifurcation schemes in both models is convincing and allows us to evaluate the simpler model.

      Strengths:

      The idea is interesting, and the mathematical approach appears to be convincing. In addition, differences between the simple and original models are also discussed.

      Weaknesses:

      A comparison to experimental data is necessary to support the theoretical work.

      As mentioned above in our answer to Reviewer 1, we demonstrate our method using as target the bifurcation diagram of a more realistic neuron model. Ideally, one would want to derive phenomenological models that capture bifurcation structures obtained from data. However, this is challenging and beyond the scope of the present study. We hope that this work encourages the development of such methods. We have revised the Introduction (see lines 52-57) and added a paragraph in the Discussion (see the paragraph starting at line 549) addressing this point.

      Reviewer #2 (Recommendations for the authors):

      The manuscript is well-structured; however, it appears that it has been edited with less care. Please see comments below:

      (1) Page 2: “A third bifurcation, the saddle-homoclinic orbit (HOM) bifurcation,”: provide a reference for the bifurcation.

      We have added a reference to the book by Izhikevich (see paragraph starting at line 63).

      We have added additional references in the Introduction that we considered helpful.

      (2) Page 3: “while a larger concentrations it is mediated by...”: remove “it”.

      There was indeed a typo in this sentence. The intended phrasing is: “while at larger concentrations it is mediated by...”. We have corrected it accordingly (paragraph starting at line 134).

      (3) Figure 2, caption: “dashed lines for unstable branches”: this is a dotted line.

      Corrected to “dotted lines”. Thank you.

      (4) Page 4: “is smaller than vSN (Fig. 3c),”: this figure panel does not exist, as well as the Fig.3d referred to afterwards. Please correct.

      We intended to refer to Fig. 2. Figure references have been corrected. See paragraph starting at line 154.

      (5) Page 6: “Fig. 3a-d shows ISN,0, vSN and a for [K]+o between 4 and 16 mM”: Fig.3c+d do not exist, please correct. Similar comment to “the absence of pump (Fig. 3e).” on the same page.

      We intended to refer to Fig. 4. Figure references have been corrected (paragraphs starting at lines 199 and 209).

      (6) Page 8: “(panel A)” → ”panel (a)”.

      Done.

      (7) Figure 4e: What is the meaning of the green dotted curve?

      This curve represents the linear fit of the reset voltage v<sub>r</sub> from panel d of Fig. 4, to show that the minimal voltage values of the limit cycles are also well captured. We have added this curve to the legend and included a brief explanation in the figure caption.

    1. Author response:

      The following is the authors’ response to the original reviews.

      eLife Assessment:

      This important study investigates how experimentally introducing two facultative bacterial endosymbionts into the Russian wheat aphid, Diuraphis noxia, affects aphid performance, dispersal, and damage to cereal host plants. The authors provide solid evidence that the two symbionts can generate contrasting phenotypes: Rickettsiella increases plant damage while reducing wing formation and dispersal, whereas Regiella reduces aphid population growth and feeding damage. The successful establishment and stable transmission of these novel symbiont-host associations, combined with experiments spanning individual, whole-plant, population and mesocosm scales, are notable strengths of the work; however, the mechanisms underlying these effects remain unresolved, evidence for horizontal transmission is indirect, and some population-level conclusions rely on relatively small sample sizes or effects that are not consistently detected across time points, and therefore the potential application of these findings to pest management remains promising but speculative. The study will be of broad interest to researchers working on insect symbiosis, plant-insect interactions, and biologically based approaches to pest management.

      We have made revisions to the manuscript to cover issues raised around sample numbers and mechanisms. We appreciate that we have not been able to finalize the exact mechanism underlying plant damage effects. We note that while comparisons of population performance were limited by the number of populations we could feasibly maintain; sample sizes were substantial in some of the other experiments. We also do substantiate effects through a combination of experimental approaches that start with controlled conditions and then encompass more complex environments.

      Public Reviews:

      Reviewer #1 (Public review):

      Summary:

      In this study, the authors examine what happens when two facultative endosymbionts, Rickettsiella viridis and Regiella insecticola, are introduced into a novel aphid host, the Russian wheat aphid (Diuraphis noxia). They ask whether these introduced symbionts affect aphid performance, plant damage, alate production, dispersal, plant defense responses, and symbiont dynamics. The main result is that the two symbionts have contrasting effects: Rickettsiella tends to increase plant damage and reduce dispersal-related traits, whereas Regiella tends to reduce plant damage and aphid population growth, with less evidence for an effect on dispersal.

      Strengths:

      The manuscript presents successful establishment of stable transinfected populations of an agriculturally important aphid species, which is a substantial technical achievement in itself. I also appreciated that the authors examined the system across several experimental contexts, including different host plants, mixed cages at two temperatures, whole-plant assays, and a mesocosm dispersal experiment, rather than relying on a single laboratory setup. Taken together, these experiments provide a useful and reasonably convincing demonstration that novel symbiont associations can generate contrasting phenotypes in this system.

      We thank the reviewer for recognizing the strengths of the work and for providing extensive comments.

      Weaknesses:

      There are some major aspects of this paper that I thought could be strengthened. My main concern is that the manuscript feels broader than it is conceptually focused. A wide range of outcomes is measured, which gives the study breadth, but it also makes the central question harder to identify. As written, the paper reads more strongly as a proof-of-principle demonstration of ecologically relevant phenotypes than as a tightly framed test of a specific biological idea.

      The broad range of tests in our work was intentional. Rather than relying on a single experimental approach or scale, we designed the study using multiple complementary approaches to independently evaluate the effects of endosymbionts. Thus, our conclusions are supported across multiple experimental contexts rather than by a single experiment or scale. For example, the effects on plant damage were consistent across different host plants, including wheat and barley (Figures 1 & S1), and across different experimental scales, ranging from individual plants maintained in small cages (Figure 1) to a dispersal experiment involving 24 plants (Figure 5). Similarly, aphid fitness was evaluated both at the individual level, using single aphids maintained on individual plants under favorable conditions (Figures S5 & S6), and at the population level under crowding conditions (Figures 3 & 4).

      Despite the breadth of measurements, the study is focused on establishing robust evidence for the contrasting effects of the two endosymbionts on aphid dispersal and plant feeding damage. To help address this concern, we have moved the summary table from the Supplementary Materials to the main text (now Table 1), which provides an overview of the experimental approaches and main findings and should help readers more clearly see how the different experiments are connected.

      A second issue is that the biological basis of the reported phenotypes remains less developed than the phenotypic description itself. The authors make a genuine effort to address mechanism through JA, JA-Ile, SA, and metabolomic profiling, but these analyses only partially explain the main results. The negative result for the canonical defense markers is informative, yet it still leaves a substantial gap between the observed variation in plant damage and the processes responsible for it.

      Our analyses of JA, JA-Ile, SA, and the metabolomic profiles provide some initial insights, but we appreciate that they do not fully explain the differences in plant damage observed between treatments. The primary aim of this study was to evaluate the phenotypic effects of the endosymbionts and their potential for agricultural application, rather than to provide a comprehensive mechanistic explanation. We have accordingly avoided overinterpreting the mechanistic results and now explicitly state that elucidating the underlying biological mechanisms will be an important direction for future research in Discussion section.

      I also think some caution is needed in how the two symbionts are compared. The authors explain why some follow-up experiments were designed differently for Rickettsiella and Regiella, and that rationale is understandable. Still, because the downstream assays were not fully matched, the paper is strongest when each symbiont is interpreted on its own terms rather than as a strict comparison.

      Our initial plant-damage experiment was designed as a first comparison to test whether different endosymbionts can have diverse and contrasting effects on their aphid host population and plant damage. We then investigated the individual phenotypes of each endosymbiont in greater detail, particularly in relation to their potential agricultural applications. Specifically, our results suggest that Regiella may reduce plant damage, whereas Rickettsiella may reduce dispersal. Based on these early findings, some further experiments were conducted with slightly different experimental setups. Nevertheless, many of the experiments conducted for the two endosymbionts were broadly comparable. We designed the additional experiment carried out only with Rickettsiella to test whether reduced alate production observed in our earlier experiments also translated into reduced dispersal at the population level. An equivalent experiment with Regiella was not undertaken because we failed to detect an effect of this endosymbiont on alate frequency in our preceding experiments. We have clarified this rationale in the Materials and methods section (“Aphid dispersal ability and plant feeding damage in mesocosms”).

      Overall, I would suggest softening the Significance Statement so that it more clearly reflects what is directly shown here, namely that introduced symbionts can alter plant damage and dispersal-related phenotypes under controlled conditions, rather than implying that the study directly tests management utility in agricultural settings.

      We have done this in the Significance Statement. We appreciate that the current experiments have been carried out under controlled conditions, rather than in agricultural settings. Pending permit approval, we are currently planning to extend this work to contained field settings to test whether effects on plant damage and dispersal ability are also observed under less controlled conditions.

      Reviewer #2 (Public review):

      Summary:

      The authors generated two novel aphid-symbiont associations and examined the impact of these new symbiotic associations on plant-insect-symbiont interactions. The authors notably provide detailed phenotypic assessments of the insect hosts and host plants. They show that one introduced symbiont, Rickettsiella, increases aphid-induced damage to host plants, while the other, Regiella, ameliorates aphid damage. The authors suggest that such novel insect-symbiont pairings may be used as tools to mitigate crop damage in the future.

      Strengths:

      Although a few experiments seem to have limited sample sizes and limited statistical power, these are often complemented with highly replicated smaller-scale experiments. The combination of larger mesocosm and population-level experiments along with assessments of individual insects generally provides a comprehensive depiction of the effects of these symbionts on their hosts. The opposing impacts of Regiella and Rickettsiella infection on the aphid host plant are of broad interest. It is also surprising that the host plants did not exhibit strong differences in canonical defensive signalling, despite these differences.

      Weaknesses:

      One thing that I struggled a little with was the rapid spread of Regiella in the shared plant experiments. Possibly this could be attributed to an increased reproductive output (due to faster developmental time, and/or an increase in fecundity) or efficient horizontal transmission. However, the other experiments performed indicate a slight negative impact (Figure 4a) or no influence (Figure 4C, 4D, Figure S6) of Regiella infection on host fitness. Given these other results, it seems that Regiella must spread fairly efficiently between hosts, which comes as a surprise, and there are very few examples of horizontal transmission of Regiella like this in the literature. The manuscript would benefit from a clear and direct demonstration of horizontal transmission, rather than it being inferred indirectly. The similar spread observed in the Rickettsiella mixed cages is less surprising, because there are several examples where this has been demonstrated.

      We agree that the rapid spread of Regiella in the shared-plant experiments cannot be readily explained by host fitness alone, though we have noted fitness benefits of Regiella in a different transinfection in oat aphids (Yu et al., 2025). In a previous study with transinfected green peach aphids and despite a substantial fitness cost, we found that Rickettsiella can spread relatively rapidly in a population and show high stability (Gu et al., 2023) and perhaps transmission of Regiella follows a similar pathway. However, whereas Rickettsiella may spread through plant tissues, Regiella showed relatively low levels of horizontal transmission through this pathway.

      We certainly agree that more work is required to establish the mechanism and dynamics of horizontal transmission in this system. Rather than focusing on mechanism, our objective here was to examine endosymbiont spread where intact plants were available and where there was a mixed aphid population. Note that we also conducted an additional experiment in which Regiella-infected aphids were present at a frequency of only 10% of the initial population, and in this situation Regiella nevertheless still increased in frequency including to a low Cp value in most (8/10) replicates, highlighting its persistence and potential to increase in populations.

      References:

      Gu et al., A rapidly spreading deleterious aphid endosymbiont that uses horizontal as well as vertical transmission. Proc Natl Acad Sci USA 120, e2217278120 (2023).

      Yu et al., A persistent bacterial Regiella transinfection in the bird cherry-oat aphid Rhopalosiphum padi increasing host fitness and decreasing plant virus transmission. Pest Manag Sci 81, 2791-2799 (2025).

      It is also a little surprising that mesocosm-dispersal experiments were not also conducted using Regiella-infected lines. At several points throughout the manuscript, the idea of using symbiont transfections to reduce plant harm is raised. I can understand that these experiments are likely time-, space-, and resource-intensive, but that seems like these would have been relevant experiments, especially in the context of controlling damage to plants.

      We conducted the final mesocosm-dispersal experiment specifically with Rickettsiella because our earlier individual-plant experiments had already shown a clear reduction in alate production in Rickettsiella-infected aphids, together with effects on plant damage (Figure S1I) and population growth (Figure 3C). In contrast, we did not detect a significant difference in alate frequency between Regiella-infected and wild type aphid strains in the similar set up experiments (Figure S1I and Figure 4C). We therefore designed the additional experiment to test whether the reduced alate production observed with Rickettsiella also translated into reduced dispersal at the population level. We did not conduct the same experiment with Regiella because there was no difference in alate frequency in our earlier experiments. We have also added this explanation in Materials and methods section (“Aphid dispersal ability and plant feeding damage in mesocosms”). We do appreciate however that future experiments on dispersal of Regiella will be worthwhile resources permitting.

      Reviewer #3 (Public review):

      Summary:

      The authors were investigating the impact of introducing novel facultative bacterial endosymbionts into the pest aphid, Diuraphis noxia, to explore the possibility of using facultative symbionts as a crop protection tool. They successfully established the vertical transmission of both endosymbionts and performed a series of aphid performance and dispersal experiments together with measurement of aphid feeding on host plant health, growth, and metabolism. While most of the experiments revealed no effect of the endosymbionts, some significant treatment effects were found, showing that Rickettsiella reduced aphid dispersal, and Regiella reduced aphid population growth and feeding damage.

      Strengths:

      The team worked with two novel facultative symbionts (Rickettsiella viridis and Regiella insecticola) that they were able to successfully establish in D. noxia. The data were collected and analyzed using solid, well-described methodology.

      Weaknesses:

      While interpretation of the data is reasonable, the few experiments which revealed significant treatment effects rest on relatively small sample sizes.

      We acknowledge that more replication is always desirable, but we would also argue that significant effects were not marginal and replication was substantial in many cases (e. g. 9-10 replicate plants per damage treatment evaluation). We were also focused on using multiple experimental approaches and scales to independently and repeatedly evaluate the effects of endosymbionts on aphid fitness, wing development, plant damage, and aphid dispersal. Thus, conclusions are not based on a single experiment or experimental scale. For plant damage, for example, we observed consistent effects across different host plants, including wheat and barley (Figure 1 and Figure S1), as well as across different experimental scales, from individual plants maintained in small cages (Figure 1) to a dispersal experiment involving 24 plants (Figure 5). Similarly, aphid fitness was evaluated both at the individual level using single aphids maintained on individual plants under favorable conditions (60 replicates per treatment) (Figures S5 & S6) and at the population level under crowding conditions (Figures 3 & 4). These complementary experimental designs allowed us to examine whether the observed phenotypes were consistent across different environmental and population contexts. We did face challenges in high levels of replication of independent aphid strains in population cage experiments but attempted to replicate as much as possible given the resources that were available.

      Measuring symbiont density is difficult. The authors use quantitative PCR to measure the "density" of endosymbionts relative to a host gene. This is a standard approach in the field; however, recent work has shown that endosymbionts like the aphid primary endosymbiont, Buchnera, are variably polyploid [1]; further the aphid cells that house the symbionts are also highly polyploid and variable in their ploidy [2]. It is important to understand that what is being measured when using qPCR is DNA copy number and not quantification of the number of symbiont cells. Alternative approaches to measuring symbiont density include flow cytometry [3], and SymbiQuant [4], a machine vision tool that can quantitatively characterize symbiont populations from DAPI-stained confocal images. These alternate approaches also have their dlimitations. Currently, there is no perfect approach to measuring symbiont density, which remains an important measure in experiments such as these. Put simply, it is important for a reader to be aware of the limitations of each approach and interpret data accordingly.

      (1) Komaki, K., and H. Ishikawa. 2000. Genomic copy number of intracellular bacterial symbionts of aphids varies in response to developmental stage and morph of their host. Insect Biochemistry and Molecular Biology 30:253-258.

      (2) Nozaki, T., and S. Shigenobu. 2022. Ploidy dynamics in aphid host cells harboring bacterial symbionts. Scientific Reports 12:9111.

      (3) Simonet, P., G. Duport, K. Gaget, M. Weiss-Gayet, S. Colella, G. Febvay, H. Charles, J. Viñuelas, A. Heddi, and F. Calevro. 2016. Direct flow cytometry measurements reveal a fine-tuning of symbiotic cell dynamics according to the host developmental needs in aphid symbiosis. Scientific Reports 6:19967.

      (4) James, E. B., X. Pan, O. Schwartz, and A. C. C. Wilson. 2022. SymbiQuant: A machine learning object detection tool for polyploid independent estimates of endosymbiont population size. Frontiers in Microbiology 13:816608.

      We agree that qPCR-based measurements of endosymbiont gene copy number have limitations even if they are the standard approach used in most studies. In the current set of experiments, qPCR provided a practical and efficient approach for assessing variation in endosymbiont abundance and infection status among samples and the only one feasible given the number of monitoring events and samples required. Nevertheless, we acknowledge the limitations of this approach (and have pointed this out ourselves in a recent COIS paper – Hoffmann et al 2026). We now mention this under further work and provide a couple of references (see Discussion).

      Reference:

      Hoffmann, A. A., Yang, Q. and P. A. Ross. Aphid endosymbionts revisited: molecular detection, diversity, and population dynamics. Curr Op Insect Sci (in press). (2026)

      Impact and Significance:

      Food security and production, and pest control are major challenges facing the human population. This work contributes knowledge that will benefit the development of alternate pest control strategies in agriculture.

      Recommendations for the authors:

      Reviewer #1 (Recommendations for the authors):

      (1) Overall, I found the study interesting and worthwhile, particularly because it shows that novel symbiont associations can generate contrasting phenotypes in an important pest species. My main suggestion would be to sharpen the framing of the paper and to bring the mechanistic and applied discussion into slightly closer alignment with the current evidence base. With those points addressed, I think the manuscript would read as a clearer and more balanced contribution.

      We have rephrased the Discussion around the mechanistic component of the work to sharpen this and link more directly to evidence. For instance:

      “Despite this, our metabolomic analyses suggest that endosymbionts in D. noxia may influence some other aspects of wheat metabolism in a spatially structured way. Within aphid-feeding areas, wheat exposed to Rickettsiella aphids showed increased valine and decreased 3-phenyllactic acid. Changes in valine have been reported in plants responding to herbivory and other forms of stress (43-45), while 3‑phenyllactic acid has been associated with antimicrobial and defense-related activity (46). In non-feeding areas, wheat exposed to Regiella aphids showed reduced urea and increased pantothenic acid. These changes may reflect differences in nitrogen metabolism and allocation (47), and in metabolic processes involving pantothenic acid (48) respectively. However, the present metabolomic data do not establish the functional consequences or causal mechanisms underlying these changes. They indicate that aphids carrying different endosymbionts are associated with some distinct metabolic responses in wheat, including responses that differ between aphid-feeding and non-feeding areas. Our findings are consistent with previous work showing that phloem‑feeding insects can induce changes in plant metabolites in response to herbivory (49, 50) and provide a basis for future studies to determine how endosymbionts influence aphid-induced plant responses and contribute to contrasting plant phenotypes.”

      We have not undertaken a complete reframing of the paper but further emphasized the focus on phenotypic contrasts in a few places including incorporating some changes to the comments below.

      (2) Lines 130-135: Please clarify more explicitly whether the main aim of the paper is to test a specific biological hypothesis about endosymbiont-mediated aphid-plant interactions or to provide a broader proof-of-principle survey of symbiont-associated phenotypes. As it stands, the framing moves between multitrophic biology and pest-management relevance, which makes the central conceptual contribution harder to identify.

      We have rephrased this sentence as “By integrating these factors, we investigate how endosymbiont infection influences aphid fitness and aphid–plant interactions, providing insights into the ecological consequences of novel microbial associations and their potential relevance to sustainable pest management.”

      (3) Line 205: For the metabolomic analysis, please consider adding a formal multivariate test for strain effects, especially for the comparisons shown in Figure 2C and 2D, or otherwise interpret the PCA more cautiously as descriptive rather than inferential.

      We have emphasized the descriptive component and rephrased this sentence as “However, within either area, there was no clear separation among aphid strains (Figures 2C & 2D), suggesting broadly similar metabolomic profiles among strains of the same aphid clone carrying different symbionts.”

      (4) Please clarify how the top and bottom feeding leaves were handled analytically in the analyses, and explain the rationale for collapsing them into a single "feeding area" category. If possible, it would be helpful to show whether leaf position itself influenced the plant-response patterns.

      We combined the upper and lower leaves together to provide a representative measure of the plant-level responses, rather than focusing on responses at a particular leaf position. This approach was consistent with the main objective of our study, which was to investigate whole plant responses to aphids hosting different endosymbionts, rather than differences in responses among different plant parts. In addition, combining the two portions provided sufficient plant material for the GC-MS analysis and helped ensure reliable metabolite measurements from the same material. Because the two leaf positions were combined prior to GC-MS analysis, we were unable to separately test the effect of leaf position on the metabolomic response in this dataset. We have clarified this point in the revised manuscript in Materials and methods section (“Plant defense responses”).

      (5) Line 228: The use of 19{degree sign}C and 25{degree sign}C is not unusual in aphid work, but it would still help the reader if the manuscript stated more explicitly why these two temperatures were chosen in this study.

      We selected 19°C and 25°C because they represent contrasting temperature conditions within the range suitable for Russian wheat aphid development, allowing us to assess whether temperature influences Rickettsiella transmission and population dynamics. In particular, our previous observations indicated differences in the rate of Rickettsiella spread between these temperature conditions (Gu et al., 2023).

      Reference:

      Gu et al., A rapidly spreading deleterious aphid endosymbiont that uses horizontal as well as vertical transmission. Proc Natl Acad Sci USA 120, e2217278120 (2023).

      (6) Lines 390-392: It would help to discuss more explicitly how the relatively modest effects in the individual life-history assays relate to the clearer signals seen at the whole-plant and population level.

      In our experiments, we assessed aphid fitness under different environmental conditions. In the individual fitness assays conducted on cups with a single plant (Figures S5 & S6), aphids were maintained under relatively favourable conditions, with limited environmental stress and without substantial crowding. Under these conditions, we observed an increase in fitness associated with endosymbiont infection. In contrast, we also examined aphid performance at the population level (Figures 3 & 4), where populations were established from a small number of aphids and subsequently experienced increasing crowding and density-dependent stress. Under these conditions, the effects of endosymbiont infection differed from those observed in the individual assays, with Rickettsiella-infected aphids showing greater population growth and Regiella-infected aphids showing reduced population growth.

      These results suggest that the effects of endosymbionts on aphid fitness are context-dependent and may become more pronounced as population density increases and density-dependent stress develops. Thus, relatively modest effects observed at the individual level where experiments are often undertaken may not translate to differences at the population level, and plant level effects may subsequently influence feeding pressure and plant damage. We have added this perspective in the Results and Discussion sections.

      (7) Line 678 & 688: In both whole-plant experiments, please explain how 3 and 4 replicate plants were selected.

      The replicate plants were randomly selected from the available plants for each treatment to minimize potential selection bias. We have clarified this procedure in the revised manuscript in Materials and methods section.

      (8) Lines 686-690 / Figure 4: In the Regiella whole-plant experiment, the Methods state that 16 plants were established per treatment and that 4 plants per treatment were removed at each time point (days 4, 8, 12, and 16). However, in Figure 4B-D, day 12 appears to include 5 data points. Please clarify this apparent mismatch between the described sampling scheme and the data shown in the figure.

      We thank the reviewer for pointing out this and we have corrected this mistake. We initially established 16 plants for the wild type and 17 plants for the Regiella treatment. Four plants per treatment were originally planned to be sampled at each time point (Days 4, 8, 12, and 16). However, because Day 12 was a key time point at which an obvious difference in plant damage was observed between the treatments, we selected one additional plant each treatment for measurement at Day 12, resulting in five data points for this treatment at that time point. The remaining plant was therefore measured at Day 16. We have clarified the sampling procedure in the revised Materials and methods section and figure legend.

      (9) Figure 2A and Figure 4A: These schematics are helpful overall, but the brown supporting sticks stand out quite strongly and may make the panels a little harder to interpret at first glance. I wonder whether they could be simplified, made less prominent, or replaced with photographs of the actual setup if those are available.

      We have revised Figures 2A and 4A to simplify the supporting structures and reduce their visual prominence.

      Reviewer #2 (Recommendations for the authors):

      Some of the statistics were not entirely clear to me, particularly the tests reported in the results which differ from what is described in the figure legends:

      (1) Lines 306-308: "Total nymph numbers were higher on Rickettsiella aphids from Day 21 to Day 25" and indicates that this is based on GLM testing, but the figure does not indicate statistical significance, and the figure legend states independent sample t-tests were used. Similar comment for the following paragraph and corresponding figure.

      The GLMs were used to test the overall patterns in nymph numbers across the relevant time periods, including Days 21–25, rather than testing each time point independently. We also conducted independent-sample t-tests to assess differences between treatments at individual time points. We have clarified this distinction in the Statistical section.

      (2) Line 43: Does not seem like the appropriate reference (reference is on plant virus transmission, not salivary toxins).

      We thank the reviewer for pointing this out. We have removed this reference and replaced it with reference 34 (Luna et al., 2018) that directly supports the statement regarding aphid salivary toxins.

      Reference:

      Luna et al., Bacteria associated with Russian wheat aphid (Diuraphis noxia) enhance aphid virulence to wheat. Phytobiomes J 2, 151-164 (2018).

      Reviewer #3 (Recommendations for the authors):

      Minor editorial comments:

      (1) Figure S10 - the figure legend needs improvement as the current version does not help the reader understand the figure. Please also include a key.

      We have changed the figure legend with reference to our aim, and also explained use of the Cp values. “Figure S10. Rickettsiella Cp values in (A) routine screening of laboratory Rickettsiella colonies and (B) the mixed cage experiment assessing endosymbiont frequency changes over time at 19 °C and 25 °C. The dark red area represents overlap between the 19°C and 25°C experiments. Cp values represent the quantification cycle values obtained from qPCR, with lower Cp values indicating a higher amount of Rickettsiella target DNA. This figure shows the typical range of Cp values observed in our laboratory Rickettsiella -infected aphid colonies. We used this range as a reference for identifying aphids that acquired Rickettsiella through horizontal transmission, as horizontally infected aphids generally showed much higher Cp values than vertically infected aphids.”

      (2) Define Cp.

      We have explained it as “Cp values represent the quantification cycle values obtained from qPCR, with lower Cp values indicating a higher amount of Rickettsiella target DNA.”

      (3) Supplemental Information: Line 113 - T is missing from Table.

      This has been added.

      (4) Move Table S2 to the main paper - this table provides a useful summary of the work.

      This has been moved.

      Main Manuscript:

      (1) Line 145: Serratia was not detected at G0 - was it detected later? It seems possible that titer could be very low to begin and increase in later generations; please clarify.

      We have previously monitored the aphid populations for the presence of Serratia transinfected from the same donor resource across subsequent generations, and Serratia was not detected at any later generation. We also did not detect Serratia in the other aphid species we examined, including green peach aphids (Gu et al., 2023 & 2025) and oat aphids (Yang et al., 2026). Therefore, we believe that the absence of Serratia at G0 was not due to a very low initial titer followed by an increase in later generations but instead that Serratia had been lost from the aphid population.

      References:

      Gu et al., A rapidly spreading deleterious aphid endosymbiont that uses horizontal as well as vertical transmission. Proc Natl Acad Sci USA 120, e2217278120 (2023).

      Gu et al., Transinfections of the endosymbiont Rickettsiella viridis in different Myzus persicae (Hemiptera: Aphididae) clones show consistent deleterious effects and stable transmission. J Econ Entomol 118, 1544-1552 (2025).

      Yang et al., A Rickettsiella transinfection in Rhopalosiphum padi reduces fitness and alate production but not plant virus transmission. Pest Man Sci 82, 3894-3906 (2026).

      (2) Line 206: "different aphid strain" - I learned from the manuscript that a single clone of D. noxia is found in Australia. Further, from my reading of the manuscript, I understand that one clonal isolate was propagated and then infected with symbionts. I think it is important to reword this sentence so that it is clear that the aphid genetic background is held constant, and that the only differences here are the presence or absence of the different symbionts. My reaction to this sentence was that you are working with the same aphid strain hosting different symbionts.

      We have clarified it by adding “the same aphid clone carrying different symbionts” after the different aphid strains.

      (3) Measuring symbiont "density" is a tricky thing to do; I explain this above in the public review. I suggest considering some revisions to the manuscript to be sure that you accurately reflect what has been measured and what can reasonably be inferred from using qPCR to measure gene copy number.

      We agree that qPCR-based measurements of symbiont gene copy number have limitations. In this experiment, we had a relatively large number of samples, and qPCR provided a practical and efficient approach for assessing variation in endosymbiont abundance and infection status among samples. While we acknowledge the limitations of this approach, the relative differences in gene copy number can still provide an indication of variation in endosymbiont abundance and infection status among treatments. Unfortunately, other approaches remain challenging given resource and expertise limitations.

      (4) I think that you may be undervaluing the results of the mixed infection experiments; I find them to be compelling. To me, the data suggest that the symbionts increase aphid fitness.

      In our experiments, we assessed aphid fitness under different environmental conditions. In the individual fitness assays conducted on cups with a single wheat plant (Figures S5 & S6), aphids were maintained under relatively favourable conditions, with limited environmental stress and without substantial crowding. Under these conditions, we observed an increase in fitness associated with symbiont infection. However, we also examined aphid performance under population-level conditions, where populations were established from a small number of aphids and subsequently experienced increasing crowding and density-dependent stress (Figures 3 & 4). Under these conditions, the effects on fitness were different from those observed in the individual assays. We therefore agree that our results suggest that symbionts can increase aphid fitness under some conditions, but that this effect may be context-dependent and can differ under population-level conditions where density-dependent stress occurs. We have also added this information to our Results section to make this clear to readers.

      (5) Lines 288-291: This sentence doesn’t make sense to me. What "minor fitness costs" are being referred to? If the infected lines are increasing in representation relative to the uninfected lines, that suggests that there are not fitness costs, but fitness advantages under the experimental conditions.

      We have rephrased it to “minor fitness effects” which we refer to the fitness test under favourable conditions.

      (6) The section that begins on line 293 - I find this part to not be particularly robust and suggest dropping it from the paper.

      We appreciate the reviewer’s concern regarding the robustness of this section. We included this experiment to monitor changes in aphid population over time and to help explain the differences in plant feeding damage observed between aphids carrying different endosymbionts. Importantly, we conducted this experiment using whole wheat plants to evaluate whether the patterns observed in our other experiments were also evident. We believe that these results provide important complementary evidence for interpreting the differences in plant damage among the aphids hosting different endosymbionts and therefore are relevant to the overall conclusions of the study. For this reason, we prefer to retain this section in the manuscript.

      (7) Line 298: three plants per time point - I do not think this sample size is reflected in the methods of the paper.

      We have mentioned in the method part with “At day 14, three replicate plants were randomly selected from the available plants for both treatments and we counted the total number of nymphs, alate adults, and apterous adults. This was repeated again at Days 21 and 25”.

      (8) Line 304: "the frequency of alates decreased as plant damage increased" - this seems to be counterintuitive!

      As plant damage increased, the total aphid population also increased, resulting in an increase in the absolute number of alates. However, the frequency (proportion) of alates decreased because the increase in the total aphid population was greater than the increase in the number of alates.

      (9) Line 404: "horizontal transmission through plant tissue and/or transfer via aphid contact or honeydew" - what evidence is there that this happens? I have not kept on top of the literature with respect to transmission of secondary symbionts in aphids, but back when I was very familiar with that literature, the data did not support transmission by any of those routes. If there is now evidence supporting transmission by these routes, please cite it here.

      Previous studies have provided experimental evidence that horizontal transmission of aphid-associated endosymbionts can occur through plants. For example, plant-mediated transmission has been demonstrated for direct detection of secondary endosymbiont in the plant tissue including Hamiltonella defensa (Li et al., 2018), Rickettsia (Shi et al., 2024) and Serratia symbiotica (Pons, et al., 2019a). Our previous research also demonstrates that Rickettsiella endosymbionts were detected in uninfected aphids after feeding by infected aphids regardless of physical contact (Gu et al., 2023). Endosymbionts have also been detected in aphid honeydew (Darby and Douglas, 2003) and some primary transmission route appears to be horizontal, through honeydew (faeces) and host plant phloem (Pons, et al., 2019a & 2019b; Perreau et al., 2021). Appropriate references have been added to the revised manuscript in the Discussion section.

      References:

      Li et al., Plant-mediated horizontal transmission of Hamiltonella defensa in the wheat aphid Sitobion miscanthi. J Agric Food Chem 66, 13367-13377 (2018).

      Shi et al., Rickettsia transmission from whitefly to plants benefits herbivore insects but is detrimental to fungal and viral pathogens. mBio 15, e02448-23 (2024).

      Pons et al., Circulation of the cultivable symbiont Serratia symbiotica in aphids is mediated by plants. Front Microbiol 10, 764 (2019a).

      Darby and Douglas, Elucidation of the transmission patterns of an insect-borne bacterium. Appl Environ Microbiol 69, 4403-4407 (2003).

      Pons et al., New insights into the nature of symbiotic associations in aphids: infection process, biological effects, and transmission mode of cultivable Serratia symbiotica bacteria. Appl Environ Microbiol 85, e02445-18 (2019b).

      Perreau et al., Vertical transmission at the pathogen-symbiont interface: Serratia symbiotica and aphids. mBio 12, e00359-21 (2021).

      (10) Line 511: revise to "to measure their relative densities relative to a host gene".

      We have revised it.

      (11) Throughout the manuscript, please replace "five aged-matched" with an accurate description of the aphids used in the experiment. Please pay particular attention to the figure legends. Simply state e.g. "five 10-day-old apterous females" etc.

      This has been replicated in the main manuscript and figure legends.

      (9) Line 727 - lowercase t for Tests.

      This has been added.

      (10) Line 738 - what happens when you don’t exclude the early time points? Do your significant results go away? Also, please define what is meant by "early time points".

      When the early time points (Day 14 for Rickettsiella and Day 4 for Regiella) were included in the analysis, the GLM still showed a significant effect of strain on alate production for Rickettsiella (F<sub>1,12</sub> = 26.434, P < 0.001). We excluded these early time points from the analysis presented in the manuscript because, at these stages, aphid population sizes were still similar between treatments. We also conducted independent-sample t-tests at individual time points and observed differences at the later time points, when aphid population sizes began to diverge. We therefore considered the later time points to be more informative for assessing fitness effects and population sizes under increasing crowding conditions. We have now clarified this as “The earliest time points in the experiments for Rickettsiella (Day 14) and Regiella (Day 4) were excluded” in the manuscript.

      (11) In the legends of all figures, please be explicit about sample sizes.

      We have added the relevant information about replicate number or sample sizes in the main and supplementary figures.

      (12) Line 1010 - replace "each leave" with "each leaf" - there was at least one other place, I think in the supplemental information, that leave was used instead of "leaf".

      We replaced this.

    1. Author response:

      The following is the authors’ response to the previous reviews.

      Public Reviews:

      Reviewer #1 (Public review):

      This work compiles a comprehensive atlas of ncORFs across mammalian tissues and cell types, derived from reanalysis of ~400 public ribosome profiling datasets. The authors then evaluate cross-species conservation and functional signatures, proposing that evolutionarily ancient ncORFs tend to have higher translation potential, stronger expression, and closer relationships with canonical coding sequences.

      Strengths:

      In general, the study provides a large-scale and timely resource of annotated ncORFs, which could be broadly useful for the community. The authors collected ~400 public ribosome profiling datasets for annotations of ncORFs, which, to my best knowledge, is the largest collection of data for such purpose. The catalog could facilitate future investigations into ncORF biology and broaden understanding of the coding potential of the "non-coding" genome.

      Weaknesses:

      Based on the ncORF catalog, some of the analyses were not properly done. Some of the results are descriptive.

      (1) Bias and representations of data source. Public ribo-seq datasets are unevenly distributed across tissues and cell lines, raising concerns about heterogeneity and underrepresentation of certain contexts. This may limit the generalizability of the catalog.

      (2) The discussion on modular domains of ncORFs is unclear, and the claim that they may originate via TErelated mechanisms is not well supported. Stronger evidence or clearer reasoning is needed.

      (3) The conservation comparisons are not fully convincing. Figure S7 shows only mild differences between ncORFs and CDS, and statistical significance is not clearly demonstrated. Comparisons with other noncoding RNAs should be added, and overlapping sequences between ncORFs and CDS should be excluded to avoid bias.

      (4) Figure 3 indicates that some ncORFs are subject to evolutionary constraints. This is not surprising. The authors should provide further analyses on more detailed features of these "conserved" ncORFs vs. the "non-conserved" ones. Some pretty informative works have been done in drosophila, worms, mouse, and human. Figure 3 suggests some ncORFs are under evolutionary constraint, but this is not unexpected. More granular analyses contrasting "conserved" versus "non-conserved" ncORFs would be informative. In fact, small ORFs, especially uORFs, have been extensively studied, for their functions and corss-species conservations. The authors should explicitly show what is new here in their analyses.

      (5) Translation levels are reported using RPF counts. However, translation efficiency (normalized by RNA expression) is a more appropriate measure to account for expression heterogeneity.

      (6) The correlation analyses between ncORF translation levels and PhyloCSF are confusing and largely descriptive. These sections need sharper framing and clearer conclusions.

      (7) Public ribo-seq datasets, generated by different research labs, are known for their strong batch effects. Representations of tissues and cells are also very unbalanced. Therefore, the co-translation analysis between ncORFs and canonical CDS is not well controlled. This should be done by referring to a recent large-scale ribo-seq meta-analysis (Nat Biotechnol. 2025. doi: 10.1038/s41587-025-02718-5).

      Comments on revisions:

      The authors have made efforts to address most of the previous concerns, and several points have been clarified or improved in the revision. However, in a number of cases, the responses rely more on acknowledgment and reframing rather than substantive analytical strengthening. Overall, the manuscript is improved, particularly in terms of clarity, transparency, and positioning of claims. I support its publication and look forward to seeing how the field engages with and discusses these claims.

      We thank Reviewer #1 for the constructive comments and recognition of the value of our ncORF atlas. We have addressed the key concerns by strengthening the analyses and clarifying the framing and limitations of our conclusions. We appreciate the reviewer’s support for publication and believe these revisions have further improved the manuscript.

      Reviewer #2 (Public review):

      Summary:

      Chang et al. attempted to analyze a large number of ribo-seq datasets through a standardized pipeline, identifying novel non-canonical ORFs and elucidating their evolutionary and expression characteristics.

      Strengths:

      (1) The datasets analyzed by the authors are sufficiently comprehensive, and the use of standardized pipelines ensures excellent analytical consistency.

      (2) Their analyses of ORF evolution and co-expression further deepen our understanding of these ORFs.

      Weaknesses:

      (1) The authors primarily conducted analyses through bioinformatics, lacking sufficient wet-lab experimental evidence.

      (2) Some analytical methods and standards were not clearly presented in the manuscript.

      We thank Reviewer #2 for the positive assessment of our comprehensive dataset and standardized analytical framework. We have clarified the analytical methods and criteria throughout the manuscript and better defined the scope and limitations of our bioinformatics-based analyses. We appreciate the reviewer’s constructive suggestions, which have helped improve the clarity and rigor of the manuscript.

      Recommendations for the authors:

      Reviewing Editor:

      We have evaluated the revision together with the reviewers' second-round assessments and your responses. The reviewers agree that the manuscript has improved in clarity and that the standardized integration of large-scale Ribo-seq datasets provides a valuable resource for the field. However, several important concerns remain insufficiently resolved. In multiple cases, the revision relies primarily on acknowledgment or reframing of limitations rather than additional analyses or clearer methodological justification, leaving the evidential support for several conclusions incomplete.

      Because the study is entirely computational, all analytical procedures, criteria, and thresholds should be explicitly defined and adequately justified to meet the expected standard of technical rigor. In particular, key components of the analytical framework require clearer description, including the definitions and criteria used for co-translation and ncORF classification. The limitations of the dataset should also be discussed more explicitly, especially regarding the heterogeneity of public Ribo-seq datasets, technical factors influencing detection sensitivity, and the interpretation of variable detection frequencies across samples.

      In addition, several conclusions remain largely descriptive, and the distinction between novel findings and confirmation of previous observations should be clarified more carefully. Conclusions should be framed strictly within the limits of the presented data and positioned appropriately relative to prior work, with suitable citation to avoid overstating novelty.

      We therefore ask the authors to refine the technical descriptions, ensure that all methods and analytical criteria are presented unambiguously, and expand the Discussion to clearly articulate the limitations of the dataset and analysis. The conclusions should also be revised to reflect an appropriately cautious interpretation of the findings.

      The primary strength of this study lies in the scale and standardization of the dataset as a community resource. Given this substantial resource value, we believe the manuscript could become suitable for publication provided that the issues outlined above are addressed clearly and transparently. With these revisions, the work will provide a useful foundation for future studies in this area.

      We therefore invite you to submit a final revised version addressing the points described above.

      We thank the Editor for the careful assessment and constructive guidance. In the final revision, we have clarified all key methodological definitions and analytical criteria, expanded the Discussion of dataset and detection limitations, and revised the conclusions to avoid overstatement. We believe these changes improve the technical rigor, transparency, and overall value of the manuscript as a community resource.

      Reviewer #1 (Recommendations for the authors):

      The authors have made efforts to address most of the previous concerns, and several points have been clarified or improved in the revision. However, in a number of cases, the responses rely more on acknowledgment and reframing rather than substantive analytical strengthening. Overall, the manuscript is improved, particularly in terms of clarity, transparency, and positioning of claims. I support its publication and look forward to seeing how the field engages with and discusses these claims.

      We appreciate the reviewer’s support for publication.

      Reviewer #2 (Recommendations for the authors):

      While the authors have made commendable efforts to revise the manuscript and address previous concerns, the revised version still falls short of fully resolving several critical issues regarding data interpretation and methodological transparency. I recommend the following modifications before the manuscript can be considered for publication:

      (1) Although the authors have annotated the detection frequencies of individual sORFs in the revised

      Supplementary Table 3 and Fig. S1B, the biological and technical implications of these data require further clarification:

      (a) As the data demonstrates, even the most abundant sORFs were detected in no more than half of the samples. If the authors attribute this low detection rate to technical limitations (e.g., batch effects, sequencing depth, or threshold stringency), this must be explicitly discussed and annotated in the main text to prevent readers from misinterpreting this as low biological penetrance.

      We thank the reviewer for this constructive comment. We have added a paragraph to the Discussion explicitly addressing the potential technical factors underlying the variable detection frequencies to avoid overinterpreting these frequencies as biological penetrance.

      (b) The authors did not fully address my previous query regarding tissue specificity. Given the diverse and complex origins of the analyzed ribo-seq datasets, it is crucial to know whether any of these sORFs are tissue-specifically translated. The authors should analyze and state whether certain sORFs are exclusively detected in specific sample categories (tissues/organs), and whether this translation pattern aligns with the tissue-specific expression of their corresponding host transcripts.

      We thank the reviewer for raising this important point. Strict tissue-exclusive translation is difficult to establish from heterogeneous public Ribo-seq datasets, as gene expression is inherently stochastic and most genes have some probability of being expressed across tissues, although expression levels may vary substantially between tissues. Moreover, failure to detect an ncORF in a given tissue may reflect low expression or insufficient sequencing depth rather than true biological absence. We therefore avoid making definitive claims about tissue-specific translation and instead quantify variation in ncORF expression across tissues using a tissue specificity index.

      (2) Echoing the concerns raised by Reviewer #1, I remain concerned that the observed uORF-CDS cotranslation might be a computational artifact or false positive. The current Methods section lacks sufficient detail on how "co-translation" was strictly defined and quantified. I strongly recommend that the authors include a schematic diagram (e.g., in Figure 6 or supplementary figures) that explicitly details their analytical strategy, statistical thresholds, and evaluation criteria for defining co-translation. As was pointed out, it is well-established that uORFs typically exert an inhibitory effect on the translation of the main CDS. To validate the accuracy and robustness of their analytical pipeline, the authors should use their collected dataset to demonstrate the prevalence and nature of this canonical inhibitory phenomenon. Successfully capturing this expected repression would serve as a crucial positive control for their methodology. While the authors provided a theoretically acceptable mechanistic model in the text to reconcile co-translation with uORF-mediated repression, this hypothesis currently lacks literature support. The authors must cite relevant prior studies that support this specific regulatory dynamic to strengthen their argument.

      We thank the reviewer for this important comment. We have further clarified the definition, detection criteria, and statistical framework for co-translation in the Methods, and have made the complete analysis code publicly available to facilitate reproducibility and independent evaluation. We have also added relevant literature supporting the proposed regulatory interpretation clarifying the relationship between our observations and the established inhibitory effects of uORFs.

    1. Author response:

      The following is the authors’ response to the original reviews.

      eLife Assessment

      This study presents valuable findings regarding cardiac and autonomic effects of seizures and epilepsy, with relevance to sudden unexpected death in epilepsy (SUDEP). They present solid evidence that genetic deletion of the potassium-chloride cotransporter in hypothalamic corticotropin-releasing hormone (CRH) neurons exacerbates bradycardia and enhances autonomic disturbances in a mouse model of temporal lobe epilepsy. However, the evidence that this deletion produces chronic hyperexcitability of the hypothalamic-pituitary-adrenal axis was incomplete, leaving a mechanistic gap. This work will be of interest to neuroscientists working on epilepsy, the HPA axis, and autonomic control.

      We thank the editors and reviewers for their feedback. Although the loss of Kcc2 from CRH neurons in Kcc2/Crh mice has been confirmed (Melon et al., 2018) and leads to HPA axis hyperexcitability in response to stress or seizures, it does not chronically drive HPA axis hyperactivity in unstressed conditions (Basu et al., 2024).

      The following details have been added regarding the Kcc2/Crh model. We now describe the Kcc2/Crh as “hyperreactive” rather than “hyperexcitable/hyperactive” throughout the manuscript.

      -In the Introduction: “This loss of Kcc2 in CRH neurons has been previously confirmed and shown to cause an exaggerated HPA axis response to stress that is absent in baseline conditions (Basu et al., 2024; Melon et al., 2018)”

      -In the Discussion: “This aligns well with lack of elevated plasma corticosterone at baseline in Kcc2/Crh mice, compared to WT, because elevated PVN<sup>CRH</sup> neuron activity should otherwise increase this signal (Basu et al., 2024).”

      -In the Discussion: “Most notable, our model utilizes a developmental strategy to knock out Kcc2 from CRH neurons, which has been confirmed previously (Melon et al., 2018).”

      Public Reviews:

      Reviewer #1 (Public review):

      This study could be improved with a more thorough assessment of heart rate, blood pressure and breathing during and following the seizures, and in particular the fatal event.

      Post-ictal HR data are now included in the Results, Table 2.1 and Figure 2. Overall, pronounced bradycardia that occurred near seizure termination was followed by recovery of HR to pre-ictal baseline in the early post-ictal period (30 sec). In Results: “Independent of genotype, HR recovered to baseline levels during the immediate post-ictal period (0-10 sec, Fig. 2G; 10-30 sec, Fig. 2K).

      In pilot work, we determined that HR during spontaneous seizures were fundamentally different than HR during status epilepticus (see Author response image 1). Therefore, it was critical for us to examine HR during spontaneous seizures. We previously published that Kcc2/Crh+KA mice have a rate of 1-2 seizures per day. To limit additional stressors and seizure provocation, we employed radio telemetry (over tethered systems) and opted out of carotid instrumentation for BP as well as restricted environments of plethysmography chambers for these assessments of HR. After determining that heart rate was different between our mouse lines, we tested whether this change was mediated by central circuits regulating HR (ie: baroreflex, Bezold-Jarisch reflex) (Fig. 3, 4, 5).

      Author response image 1.

      In Discussion: “Although the present study includes only non-fatal seizures, our report of HR during spontaneous seizure events supports work suggesting physiological events during non-fatal seizures predict SUDEP risk (Lamrani et al., 2023; Ryvlin, Nashef, & Tomson, 2013; Schuele et al., 2011). It remains to be determined if ictal events during fatal and non-fatal spontaneous seizures are different and future studies could help clarify any distinctions. Our examination focused on HR (and not respiration or BP). Whether exaggerated BJR-mediated HR response co-occurs with greater magnitude BJR-mediated apnea and hypotension remains to be determined.”

      It is unclear if the bradycardias were spontaneous or a result of preceding central or obstructive apneas, oxygen desaturations, hypercapnia, arrhythmias, or other possible triggers.

      Our work demonstrates the occurrence of ictal bradycardia whereas identifying precipitating factor(s) and interaction(s) of this phenomenon will require alternate approaches. Normal activation of hypoxic and hypercapnic ventilatory responses would be expected to increase HR. However, whether these chemoreflex circuits undergo remodeling in Kcc2/Crh mice remains unknown. Obstructive apnea via laryngospasm can cause reflex bradycardia, but we did not record airflow or respiratory EMG in these studies to determine the existence of obstructive apnea. More testing is merited.

      In Discussion, “…Additional seizure-related disturbances such as central or obstructive apneas may contribute to BJR activation. Hypoxia, which could result from ictal apnea, is known to increase excitatory neurotransmission to cardiac vagal motor neurons that cause vagal bradycardia (Griffioen et al., 2007) and induces platelet activation (Tyagi et al., 2014) which is considered the main source of circulating serotonin for the BJR. As such, hypoxia resulting from apnea may increase likelihood of exaggerated BJR during seizures. Consistent with this…”

      Considerable prior work in the literature suggests SUDEP could be mediated, in some patients, by a burst of parasympathetic activity to the heart. Were the heart rate changes in these animals during seizures inhibited or blocked by atropine or atenolol?

      With this study targeting spontaneous seizures we were unable to test acute pre-treatment with atropine or atenolol. We did observe reduced mortality in Kcc2/Crh+KA mice that underwent chronic parasympathetic blockade via osmotic minipump of methylscopolamine (Figure 5).

      In Discussion:

      “Chronic inhibition of vagal parasympathetic motor output (the driver of BJR reflex bradycardia) improved mortality by 10% in Kcc2/Crh mice. Although this improvement provides some hope for patients at high risk for SUDEP with no treatment options, additional avenues of investigation are needed to more directly link seizure-related bradycardias to vagal parasympathetic motor output.”

      The injection of the 5HT agonist phenylbiguanide into the right jugular is not a selective approach for activating the Bezold Jarisch Reflex (BJR), which is caused by increased activity of intracardiac sensory neurons (generally activated with is chemia or a combination of low preload with high contractility). The results should be interpreted more cautiously, as a response to systemic administration of phenylbiguanide only.

      BJR can be experimentally triggered with intravenous infusion of various compounds including veratrum alkaloids (Cramer, 1915), 5HT (Fozard 1983), or 5HT3R agonists (Verberne & Guyenet, 1992). We now specifically refer to BJR in our study as that induced by PBG (a 5HT3R agonist), as others have done (Yamano et al., 1995; PMID: 8786638) and acknowledge endogenous BJR activation in the discussion.

      Added to the results: “As dysfunction of serotonergic signaling is implicated in the pathophysiology of SUDEP (Richerson & Buchanan, 2011), we investigated the Bezold Jarisch Reflex (BJR) (Fig. 5), a cardioinhibitory reflex that is reliably triggered experimentally by activation of cardiopulmonary vagal afferents containing serotonin type 3 receptors (5HT3R) (Fozard 1983; Yamano et al., 1995).”

      Added to Discussion: “Although our report is the first to link BJR to SUDEP, serum serotonin levels are elevated following generalized seizures (Murugesan et al., 2018), likely via release from activated platelets (Cloutier et al., 2018). This surge in serum serotonin could lead to endogenous activation of BJR, as bolus intravenous infusion of serotonin reliably triggers BJR experimentally (Fozard 1983; Whalen et al., 2000).”

      Reviewer #2 (Public review):

      Some of the conclusions may be a bit overstated as is and would benefit from more discussion and perhaps additional data.

      Post-ictal HR data are now included in the Results, Table 2.1 and Figure 2.

      The Discussion now includes more details regarding respiration, BP, obstructive apnea, properties of the BJR, and distinctions in seizure type based on whether evoked or lethal.