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    1. eLife Assessment

      Huntington's disease is caused by excessive polyglutamine repeats in the protein huntingtin (HTT). In this important study, Lixiang et al use high resolution microscopy to study the effect of HTT aggregates on intracellular organelles. While the evidence remains incomplete, the study proposes that aggregates affects the scaffolding of the Golgi apparatus.

    2. Reviewer #1 (Public review):

      The authors have provided responses and additional data, but these revisions have not adequately resolved the major concerns raised in my previous review. In particular, the evidence supporting the central premise of the study-the structural and functional relationship between polyQ assemblies and the Golgi apparatus-remains insufficient. Much of the cell biological evidence is descriptive, and the observations are not integrated into a convincing mechanistic model. Most importantly, the proposed polyQ HTT-induced Golgi dysfunction (Golgipathy) has not been convincingly established. Several findings could be alternatively explained by the association of polyQ HTT with the Golgi and the Golgi's known sensitivity to cellular perturbations. Significant concerns also remain regarding the interpretation and quantification of microscopy images, as well as the clarity of several figures. Consequently, my overall assessment remains unchanged.

      Comments on the Authors' Responses

      (1) Golgi localization of polyQ HTT

      This is a central claim of the study and therefore requires particularly rigorous and convincing evidence. Although the authors have performed additional immunostaining using different HTT antibodies, the EGFP-tagged HTT exon 1 fragments do not appear to localize to the Golgi. Why did the authors not examine the localization of EGFP-tagged full-length HTT containing an expanded polyQ tract? Such an experiment would provide an important independent validation of their immunostaining results.

      (2) 3D rendering

      This concern has not been adequately addressed. Since the authors acknowledge that the vasculature-like features are artifacts, these features should be removed to avoid misleading readers. Furthermore, it remains difficult to correlate the rendered structures with the corresponding boxed regions in the original fluorescence images.

      (3) Quantification of area and volume

      This concern remains unresolved. If polyQ assemblies consist of fine meshworks with features below the optical resolution, these structures would appear as continuous fluorescent regions rather than resolvable networks. Consequently, the measured fluorescent area or volume would not accurately represent the physical space occupied by the assemblies.

      (4) Interpretation of structural features

      This concern has not been adequately addressed. The proposed spindle-like and ring-like structures remain difficult to distinguish convincingly in the presented images.

      (5) Mitotic fragmentation

      The authors appear to have misunderstood my concern. The critical question is whether the polyQ assemblies in the same cells were intact before entering mitosis and subsequently underwent fragmentation. Comparing different interphase and mitotic cells cannot establish this sequence of events. Furthermore, Golgi fragmentation during mitosis is a well-established phenomenon. Therefore, the observed fragmentation of Golgi-associated polyQ assemblies may simply accompany normal mitotic Golgi disassembly rather than represent a distinct property of polyQ assemblies.

      (6) Nuclear localization claims

      The presented images suggest, at most, partial nuclear localization of polyQ assemblies. Nuclear accumulation appears evident in some cells but absent or much less pronounced in others.

      (7) Drug treatment and data interpretation

      My previous concerns remain unresolved. Figure 3E is still inappropriately plotted and may mislead readers. Furthermore, the rationale for selecting Onjisaponin F remains insufficiently justified.

      Additional Concern: Insufficient Description of SIM Microscopy

      In their response to Reviewer #1, Comment 3, the authors explicitly state that "Our SIM resolution reaches approximately 64 nm." However, this specification is not reported or substantiated in the manuscript. Neither the main manuscript nor the supplementary methods provide essential technical information about the SIM imaging system, including the microscope manufacturer and model, objective lens and numerical aperture, acquisition parameters, and controlling software. This is a substantial methodological omission.

    3. 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 RNAseq 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.

      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.

      Comments on revised version.

      In this revision, the authors have addressed all the comments and the manuscript has been better improved.

    4. 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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      Han, X., Ma, L., Gu, J., Wang, D., Li, J., Lou, W., Saiyin, H., and Fu, D. (2021). Basal microvilli define the metabolic capacity and lethal phenotype of pancreatic cancer. J Pathol 253, 304-314. Hexige, S., Ardito-Abraham, C.M., Wu, Y., Wei, Y., Fang, Y., Han, X., Li, J., Zhou, P., Yi, Q., Maitra, A., et al. (2015). Identification of novel vascular projections with cellular trafficking abilities on the microvasculature of pancreatic ductal adenocarcinoma. J Pathol 236, 142-154.

      Hickman, R.A., Faust, P.L., Marder, K., Yamamoto, A., and Vonsattel, J.P. (2022). The distribution and density of Huntingtin inclusions across the Huntington disease neocortex: regional correlations with Huntingtin repeat expansion independent of pathologic grade. Acta Neuropathol Commun 10, 55.

      Khoshnan, A., Ko, J., and Patterson, P.H. (2002). Effects of intracellular expression of anti-huntingtin antibodies of various specificities on mutant huntingtin aggregation and toxicity. Proc Natl Acad Sci U S A 99, 1002-1007.

      Klein, F.A., Zeder-Lutz, G., Cousido-Siah, A., Mitschler, A., Katz, A., Eberling, P., Mandel, J.L., Podjarny, A., and Trottier, Y. (2013). Linear and extended: a common polyglutamine conformation recognized by the three antibodies MW1, 1C2 and 3B5H10. Hum Mol Genet 22, 4215-4223.

      Klumperman, J. (2011). Architecture of the mammalian Golgi. Cold Spring Harb Perspect Biol 3. Ko, J., Ou, S., and Patterson, P.H. (2001). New anti-huntingtin monoclonal antibodies: implications for huntingtin conformation and its binding proteins. Brain Res Bull 56, 319-329.

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    1. eLife Assessment

      This valuable study examines the relationship between simultaneous LC single-unit recordings and pupillometry, both within and across baseline and evoked epochs, finding that cross-epoch relationships are unreliable. The evidence is convincing and suggests that care should be taken when interpreting pupil responses as reflecting LC activity. This manuscript will be interesting to basic and clinical researchers working in cognitive and decision neuroscience as well as computational psychiatry.

    2. 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.

      Comment on revised version.

      The revised manuscript has addressed previously raised concerns. This is a valuable contribution to the field.

    3. Reviewer #2 (Public review):

      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. In addition, by demonstrating that the results remain robust in the subset of neurons exhibiting significant baseline LC-pupil relationships, the authors further strengthen their conclusions.

      As pupil size is increasingly used as an index of arousal, these findings are particularly 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

      Comments on revised version.

      The authors have thoroughly addressed my previous comments, and I appreciate their efforts in revising the manuscript.

    4. 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. eLife Assessment

      This important study establishes a zebrafish model to investigate the development of interoceptive circuits involved in the regulation of heart rate and their functions in vivo, in an intact vertebrate body. Using a combination of targeted functional imaging, manipulation, and mathematical modeling, the study presents compelling evidence for the staggered development of motor and sensory feedback elements of the interoceptive circuit.

    2. 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 to how the heart-brain communication develops early in life. The paper describes a three staged 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.

    3. 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 (Fig 1C, D, supp. Fig 1C-F) and increases over development. This has been quantified in supp. Fig 2.

      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 Figs 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, it 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 have not been probed. Some other known modulatory influences on the cardiac rhythm are mentioned in the text, however exploring these pathways would be outside the scope of this study.

      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. The authors have included a section on the limitations of the model, where they importantly clarify that the proposed mechanisms, although likely, do not establish direct synaptic connectivity, for example whether the brainstem neurons identified for their functional roles are the ones that give rise to efferent projections via the motor vagus nerve. The addition of clear labels in Fig 9 also helps the reader interpret relationships between model components more clearly.

      To conclude, this study establishes the larval zebrafish as a tractable in vivo model to study heart-brain interoceptive and regulatory circuits through development and describes a detailed mechanistic framework to take forward.

    4. 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. eLife Assessment

      This paper provides a useful assessment of the role of macrophages in the development of functional paw withdrawal, which is a feature in the mouse model of vincristine-induced peripheral neuropathy (VIND). The authors present solid data suggesting a role for E-selectin as a critical molecule promoting VIPN, acting via immune cell recruitment and inflammasome-mediated signalling; however, the role of NLRP3 in this model is based on in vitro assays. This study will be of interest for immunologists.

    2. Reviewer #1 (Public review):<br /> <br /> The authors have included a number of written edits to their manuscript that improves the readability of the text and also provides clarity on their experiments and findings. Together these changes better highlight the role of E-selectin as an upstream driver of innate immune inflammation in vincristine-induced neuropathy.

      A comment I made in the first review round (previous comment #3) was that NLRP3-inhibitors were only used in vitro and not used in vivo to confirm that it is this specific innate immune complex that contributes to the pathway. Instead, the downstream inflammatory mediator IL-1b was inhibited in vivo using anakinra (and not tested in vitro). The authors have referred to their previous work on NLRP3 inhibitors in their vincristine model and modified some text to delineate that in vivo, only a role for IL-1b was investigated in the E-selectin experiments in the current paper. It would be useful to clearly distinguish throughout the text, that the role of NLRP3 was only confirmed in macrophages in vitro. E.g. lines 44, 87, 740 and 773 discuss their findings on NLRP3 in macrophages, but do not specify that this is in vitro data.

      MCC950 is also known as CP-456773 and CRID3, which would be helpful to mention the first time the inhibitor is introduced as all versions of the name are used in current publications.

    3. Reviewer #2 (Public review):

      Summary:

      This is an interesting mechanistic study on the topic of Vincristine-induced peripheral neuropathy (VIPN). It defines E-selectin as critical molecule of promoting VIPN, acting via immune cell recruitment and inflammasome-mediated signalling.

      Using antibody treatments, genetic models and in vitro studies, the authors convincingly show that E-Selectin is a driver of VIPN.

      Strengths:

      In vivo studies are robust and useful. Antibody studies as well as the inflammasome-related work are very well done.

    4. 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. eLife Assessment

      This useful study examines fine-scale population diversity in marine Pelagibacterales using an extensive collection of O-chain biosynthesis cluster (OBC) sequences as markers of lineage abundance across Mediterranean metagenomes. There is solid evidence for OBC diversity and reproducible associations between lineage abundance and environmental conditions, particularly water-column depth. However, the evidence supporting the study's broader conceptual claims is currently incomplete; in particular, it remains unclear whether OBC-defined lineages adequately represent distinct clonal genomic backgrounds, whether the observed co-variation reflects more than conventional ecological niche partitioning and whether the proposed consortia constitute biologically meaningful functional units. The interpretation of frequency modulation as differing from existing interpretations of microbial ecotypes goes beyond what the current data establish; stronger genomic and functional evidence would be required to support its more ambitious conclusions.

    2. 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.

      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.

    3. 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.

    4. 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. eLife Assessment

      This valuable study uses endogenous HiBiT tagging to show that the autophagy receptor p62 is released from cells in membrane-bound vesicles at a rate comparable to LC3B, with release increasing when lysosomal degradation is blocked, depending on core autophagy genes and on p62's ability to self-assemble. The evidence is solid, but it rests mostly on single experiments; some results differ between figures, and the vesicles themselves are not characterized. The proposed link between this export and the NRF2 stress response is plausible but correlative, as the tools used to test it are broad.

    2. Reviewer #1 (Public review):

      Summary:

      The authors further develop in this article an approach to quantify the release of EV cargo by fusing the HiBiT fragment of nanoluciferase to the cytosolic end of various proteins, via knock-in (rather than overexpression) in HEK293 cells. They have previously published this approach for several EV-associated proteins (Maeda 2024: tetraspanins, flotillin1, syndecan), or the autophagosome-associated protein LC3, or the mitochondrial protein Tom20 (Saito 2026). They now expand it to p62, another protein involved in the autophagy pathway. Their results convincingly show that p62 is indeed released extracellularly, at low levels spontaneously and mainly associated with larger/denser EVs (10k pellet), and much more after blocking lysosomal activity by BafA1 and mainly in small EVs (100K pellet), as well as in a free form.

      Strengths:

      The authors produce a lot of interesting experiments using knock-in or expression under the control of a mutated CMV promoter to avoid high overexpression of the studied proteins. They nicely decipher the molecular machinery involved in this secretion.

      Weaknesses:

      I am a bit unsatisfied with the way all experiments are presented, as bar graphs show individual dots of technical replicates, rather than individual dots of independent experiments (the authors specify that each experiment was performed at least twice). This representation minimizes the potential inter-experiment variability: for instance, when comparing Figure 3B where relative secretion (in BafA1) is around 25 for 10K vs 140 for 100K, and fig 4A where it is 50 for 10K vs 30 for 100K, there is a 5 fold difference of the rate of secretion in 100K, and the ratio 10K/100K is inversed between the experiments of Figure 3 and Figure 4. It would therefore be highly recommended to show all the figures of secretion rate with individual symbols for each individual experiment (calculating the mean of technical replicates for each experiment).

      It is also unclear if the truncated CMV promoters that induce a not-too-high overexpression of the p62 mutants in Figure 5 are also used for Figure 6 (KEAP and mutants) and in Figure 7 (Rab27 and mutants). If not, can the authors justify that, for these molecules, high overexpression does not preclude interpretation of the results?

      An important technical detail is missing in the WB of Figure 4B, where the authors quantify p62-HiBiT in extracellular vesicle pellets: quantification is done in pellets as compared to the cell lysate, but I did not find how the gels were loaded: equal amounts of protein from cells and pellets, or pellets coming from the same number of producing cells loaded in the gel, or other? Also, this experiment seems to have been performed and quantified only once.

    3. Reviewer #2 (Public review):

      Summary

      In this work by Saito et al., the fate of p62 is studied. Under normal cellular conditions, p62 acts as a cargo receptor, binds cargo, and is recruited to the growing autophagosomal membrane via its interaction with LC3. When lysosomal function is inhibited, these structures can also be secreted in a process called secretory autophagy. This valuable paper tries to address the fate of p62. By fusing a HiBiT peptide at the C-terminus of endogenously expressed p62, extremely low amounts of p62 can be detected in the media surrounding HEK293 cells. Most of the secreted p62 was found in membrane-enclosed structures that are continuously secreted from the cells, a process that is dramatically increased after lysosomal inhibition via BafA1. This process is ATG5- and FIP200-dependent. Interestingly, this process depends on p62's ability to oligomerize, but does not depend on its ability to bind LC3, KEAP1, or poly-ubiquitin. KEAP1 was also detected in these membrane-enclosed vesicles, and its secretion did not depend on p62 interaction, but was also increased upon lysosomal inhibition. The exact secretion mechanism was not fully elucidated in this manuscript, but it was found to be RAB27-dependent. Future studies will be needed to fully map the cellular mechanism behind p62 secretion.

      Strengths

      (1) Fusion of the HiBiT peptide to p62 allows for careful quantification of secreted p62 and is of interest to the wider research community as it is an interesting strategy.

      (2) Work on endogenous expression levels of p62 avoids artifacts due to overexpression and adds to the conclusions of the paper.

      (3) Several mutants were analyzed to assess which binding partners of p62 are co-sorted to secreted vesicles.

      Weaknesses

      (1) The exact form of p62 is not clear. The fractions analyzed are pellets that sedimented at two different centrifugation speeds, supernatant, and whether the signal increases upon detergent addition. No effort was made to do further analyses on what these fractions contain or what they look like.

      (2) As pointed out in the discussion, p62 needs to oligomerize to be sorted to these vesicles, and this process is not dependent on LC3 binding. No efforts were made to exclude binding to other cargo receptors via mutation or knockdown, i.e., NBR1 D50R.

      (3) The supernatant was not fully analyzed. It is unclear whether "soluble" p62 secretion is also continuous, whether it depends on ATG5/FIP200, is affected by lysosome inhibition and whether is it potentially decreased upon p62 oligomerization.

      (4) Besides p62 and KEAP1, the contents of the vesicles were not analyzed, and it is unclear whether they contain lipidated LC3 or other autophagy proteins.

      (5) Some details of the experiments are slightly inconsistent. For instance, in Figure 3C, close to zero p62 is detected in the pellet fraction in the absence of detergent. In Figure 4, there is some p62 detected under those same conditions. I believe both of those experiments were done under the same conditions, yet yielded slightly different results. This does not detract from the conclusions of the paper, however.

      Conclusion/discussion

      The work presented is interesting and sheds light on an under-studied cellular function. The method used in this manuscript is very interesting and has the potential to be widely applicable to answer other research questions in other low-protein concentration scenarios. It will be very interesting to see which other autophagy proteins get secreted and what cellular mechanism is used to achieve this.

    4. 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. eLife Assessment

      This study uses a new behavioural paradigm and a helpful analysis framework to study prey capture in a complex environment, providing a valuable approach with methods that are inexpensive and easily replicable for future work. However, the claims of the paper that the behaviour is memory-guided are incomplete, as alternative explanations for the observed behavioural patterns have not been ruled out. The modelling is a reasonable demonstration that a small set of rules can produce the observed patterns, but model predictions are not compared to actual data or compared against alternatives.

    2. Reviewer #1 (Public review):

      Summary:

      Schneider et al. use a reproducible and inexpensive behavioral paradigm to study prey capture in a cluttered environment. They compare mice hunting cockroaches in a sparse, circular arena with no obstructing objects versus a cluttered arena. The authors set out to define search and pursuit phases in the cluttered environment. They claim to find signatures of short-term memory within the search phase that they propose should not be involved in uncluttered environments. They also create an agent-based framework for prey capture with and without additional objects, and predict that trials should take longer when objects are included. They provide the agent-based model with a component that prevents revisiting the same object and predicts big differences between object order visits during search and pursuit. They also create machine learning classifiers on mouse keypoint data with the goal of measuring interactions with specific objects.

      Strengths:

      The experimental set-up is excellent and broadly useful as it uses inexpensive objects to perform easily repeatable experiments. Further, the model has interesting characteristics and is well constructed.

      Weaknesses:

      The major weakness of this manuscript is the lack of comparisons throughout the text. For example, all of the claims depend on the assumption that mice are searching for roaches when they are not pursuing the roach: these non-pursuit times could be anything, including grooming, sleeping, etc. But without a comparison to animals in the same physical environment who are not searching for roaches, these claims cannot be supported with evidence. Similarly, all of the claims about complexity being required or revealing memory need to be compared to a lack of complexity to support those claims with evidence. The authors note they have both naive mice in the cluttered arena that did not hunt and their baseline data from uncluttered environments also exist, and these comparisons would allow them to address and potentially support their claims.

      Additional context:

      This manuscript lacks sufficient context from a few related areas of the literature: thigmotaxis and novel object recognition, as well as mouse proclivities (e.g. mice prefer to move forward and not backwards (Rosenberg et al. 2021). While thigmotaxis is acknowledged, it is referenced only in passing and not evaluated as a null model for how animals are behaving. Without comparisons to uncluttered or non-hunting mice, thigmotaxis, novel-object recognition, and other mouse proclivities like preferring forward movement could explain all of their behavior without a memory component

    3. Reviewer #2 (Public review):

      Summary:

      Schneider et al. ask whether adding environmental complexity to a simple prey capture task reveals learning that the simple task does not engage. They train six mice to hunt cockroaches in an empty arena for about ten weeks and then test them for eight days in an arena with objects that block movement and vision and give the prey places to hide. In the enriched arena, capture success increases and trial duration decreases across the eight days. The authors divide the behavior into three states: pursuit, search, and abandonment. Search dominates the trials, followed by pursuit. Interestingly, the time spent in search and pursuit does not change with experience. They show that pursuit kinematics are largely stable, whereas search speed and its variability increase. During search, mice prefer sequences of three distinct objects over returning to the object they just visited, and this preference is absent on the first day. Mice also shift their search toward the ping-pong balls, where roaches are most often found, and toward actions that displace the balls and flush hidden prey. A minimal agent-based model with short-term memory of visited objects and object-specific search values reproduces these patterns. The authors conclude that learning in a complex environment is expressed in search rather than pursuit, and that unenriched arenas can support expert performance without engaging memory-guided search.

      Strengths:

      Laboratory versions of ethological tasks often remove the environmental structure that shapes the behavior in nature, and the authors make a good case that this matters. The paradigm is simple, inexpensive, and easy to reproduce in other laboratories. The object-referenced ethogram links each action to the object it is directed at, which is a useful addition to unsupervised approaches. The authors combine several independent analyses (state segmentation, kinematics, object sequences, object occupancy, and classified object interactions), and these point in a consistent direction.

      Weaknesses:

      The most important weakness is a missing control where mice experience the objects without the prey. Mice were tested in the enriched arena with prey from the first day the objects were introduced. Many of the changes described in search, including the increase in speed and variability (Figure S4), the shift in object occupancy (Figure 5), and the change in object interactions (Figure 7), could reflect habituation to the new objects in the enriched arena rather than learning about prey behavior. A group exposed to the objects without prey, or pre-exposed to the objects before prey are introduced, is needed to attribute these changes to prey capture.

    4. Reviewer #3 (Public review):

      Summary:

      Predator-prey interactions indicate important changes in behavior after the addition of clutter to an environment, whereas many task designs for rodents, including predator-prey, are open field. The environment has a big effect on behavior in ways currently not appreciated by the scientific community due to challenges in recording natural behavior with clutter.

      Strengths:

      A rare study of rodent predator-prey interaction in clutter.

      Weaknesses:

      (1) The arena size is only approximately 3 body lengths. Clearly, a search task when everything is so nearby is affected in numerous ways.

      (2) The empirical result that in search, X-Y-Z object sequences are more common than X-Y-X is solid. But the interpretation, based on the model, that this is due to memory is not. What if the mouse policy is: go toward the location giving the strongest prey-related cue? As it gets to that location, the prey moves. The prevalence of X-Y-Z sequences over X-Y-X then just represents the prey not returning to the original object it ran from (probably a good idea).

      (3) The shuffle test (and model) suggests that memory is sufficient, but it does not demonstrate that memory is necessary to obtain the observed patterns. Again, the obvious prey-driven non-revisit is possible.

      (4) The authors seem to hedge the memory claim (e.g. p.19 "complex behavioral organization can emerge") and at other times not ("More broadly, our findings highlight the importance of memory"). It would be good for them to be clearer about what is and is not supported by their empirical findings (or to add an analysis that shows cued pursuit cannot explain the absence of X-Y-X).

      The field needs more of this kind of work (namely, how animals operate in more naturalistic environments with a naturalistic task). Within rodents, there has not been a lot of it outside of the new Emily Dennis preprint (Shettigar et al. 2026), and the 2024 Dombeck Cell Reports and 2020 simulation results by MacIver, all predator-prey analyses with clutter (which make many of the same points as the author in the intro and discussion).

    1. eLife Assessment

      This paper presents important data from a very high-resolution MRI scan of the human hippocampus. The data, which is openly shared, convincingly shows that diffusion MRI at high resolution can reveal a lot of the known mesoscale anatomy. This study will be of interest to scientists who use neuroimaging to measure brain structure and function.

    2. Reviewer #1 (Public review):

      The authors present results from an ultra-high-resolution ex vivo MRI scanning of hippocampi. Scanning was extensive, and the figures are impressive. The description and scope of this resource appear a bit limited, however, as the data do not seem to be made openly available.

      (1) Title:

      The title is a bit ambiguous as "virtual histology" has also been used in an imaging-transcriptomics context (eg https://jamanetwork.com/journals/jamapsychiatry/fullarticle/2769908). I would suggest rewording or dropping everything after 14.1T.

      (2) Abstract:

      I would reword the statement "representing, to our knowledge, the highest resolution reported for human brain diffusion MRI" to "representing one of the highest resolutions reported<br /> for human brain diffusion MRI"

      (3) Introduction:

      When talking about selective vulnerability across disorders, the authors are encouraged to specifically mention AD, schizophrenia, and temporal lobe epilepsy, as these are conditions with a close association to hippocampal structural damage.

      (4) Introduction:

      It will, for balance, nevertheless be important in the introduction to outline that high-field in vivo MRI at 3-7T can achieve resolutions at least in the order of a few hundred microns. Such resolution, combined with automated image processing, can resolve subregional detail of the hippocampus. See for example https://pubmed.ncbi.nlm.nih.gov/31245529/, https://pubmed.ncbi.nlm.nih.gov/40654693/, https://www.nature.com/articles/s41592-025-02783-3 etc. As such, the statement that "clinical MRI fails to resolve the mesoscopic and microscopic organization essential for characterizing complex structures" is only partially correct, and I would suggest toning this down.

      (5) Methods:

      The methods appear relatively brief. The authors are encouraged to provide further details on the specific segmentation protocol that was used. Did multiple raters perform substructural segmentation? How high was inter- and intra-rater reliability?

      (5) Methods:

      How far is a diffusion MRI acquisition with 20 directions viable for tractography? I understand that multiple averages were used, but 20 directions appear limited to reliably sample 3D space and to, e.g., resolve complex, crossing, and kissing fibers.

      (6) Results:

      The figures are very nice, and the authors are also commended for doing such an ambitious imaging acquisition. Currently, the results appear a bit qualitative and descriptive, however. Ideally, and for greater impact, a resource such as the one presented should be made openly available for the research community, as this allows for independent verification and greater uptake of the study results. Other resources, e.g., AHEAD, BigBrain, etc. were shared with the international research community, so it would be great to see the same for this dataset.

    3. Reviewer #2 (Public review):

      This work uses extremely high-resolution diffusion MRI to reveal hippocampal layers and fiber organization in ex vivo tissue, showing compelling (and beautiful) evidence that this dMRI microscopy can truly act as "3D virtual histology" that gives information and signatures conveyed through a number of traditional stains.

      Specifically, they scan hippocampal tissue blocks (one from a control donor and one from an AD donor) using a 14.1T scanner, and compare diffusion maps and 3D tractography against axons, dendrites, amyloid, and tau. Acquisition is an impressive 50x50x100 µm resolution over 78 hours of scanning. They show (i) clearly distinguished hippocampal layers, (ii) this clear separation is lost at> 100 µm and beyond, (iii) tractography depicts several pathways consistent with the perforant path, mossy fibers, and Schaffer collaterals, (iv) the AD specimen showed weaker layer contrast, structural discontinuity, and disorganized trajectories (which agree with histological observations).

      Overall, I very much enjoyed reading this work; it read like a fully polished paper. I recommend only what I consider very minor revisions. And I would consider none a "requirement" for future revisions, as they are mostly stylistic preferences, small clarifications, and organizational choices.

      (1) The first results section "Diffusion MR microscopy protocol and multi-modal dataset of the human hippocampus" describes "methods". It contains/describes the acquisition, resolution, staining, and layer segmentation/naming (whereas the next section is the first results showing that diffusion microscopy allowed clear separation of layers).

      (2) There are some terms or scales that are introduced but may be ambiguous or not clear to readers. I'm assuming "diffusion MRI microscopy" is diffusion MRI on the scale of microns (or 10s of microns). "Meseoscopoic and microscopic" scales might be clarified.

      (3) "Structure tensor analysis" is introduced (and in the methods) without giving the reasons "why" this is used. The authors are using it to validate and compare orientation. The methods are described, but it isn't immediately intuitive what you are using ST analysis for (unless one is already familiar with this image processing technique).

      (4) This does not need to be addressed in the paper, but a recommendation: with 1mM Gd, you can likely get by with a much lower TR with 3D EPI, allowing much higher SNR-time efficiency, and it may be beneficial to avoid averaging and pursue more unique directions.

      (5) The image showing TDI might benefit from scaling each result independently - the 400 µm, by definition, has fewer streamlines per voxel, and is darker (and less visually appealing).

      (6) The Tri-synaptic pathway results are fascinating, a beautiful visualization of these small connections using tractography, and likely the first time I've seen this in a convincing manner using diffusion MRI. I'm unsure if the novelty of these findings is fully conveyed - adding a "virtual dissection" aspect to the "virtual histology".

      (7) Regarding Figure 5, "Disorganized radial dendritic orientations", are these disorganized, or rather geometrically different (i.e., less orthogonal), but still coherent? I wonder if, very simply, organizational coherence could additionally be quantified. Although, again, this is more a curiosity and specificity of the word "disorganized", and I do not consider further analysis a necessity.

      (8) Is the dataset made available (I may have missed this in the text)?

    1. eLife Assessment

      This study provides fundamental 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 establishes an experimental framework and provides an invaluable resource for dissecting how regulatory variation in neuromodulatory systems contributes to species differences in social behavior. This work will be of interest to researchers studying social behavior, oxytocin, neuromodulation, and related conditions.

    2. 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 ligan 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 they 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 was incongruent.

      The manuscript then hypothesizes that Oxtr gene is positioned in different 3D chromatin strictures 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.

      Comments on revised version.

      Weaknesses have been satisfactorily addressed in the revised manuscript.

    3. 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. eLife Assessment

      By combining previously established mathematical models, this valuable study demonstrates that the opposite direction of surface contraction waves in Xenopus embryos and starfish oocytes can in principle arise from the same underlying mechanism. The modeling results, showing the effect of nuclear size and position, cell size, and nuclear Cdk1 concentration, are convincing and plausible but have not yet been experimentally verified.

    2. Reviewer #1 (Public review):

      [Editor's note: this version has been assessed by the Reviewing Editor without further input from the original reviewers.]

      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.

    3. 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.

      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.

    4. 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.

    5. 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. eLife Assessment

      This set of studies provides important knowledge for the role of zona incerta neurons in motivation and food-seeking in mice. The evidence supporting the findings is convincing, with the use of multiple approaches and nice behavioral procedures to provide converging lines of evidence. This work will be of interest to those interested in motivation and its brain substrates.

    2. Reviewer #1 (Public review):

      [Editor's note: This version has been assessed by the Reviewing Editor without further input from the original reviewers. The authors have addressed the comments raised in the previous round of 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 footshock) 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.

    3. 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.

    4. 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.

    5. 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. eLife Assessment

      This valuable study provides new insights into how the Par polarity complex regulates changes in stem cell state and tissue organization during early development. The evidence is solid for the role of Par in the naïve-to-primed transition and associated morphological changes, supported by genetic and cellular analyses across several experimental models. However, the proposed detailed signaling mechanism has only partial experimental support, and its physiological relevance during embryogenesis remains to be established.

    2. Joint Public Review:

      The study by He and colleagues investigates how cell polarity regulates the transition from naïve to primed pluripotent stem cells and subsequent differentiation. By comparing knockout cells lacking the Par, Crumbs or Scrib polarity complexes, the authors identify a specific role for Par in morphological remodelling and epithelial organization. The conditioned-medium rescue experiments and the identification of high-molecular-weight secreted factors are particularly interesting and informative.

      The revised manuscript has addressed most of the concerns raised during the initial review. Additional data and discussion have improved the characterization of the Par knockout phenotype, particularly its effects on pluripotent stem cell maintenance and differentiation. The authors have also placed their findings in a clearer developmental context, connecting the observed phenotypes to rosette formation, apical domain specification, epithelialization and lumen formation during early embryonic development.

      Some limitations remain. In particular, direct experiments in embryos would have strengthened the study by establishing whether the proposed mechanism operates during normal embryogenesis. In addition, although the inhibitor and rescue experiments suggest a relationship between Par, AKT/FAK signaling and secreted factors, the proposed signaling cascade is not yet fully established.

      Nevertheless, the revised study provides valuable observations and a clearer understanding of the role of the Par polarity complex in pluripotent-state transitions and morphogenesis.

    3. 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. eLife Assessment

      This study presents important findings suggesting that the late maturation of prefrontal cortex-based control processes enhances conceptual learning by allowing a period of less-constrained knowledge acquisition. The authors provide compelling computational evidence that delayed semantic control promotes learning without compromising representation integrity, with the strongest benefits emerging when control connections target intermediate layers of the model. The meta-analysis supports the developmental trajectory, but does not directly test the model's specific predictions regarding task outcomes or error patterns.

    2. 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 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 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.

      Weaknesses:

      Computational models of cognition inherently require simplification in order to focus on the mechanisms under investigation. However, the authors are explicit about the logic of the simplifications and how sacrificing ecological validity allows for better understanding of the computational mechanisms.

      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. Simulation 2 specifically demonstrates that the control locus should be at intermediate or spoke layers, *not* at the hub layer, and the authors review neuroanatomical connectivity data consistent with this finding. The meta-analysis compares taxonomic vs thematic relations, both of which are multimodal. The authors correctly note that "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", but in the context of their model, this requires that there are distinct sets of taxonomic versus thematic features (in the same way that colour, function, etc. are distinct sets of features).

      More problematic is the inference that "taxonomic and thematic relationships ...[are]... both being encoded within the same system of representation". This statement is trivially true in the sense that both are encoded in the human brain, but presumably the authors mean something more specific. What they *can't* mean is that both are encoded in the ATL hub because their simulations specifically argued that control does not operate on the hub layer (and that PFC is not connected to the ATL). If the taxonomic-thematic distinction happens in somewhere outside the ATL hub - if there are some distinct sets of taxonomic and thematic feature spokes - then this is precisely the argument that Mirman, Schwartz and others have made and the present results are fully consistent with their view (and conflict with the view that both are represented within the ATL hub).

    3. 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.

      Comments on revised version.

      The authors reply to all my comments and acknowledge the limitations of the paper.

    4. 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. eLife Assessment

      This study provides valuable findings on profiles of site-specific DNA demethylation during mouse spermatogenesis. The correlation between site-specific DNA demethylation in meiotic spermatocytes and sites of nucleosome retention in sperm is compelling. Overall the conclusions are well justified by solid data. This work will be of interest to readers in the fields of reproduction and epigenetics.

    2. Reviewer #1 (Public review):

      Summary:

      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.

      The revised manuscript addresses all reviewer concerns.

    3. 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 indicate 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 in meiotic cells precedes histone modification and histone retention in sperm is interesting.

      Weaknesses:

      All previous weaknesses have been addressed in the revision.

    4. 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. 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. The evidence is solid for the stated claims, but reviewers continue to note the limitations due to lack of analytical results, consideration of multiple subclasses of inhibitory neurons, and comparison between theory and experiment that are from different stimuli and modalities.

    2. 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 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 participation ratio and decoding accuracy increase as E/I ratio decreases. This suggests higher computational complexity.

      This is the start to 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. The paper would be stronger if this was attempted.

      Right now, the research contribution is rather thin: a grid search on parameter values, plus a thorough discussion of what is observed, plus a lot of comments on experimental findings which are suggestive (e.g. "distinct integrative role in L2/3") but don't directly connect to the study at hand. I also have concerns about the experimental comparison which I will detail below.

      Strengths:

      Some issues I appreciated are:

      (1) The use of a publicly available simulator (Brian), which helps reproducibility.

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

      (3) A good motivation of 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

      (2) The analysis of experimental data uses sub-sampling as a way to get a desired EI ratio. However, the authors' central claim is that the EI ratio intrinsically changes the underlying dynamics. Sub-sampling has no influence on the dynamics.

      To elaborate on these points:

      (1) If your networks are in the "classical asynchronous" regime as described by Otojic et al. (2014), you could implement the fixed-point calculation for your specific networks. This would be equations (1), (7)-(16), (maybe also (5-6)). As you change the EI ratio, you modify f (relative numbers of E and I cells), J_{ei}, and modifying theta_{inh} will change the set point of the firing rate function.

      Why do this? Although you would not observe a state change, the difference in the stability matrix might lead to interesting hypotheses. For example: as you raise the EI ratio while adjusting J_{ei} and/or theta_inh to keep firing rate constant, does the stability matrix get closer to instability? If so, could this be an explanation for change in D_{PR}?

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

      Earlier, I had asked the authors to comment on this finding: "in Dahmen et al. 2020 (https://doi.org/10.1101/2020.11.02.365072), the opposite was found (see Fig. 2d of Dahmen et al.): layer 2 had a lower PR than layer 4. Can you explain how that difference might arise?"

      I did not find the explanation of subsampling, as an explanation, persuasive:<br /> "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. "<br /> If I understand correctly the authors mean that they preferentially sampled either E neurons or I neurons from that data set, before performing their analysis. Although it is possible this could bias D_{PR} it is not clear why the observed difference should be in one direction or another. In addition, what the authors are trying to show (overall) is that a changed E/I balance does *something* nontrivial to the dynamics of the network to change dimensionality, and presumably this difference would still be visible even if you subsampled differently (i.e. subsampling has no impact on the network dynamics, it just changes which units you are allowed to see). If subsampling DID change D_{PR} significantly, this would suggest that excitatory and inhibitory cells contribute differently to network dimensionality, in a way that merits more exploration.

      (I find it a more persuasive explanation that Dahmen et al. and the authors measured D_{PR} in different recordings; spontaneous activity (mean gray stimulus) vs. natural stimuli. A priori, there is no reason to think statistical features of the activity should remain the same, under different stimuli. In short: the analyses were not comparable)

      But that also motivates the question: what happens to D_{PR} in the authors' networks, in the spontaneous state? The authors should show this as well. This would be the more meaningful comparison with the figure from Dahmen, AND would address the question: is network activity already high-dimensional, before a stimulus is presented; is the network "primed" to create high-dimensional responses?

      As I think about this more, I question the probative value of analyzing the visual recordings in this way, because sub-sampling the population seems to undercut the authors' central claim, which is it is the E/I ratio *of the interacting network* that is responsible for the dynamics.

      For example: if you simply used the whole population, or subsampled according to whatever the actual EI ratio is (in the V1 data), would you get substantially similar results? It seems that if you found higher D_{PR} in the layer with a lower EI ratio, whichever that would be, you would be making the point you want to make. TL;DR: I recommend re-doing the analyses without biased sub-sampling (i.e. don't try to get a certain EI ratio).

    3. 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. The modeling relies on anatomical data from the barrel cortex, but the decoding comparison is based on V1 data.

    4. 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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      (2) Dahmen D, Recanatesi S, Jia X, et al. Strong and localized recurrence controls dimensionality of neural activity across brain areas. 2023; 2020.11.02.365072.

      (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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      (5) Li H, Crair MC. How do barrels form in somatosensory cortex? Ann N Y Acad Sci 2011; 1225: 119–129.

      (6) Argunşah AÖ, Stachniak TJ, Yang J-W, et al. Local Inhibitory Dynamics Underpin Temporal Integration and Functional Segregation between Barrels and Septa in the Mouse Barrel Cortex. 2025; 2024.01.23.576792.

      (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.

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      (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.

      (15) Rosenbaum R, Doiron B. Balanced Networks of Spiking Neurons with Spatially Dependent Recurrent Connections. Phys Rev X 2014; 4: 021039.

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      (17) Volo M di, Destexhe A. Optimal responsiveness and collective oscillations emerging from the heterogeneity of inhibitory neurons. Sci Rep ; 11. Epub ahead of print 2 September 2021. DOI: 10.1038/s41598-021-96745-2.

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      (19) Schlegel P, Yin Y, Bates AS, et al. Whole-brain annotation and multi-connectome cell typing quantifies circuit stereotypy in Drosophila. BioRxiv Prepr Serv Biol 2023; 2023.06.27.546055.

      (20) Vereczki VK, Müller K, Krizsán É, et al. Total Number and Ratio of GABAergic Neuron Types in the Mouse Lateral and Basal Amygdala. J Neurosci Off J Soc Neurosci 2021; 41: 4575–4595.

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    1. eLife Assessment

      This important study presents a comprehensive comparison of human and macaque monkey behavior across a range of visual perceptual phenomena using a unified oddball visual search paradigm, which enables direct cross-species comparison while minimizing task-related confounds. It provides convincing evidence that visual perception is largely similar between these two species, but 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.

    2. Reviewer #1 (Public review):

      [Editor's Note: this version has been assessed by the Reviewing Editor without further input from the original reviewers. The original reviews for this study were unanimously positive. Reviewers requested more extensive discussion of the study's limitations (including potential cross-species differences in familiarity with the object stimuli used), and clarification of the training procedure and some design choices (such as the choice of tasks). The revised manuscript comprehensively addresses these comments. Since reviewers did not question the accuracy or validity of the study's conclusions and mentioned that the paper can serve as an impactful example of cross-species comparisons in other fields (R2), the eLife assessment was adapted to state that this is an important study providing convincing results.]

      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.

      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.

      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.

    3. 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.

      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.

    4. 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.

      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.

    5. 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. 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.

      Comments on revised version:

      The authors have addressed all my comments, including correcting the cobalamin riboswitch description and adding the recommended literature.

    2. 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

    3. 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.

      Comments on revised version:

      The authors have satisfactorily addressed my (minor) criticisms.

    4. 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.

    1. Reviewer #3 (Public review):

      This manuscript by Widuch, Seipka, and Carthew examines an unexpected relationship between insulin signaling, the heat stress response, and aging. Previous studies have demonstrated that the heat stress response declines with age, which correlates with an age-related decline in the expression of heat-shock proteins. Similarly, insulin signaling is strongly associated with aging, as decreased insulin signaling correlates with increased longevity and healthspan. Here, the authors extend upon these earlier observations with a simple yet elegant series of transcriptomic experiments that examine how the transcriptional response to heat stress changes in both control animals as well as those where the insulin-producing cells have been ablated. The resulting data are striking - In control animals, the transcriptional response to heat stress was largely independent of age. In contrast, animals lacking IPCs displayed a coupling of the transcriptional responses to aging and heat stress, such that the response to heat became strongly age-dependent. Based on these findings, the authors propose that insulin signaling functions as a "topological switch" that determines whether aging and heat stress regulate the transcriptome independently or through an integrated transcriptional response.

      Overall, I find the study fascinating, and I'm still not quite sure how to think about it ... in fact, I've spent more time thinking about this manuscript than any other paper that I've reviewed in the last few years. On the surface, this is a simple study that seems to be examining phenomena that are well documented in the aging and physiology communities. But the manner by which insulin appears to uncouple aging from the heat stress response appears to be a unique and fundamentally important observation.

      In the end, I have few criticisms. IPC ablation slows development, produces smaller adults, extends lifespan, and presumably alters the rate of biological aging. Thus, although the animals are matched for chronological age, the RNA-seq experiments may not compare equivalent physiological states. This caveat complicates the interpretation of the results but does not diminish the striking observation that insulin signaling alters the relationship between age-dependent and heat-stress-induced gene expression. I believe this finding points to a deeper biological principle that warrants further consideration.

    2. Reviewer #2 (Public review):

      Summary:

      This is an interesting study that addresses an important question: how does the response to heat stress degrade in older individuals? The authors assess this in young (4d old) and aged (30d old) Drosophila adult females, assessing global changes in gene expression in animals subjected to and recovering from a 2-hour heat stress. They find that global responses to heat stress are indistinguishable in young and old adult flies, suggesting that aging and response to heat are independent inputs with regard to global gene expression. Loss of insulin-producing cells from early larval stages altered the ways in which stress and aging regulate gene expression, with sets of genes responding to heat stress in an age-dependent manner.

      The findings are intriguing, but the role of insulin signaling in switching genome-wide responses to stress and aging is challenging to interpret due to the timing of insulin-producing cell ablation. Consequently, alterations in developmental processes that are dependent on insulin-producing cell function may contribute to the gene expression programs observed here.

      (1) Expression of the UAS-reaper transgene under control of Dilp2-GAL4 likely leads to elimination of insulin-producing cells (IPCs) from at least the first larval instar, if not earlier. Consequently, a large number of processes ranging from animal growth and fertility (as the authors note) to brain development will be affected by this manipulation. This is important because the authors interpret their findings as demonstrating "a state of active repression maintained by high IIS activity", but it is not clear that these changes are due to active insulin signaling rather than changes that occurred during development.

      (2) Does reduced fertility itself, without altering insulin signaling, lead to the global changes in gene regulation that the authors observed in old vs young and IPC-intact vs IPC-ablated animals? Addressing this would shore up the idea raised in the discussion about reallocation of resources from stress to reproduction.

      (3) All measures of gene expression were made using RNA-sequencing of whole-fly transcriptomes, which limits finer-grained assessment of organs that contribute most strongly to the gene expression patterns observed here.

      (4) The authors compare gene expression in young and old adult flies (subjected to heat stress or not and with IPCs or not). Broadly speaking, they do not directly compare gene expression between IPC-intact and IPC-ablated animals, except for data shown in Figure 7. Additional comparisons of this nature would be helpful in showing the trends in the data.

      (5) The sample size for the RNA-Seq experiments is not included.

    3. Reviewer #1 (Public review):

      Summary:

      The goal of this study was to understand how thermal stress and aging are intertwined, but their transcriptional responses are distinct. The experimental premise is that insulin signaling influences the distinct transcriptomic responses, given the role of insulin in aging and stress responses, across several studies. The authors examined gene expression in whole female Drosophila that have neuronal insulin-producing cells ablated (dIlp2-gal4>reaper), to controls with only the dIlp2-Gal4. In control flies, the genomic response to heat stress and aging are independent, but in experimental flies they argue that the heat-stress response is "age-aware". This is based on a PCA analysis and the patterns of changes observed across several time points after a heat stress in young and old flies.

      Strengths:

      The authors present an interesting interpretation of the carefully collected gene expression data. The hypothesis is interesting and sheds light on how insulin signaling may influence aging and stress responses. The presentation was clear overall, though it is a complicated set of interpretations. There were several places where the authors note weaknesses in their study, including potential issues with using a subset of genes for their work, which they address. They also address the issue of selecting flies that can perform in the geotaxis assay, as they may be only examining the hardiest of flies, by additionally performing gene expression on the set that were not able to climb. They also indicate that dIlp2-gal4>reaper flies show very slow development, and that the ablation happens pre-adult stages, which are clear limitations.

      Weaknesses:

      (1) It is my understanding that sPCA analyses are meant to be more exploratory, and a stronger analysis would include multivariate statistical analysis that would indicate if an interaction is significant. Also, could the authors be missing genes that have a statistical interaction across the conditions, but would not be in the top three PC?

      (2) In addition, the authors make strong statements such as suggesting that there are "rewiring" and "topological switch" changes that are not supported by additional experimentation. While these are exciting hypotheses, the language should be more consistent with what is in the paper. No topological analysis is performed, and that word is in the title.

      (3) It is not clear that the authors controlled for strain background. Was the UAS-reaper line introgressed into the same genetic background as was used in the control cross?

      (4) The authors should be careful about over-interpreting a large fold change, and show the starting baseline and induced amounts, in addition to the fold change.

    4. eLife Assessment

      The authors compare gene expression in female Drosophila in which the neuronal insulin-producing cells (IPCs) are ablated and compare them to controls that retain these IPCs. The methods broadly support the claims that when IPCs are ablated, gene expression patterns in response to heat stress are age-dependent. This contrasts to what is observed in controls where heat responses are not age-dependent. The findings are valuable and the evidence is considered solid.

    1. eLife Assessment

      This study presents a well-executed and valuable proof of concept relating to the targeting of TGFBR2 in human disease. The evidence supporting the claims of the authors is largely solid, although it falls considerably short of a conclusive pre-clinical package of data, and as such the claims relating to clinical impact need to be downplayed. Additionally, flow cytometry data quantification should be included to allow numerical contrast between receptor abundance and functional potency. The work will be of interest to biologists and translational scientists working on cancer or lung disease.

    2. Reviewer #1 (Public review):

      Summary:

      This manuscript addresses a genuinely important and long-standing problem in the field: how to exploit the therapeutic potential of TGFβ pathway blockade while avoiding the systemic toxicity that has repeatedly derailed clinical candidates. The biologic rationale is sound, the stepwise molecular design is elegant, and the central finding - a ~300-fold potency enhancement in PDGFRA-expressing human fibroblasts with no enhancement in PDGFRA-negative HEK293 cells - is striking and clearly presented. As a proof-of-concept study, the work is significant. However, the evidence base is entirely in vitro, rests primarily on a single immortalized human fibroblast line, and leaves the mechanism of the potency enhancement incompletely resolved. The study should be viewed as a well-executed first step, not as validation of a therapeutic strategy, and the findings' generalizability and mechanistic claims require further substantiation before the conclusions drawn can be fully accepted.

      Strengths:

      The paper is well-motivated. The failure of broad TGFβ pathway inhibitors in the clinic, including the recent halt of the BEACON-IPF bexotegrast trial (NCT06097260), lends urgency to the idea of cell type-targeted antagonism, and the authors situate their work clearly in that context. The incremental design logic is a particular strength: they first characterize the natural bispecific TGM6, use it to establish mechanistic principles (LYTAC-like receptor degradation, tolerance for lower-affinity TGFBR2 binders), then systematically replace the immunogenic worm domains with antibody fragments, culminating in a fully human-sequence bispecific. This stepwise approach makes the reasoning transparent and persuasive. The choice of PDGFRA as a fibroblast targeting handle is well-justified by recent literature (Tsukui et al., 2024), and the use of multiple orthogonal readouts - luciferase SBE reporter, flow cytometry for surface TGFBR2, RT-qPCR for fibrosis-relevant genes, and western blotting for pSMAD2/3 is commendable. The ~300-fold potency shift in fibroblasts, absent in HEK293 cells, is the paper's headline result and is reproduced across independent readouts in a compelling manner.

      Weaknesses:

      Mechanistic interpretation of LYTAC (Lysosomal Targeting Chimera) like activity. The authors propose that TGM6 and the bispecific act by co-engaging a co-receptor that drives lysosomal degradation of TGFBR2. The flow cytometry data showing rapid, near-complete surface TGFBR2 depletion is visually striking. However, the inhibitor experiments (Figures 1I, 1J) are imperfect support for this conclusion. Dynasore (a dynamin inhibitor) only partially restores surface TGFBR2, consistent with but not proof of endocytosis-mediated depletion. More problematically, the proteasome inhibitor MG132 is used to support lysosomal involvement, but proteasome inhibition does not directly block lysosomal degradation of transmembrane receptors. A lysosomal inhibitor (e.g., bafilomycin A1 or chloroquine) would be the appropriate reagent; its absence leaves the mechanistic claim inadequately tested. The paper also does not directly demonstrate co-internalization of TGFBR2 with either PDGFRA or LRP1 (the latter identified as the D4D5 receptor in van Dinther et al., 2026, cited by the authors).

      The potency enhancement mechanism for the PDGFRA bispecific is insufficiently dissected. The authors attribute the 300-fold potency enhancement to cell-targeting and a LYTAC-like mechanism, and flow cytometry (Figure 3D) does show greater TGFBR2 depletion with the targeted molecule. However, simple bivalent avidity effects from simultaneously engaging two receptors on the same cell surface are not formally excluded. A monovalent anti-PDGFRA control (e.g., anti-PDGFRA Fab alone, or a bispecific with a non-TGFBR2-binding VH) would help partition the targeting and degradation contributions. Similarly, no ternary complex (simultaneous binding to PDGFRA and TGFBR2) is demonstrated biochemically.

      Limited cell model diversity. The human fibroblast data all derive from a single commercially available immortalized fetal lung fibroblast line (MRC5). Whether the results generalize to primary adult human pulmonary fibroblasts, fibroblast subtypes from IPF patients, or fibroblasts from other tissues is entirely unknown. This substantially limits the translational claims in the Discussion.

      Selectivity concerns PDGFRA as the target receptor. PDGFRA is expressed not only on pulmonary fibroblasts but also on pericytes, stellate cells, some hematopoietic progenitors, and certain tumor cell types. The paper tests selectivity only against HEK293 cells, which lack many fibroblast-relevant properties beyond PDGFRA expression. Whether the bispecific engages and functionally modulates TGFβ signaling in other PDGFRA-expressing cell types is not addressed.

      The VH271-12-TGM6-D4D5 data in human cells (Figure 2F) are only duplicates. This is explicitly acknowledged, but it means the most mechanistically informative intermediate construct is under-replicated. The authors should provide p-values.

      Functional readout limitations. The RT-qPCR panel covers only two ECM genes (COL1A1 and ELN), and there is notable variability in the data (Figure 3E). The western blot for ACTA2 (Figure 3F) also shows wide individual-experiment scatter. These data are directionally consistent with the reporter assay but are not themselves quantitatively convincing.

      Conclusion:

      The core in vitro proof-of-concept claim that a PDGFRA-targeted TGFBR2 bispecific can achieve cell-selective, potency-enhanced TGFβ pathway antagonism in human fibroblasts is supported by the data as presented. However, the mechanistic framing (LYTAC-like degradation) is incompletely evidenced, the generalizability beyond MRC5 cells is untested, and there are no in vivo data of any kind. The Discussion's forward-looking statements about therapeutic application to IPF and cancer should be substantially tempered.

    3. Reviewer #2 (Public review):

      Summary:

      In this study, the authors aim to provide proof-of-concept evidence to support the development of a targeted anti-TGF beta therapy for the treatment of solid tumours and fibrotic diseases. By mimicking a natural strategy employed by a murine parasite, they aim to provide a foundational design for a precision, cell-targeted therapeutic to circumvent the prohibitive toxicity associated with systemic TGF-beta inhibition.

      Strengths:

      (1) The authors demonstrate the design of a molecule that can achieve an in vitro selectivity of around 300-fold and show a functional effect of inhibition on fibrotic signalling and myofibroblast phenotype. A 300-fold cellular potency window would be expected to be of clinical and therapeutic relevance if it could be replicated across tissues.

      (2) The mechanistic investigations around receptor internalisation and degradation are solid and are supported by a paper that has been published since this manuscript was submitted (van Dinther et al. 2026).

      (3) The paper gives some insights into factors that may further influence selectivity. The authors note that whilst the non-target HEK293 cells are 100-fold less sensitive than the MCF5 lung fibroblasts to TGF-beta inhibition with the targeted molecule, the HEK293 are more sensitive to the untargeted ligand. This raises the likelihood that expression levels of the therapeutic target may play into the selectivity of the molecule as well as the expression distribution of the targeting protein.

      Weaknesses:

      (1) The cell line chosen to demonstrate selectivity is an embryonic line with characteristics of neural progenitor cells and, as such, not relevant to the intended patient populations for TGF-beta inhibitors. This study could have had more impact if it had investigated selectivity against the cell types relevant to the known cardiovascular side effects associated with TGF-beta inhibitors.

      (2) The authors mention that selectivity may be influenced by expression levels of the target proteins but do not compare expression levels of TGFBR2 and PDGFRA in HEK293 and MCF5 lung fibroblasts directly. Furthermore, there is little investigation into the relative impact of different binding affinities against both TGFBR2 and PDGFRA; the paper could have been more compelling if this concept had been expanded on. A deep understanding of relative binding kinetics and target protein expression levels will be critical to the successful development of a cell-targeted TGF-beta inhibitor.

      (3) The molecule developed is aimed exclusively at targeting pathogenic fibroblasts, but pulmonary fibrosis is a complex disease involving multiple cell types that respond to TGF-beta. This includes the epithelial alveolar type II cell, which is known to be a driver of disease. A truly disease-modifying therapeutic will need to tackle multiple cell types in IPF whilst minimising the impact on protective TGF-beta functions.

      Impact:

      A targeted TGF-beta therapeutic that enables selective inhibition of the pathological functions of TGF-beta whilst maintaining normal homeostatic signalling would have far-reaching benefits for patients. This study demonstrates for the first time that a naturally occurring helminth strategy for TGF-beta modulation can be adapted for human tissue targeting in vitro. It raises interesting potential as a therapeutic strategy, though the data as presented currently is far from that required for a convincing preclinical data package. The pharmacology will be complex, and it is of note that the helminth strategy to modulate the pathway local to the site of infection utilises multiple proteins and multiple targeting domains. Systemic modulation is an even higher bar, requiring detailed knowledge of the system kinetics and extensive in vitro profiling of normal and disease tissue responses. The next steps would also include an understanding of the therapeutic window required in vivo.

    4. Reviewer #3 (Public review):

      Summary:

      The authors aim to develop a cell-targeted approach to inhibiting transforming growth factor beta signalling, motivated by the potential toxicity associated with systemic inhibition of this pathway. They first investigate the naturally occurring helminth protein TGM6, which inhibits signalling in mouse fibroblasts and causes rapid loss of its receptor from the cell surface. They then use this biological principle to engineer an antibody-based bispecific antagonist that simultaneously binds TGFBR2 and PDGFRA, the latter being expressed by pulmonary fibroblasts relevant to fibrosis.

      The principal finding is that targeting the antagonist to PDGFRA substantially increases its activity in human MRC5 pulmonary fibroblasts. The targeted molecule inhibits TGF-beta-induced signalling with an IC50 of approximately 120 pM compared with approximately 35 nM for the untargeted molecule, corresponding to an almost 300 fold difference in potency. This enhancement is not observed in PDGFRA-negative HEK293 cells. The targeted molecule is also associated with reduced surface TGFBR2 and decreases downstream transcriptional and protein responses to TGF beta.

      The study provides a valuable proof of principle that engagement of a second cell surface receptor can markedly enhance the activity and potentially the cellular selectivity of a TGFBR2 antagonist. This could provide a useful general strategy for developing inhibitors of signalling pathways for which systemic inhibition is limited by toxicity. The evidence for the central phenomenon is solid, although the mechanism responsible for the striking increase in potency and the extent to which this can be attributed specifically to PDGFRA engagement and receptor depletion remain incompletely established.

      Strengths:

      The major strength of the study is the magnitude and apparent cellular specificity of the enhancement in antagonist activity. In MRC5 fibroblasts, the PDGFRA-targeted antagonist is almost 300-fold more potent than the corresponding untargeted molecule, whereas targeting provides no apparent advantage in PDGFRA-negative HEK293 cells. This provides persuasive evidence for the underlying concept that engagement of an additional cell surface receptor can markedly enhance TGFBR2 antagonism.

      The experimental progression is also a strength. The authors move logically from characterisation of the naturally occurring TGM6 protein, through replacement of its TGFBR2 binding component with an antibody-derived binder, to replacement of the helminth targeting domains with an antibody against PDGFRA. The intermediate construct retains activity in mouse fibroblasts and, importantly, also inhibits TGF-beta-induced signalling in human MRC5 fibroblasts. This provides a coherent link between the biological observations concerning TGM6 and the final fully antibody-based molecule.

      The use of several complementary readouts also strengthens the conclusions. In addition to a signalling reporter assay, the authors examine receptor abundance at the cell surface and downstream effects on extracellular matrix-associated gene expression and ACTA2 protein. The revised manuscript has further strengthened these aspects by improving quantification and reporting of biological replication and by adding the protein-level downstream readout.

      Finally, the authors appropriately identify an important potential limitation of ligand competitive TGFBR2 antagonism. HEK293 cells are more sensitive than the intended fibroblast population to the untargeted antagonist, despite lacking the targeting receptor. This observation is important because it indicates that cellular context can substantially influence sensitivity independently of the targeting strategy and highlights an issue that will need consideration in further development of this approach.

      Weaknesses:

      The principal weakness is that the causal contribution of PDGFRA engagement to the increased potency has not been directly demonstrated. The central evidence comes from comparison of MRC5 fibroblasts with PDGFRA-negative HEK293 cells. These are biologically distinct cell types and, importantly, differ in their sensitivity to the untargeted TGFBR2 antagonist. An isogenic system would provide a more rigorous test of the proposed mechanism. For example, deletion of PDGFRA in MRC5 cells, ideally followed by restoration of its expression, could establish whether the marked potency advantage of the targeted molecule is specifically dependent on PDGFRA engagement.

      There is also an important apparent disparity between the magnitude of the functional effect and the changes in surface TGFBR2. The approximately 300-fold difference in functional potency is striking, whereas the differences in the flow cytometry distributions appear considerably more modest. The flow cytometry experiments are largely presented as representative distributions rather than quantitative measurements of receptor abundance across biological replicates. Quantification of median fluorescence intensity or relative surface receptor abundance, together with appropriate analysis across replicates, would allow the magnitude and reproducibility of receptor depletion to be assessed more clearly. It would also help determine whether receptor removal is sufficient to explain the very large functional effect.

      Related to this, the precise mechanism underlying the enhanced potency remains uncertain. TGM6 causes rapid loss of TGFBR2 from the cell surface, and inhibitors of internalisation and protein degradation partially reduce this effect. These findings are consistent with altered receptor trafficking and degradation but do not directly establish lysosomal degradation. Moreover, the disparity between the modest apparent changes in surface receptor abundance and the large change in functional potency raises the possibility that increased local concentration, avidity, or other consequences of PDGFRA engagement contribute substantially to the enhanced activity. The description of the mechanism as "LYTAC like" should therefore remain appropriately qualified.

      The biological validation of the final construct is relatively limited. The human experiments use MRC5 cells, an established foetal lung fibroblast line, and downstream effects are assessed principally through a signalling reporter, two extracellular matrix-associated transcripts and ACTA2 protein. These experiments establish inhibition of TGF beta signalling but do not demonstrate a broader change in fibroblast phenotype or an antifibrotic effect. Confirmation in primary adult pulmonary fibroblasts, particularly cells derived from fibrotic lungs, would increase the biological relevance of the findings.

    5. 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. eLife Assessment

      This important work outlines why commonly applied performance metrics in predictive modelling do not accurately reflect translational potential, using the example of psychiatric care; it provides a web-based tool to contextualize effect sizes in psychiatry with respect to reliability and base rates, and to calculate the real-world utility of prediction models under different scenarios. The evidence supporting the conclusions is convincing, incorporating established psychometric principles that will be of use for multiple fields, along with transparent quantitative logic and example applications. The work will be of broad interest to both clinical experts and scientists in biomedicine and the life sciences.

    2. 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 adjusted performance metrics and additional predictive‑value and decision‑analytic measures.

      Strengths:

      The manuscript speaks convincingly about the risk of face validity and 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 adoption of the proposed framework beyond quantitative methodologists.

      Impact on the field:

      I think the tool can serve as a valuable approach to estimate a first approximation of clinical relevance for a given linear predictor model and provides researchers with a structured outline to assess their own findings in the light of translational value.

    3. 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 how-to. The method itself is not new, but I think the tool will be valuable for researchers from different fields. There are already tools for the conversion of effect sizes (my current favourite 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 well-written.

      Weaknesses:

      While comprehensive explanation and examples are important for correct use of the tool, I don't really see the added value of a peer reviewed publication over and above the authors' online how-to, as the software 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)

      Comments on revised version.

      The authors have adequately addressed my previous comments.

    4. 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 has been strengthened through revision by increased clarity on the formulation of the paper and stated goals of the examples used. The use of this tool will likely bring forth additional thoughts, but I commend the authors on their work and helping to better disseminate these ideas, while also acknowledging some of the remaining areas for further development.

      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 wide-spread analytic power analysis tools in study planning. The paper also well contextualizes 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:

      The authors have well-addressed the majority of my previous comments in this important work that can support multiple subfields. Remaining weakness reflects the complexity and breadth of the intended use cases and balancing clarity of explanation for the E2P tool and broader psychometric issues in applied fields. Likewise, users of E2P should remain vigilant to distinctions between predictive utility and validity. As current construed, however, these minor weaknesses do not substantively undermine my enthusiasm or estimate of the impact of this work.

    5. 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. eLife Assessment

      This article by Lästad and colleagues proposes to reconsider some important aspects of single-cell volume and dry mass homeostasis in a model system of epithelial monolayer, based on a novel method relying on quantitative phase imaging to measure these parameters. The article proposes a solid in-depth analysis of a large dataset uniquely based on this method. This is the main current weakness of the manuscript, since the claims that differ from previous findings are not tested using other methods to exclude potential artifacts.

    2. Reviewer #1 (Public review):

      Summary:

      The study uses Quantitative Phase Imaging to measure and infer cell shapes, areas, volumes, and masses during the evolution of a confluent epithelium. These are important physical parameters of a monolayer and help to better understand the dynamical evolution of an epithelium and collective cell behaviors.

      Strengths:

      Quantitative Phase Imaging allows simultaneous, live-cell measurements of mass density and height that are not easily achievable by other means.

      Weaknesses:

      The biological or biophysical conclusions drawn are not fully substantiated, as QPI is the sole experimental technique used, and the analysis relies heavily on indirect 2.5D assumptions that the authors themselves question. This makes the novelty questionable, especially since a technical paper establishing this QPI pipeline for epithelia has been published elsewhere by the same authors.

      To study the dynamics of confluent epithelium, the authors applied 2D and 3D quantitative phase imaging (QPI) to measure local dry mass densities and heights of MDCK monolayers. These techniques allow simultaneous, live-cell measurements of mass density and height that are not easily achievable by other means, enabling a direct test of dry mass conservation that enriches the coarse-grained description of epithelial tissues. The authors also use the mass/height information and apical segmentation to estimate cell areas, volumes, and dry masses, leading to deductions about non-prismatic cell shapes, mass shedding, and volume reduction.

      Overall, the study demonstrates an interesting technical application of QPI. However, while I find the methodology promising, I am not fully convinced by the biological or biophysical conclusions drawn, as QPI is the sole experimental technique used, and the analysis relies heavily on indirect 2.5D assumptions that the authors themselves question. Furthermore, given that the authors have already published a technical paper establishing this QPI pipeline for epithelia (Reference 22), the present manuscript cannot claim novelty on methodological grounds alone. Its contribution therefore hinges almost entirely on the biological insights it provides. However, as I outline below, those biological insights are either expected from previous literature (non-prismatic shapes in low-density MDCK), inferred indirectly from 2.5D projections (frustum shapes), or remain at best correlative without experimental validation (mass shedding). Thus, in its current form, I struggle to identify a clear advance. Below, I outline specific technical concerns and suggest ways to strengthen the study.

      (1) Indirect inference of non-prismatic cell shapes from 2.5D projections.

      The authors segment the projected (apical) area of the cells and assume prismatic, vertical-sided geometries to calculate cell volumes, and compare them to frustum-based cell models. They conclude that cells are non-prismatic if volumes are constant. While I appreciate the modeling effort, the evidence for non-prismatic shapes remains indirect, as it relies on comparing 2.5D projected correlations rather than a direct measurement of the 3D geometry. Since the authors already have full 3D refractive index tomograms (as shown in Figure 1A), a much more direct and definitive approach would be to perform true 3D volumetric segmentation along the z-axis to directly reconstruct actual cell shapes. Additionally, structures that lead to non-prismatic shapes (e.g., cryptic lamellipodia) are well-documented for low-density MDCK cells, so I do not find this conclusion particularly illuminating for epithelium biology. To improve on this analysis, tracking the evolution of directly segmented 3D shapes as density increases beyond the range they presented would be highly instructive, as one would expect the lateral sides to become progressively more vertical under compaction.

      (2) Apparent conflict between ensemble and single-cell dry mass concentration trends.

      The ensemble-averaged dry mass concentration is shown to increase with cell density (Figure 1D). However, the single-cell tracks in Figure 3B (which span approximately 10 hours of evolution) show dry mass density to be roughly constant. Given that the monolayer density is likely changing over these 10 hours, this seems like a conflict between ensemble and single-cell data. Can the authors clarify?

      (3) Breakdown of continuum mass conservation at the cellular scale.

      The authors showed a breakdown of the 2D continuity equation at cellular scales, which is not surprising. To move beyond this, I would suggest directly testing mass conservation at the cell scale by following mass evolution of each cell using integrated mass from 3D tomograms. This would provide a much stronger conclusion than the current 2D coarse-graining analysis, which is relevant for monolayer-scale, but not at the cell-scale.

      (4) The "mass shedding" hypothesis requires experimental validation.

      The claim that cells periodically shed 10-15% of their dry mass is an important biological statement, yet it remains unclear due to the 2.5D analysis and is, at best, correlative. Given that epithelial cells are known to secrete basement membrane components, this hypothesis is testable. I would suggest the authors perform appropriate pharmacological perturbations of secretion pathways, if not genetic perturbations, and repeat the inference from 3D tomograms to see if the apparent volume/mass loss is abolished.

      (5) Sensitivity of mass measurements to the specific refractive index increment.

      The conversion from refractive index contrast to dry mass concentration relies on the specific refractive index increment. While the authors use a standard average value of α ≈ 0.18−0.2mL/g, it is worth noting that this parameter varies between different biomolecular classes. The authors should discuss the potential sensitivity of their absolute mass and concentration values to compositional shifts (e.g., changes in the lipid-to-protein ratio) that might occur as cell density increases, and provide an estimate of the error bounds this could introduce into their conclusions.

    3. Reviewer #2 (Public review):

      Summary:

      In this study by Lästad et al., the dry mass and mass density of confluent MDCK epithelia are carefully measured using 2D and 3D QPI microscopy. Extensive imaging experiments were performed. The single-cell-resolved data show that the cell mass density is relatively conserved, even though there is considerable cell height and cell volume variation. There appear to be transport processes happening between neighboring cells within the epithelium.

      Strengths:

      The data appears to be high quality, with good statistics. I think the conclusions are generally interesting and sound, with some questions noted below.

      Weaknesses:

      (1) I think the weakest part might be Figure 3 concerning cell volume and area. The authors refer to their previously published paper on their segmentation and height determination methods. It appears that some of these results may depend on the parameters of the imaging method, although I am not an expert. I am wondering to what extent the data depends on these image analysis methods. For example, there are some Gaussian blur parameters used. Do these parameters significantly affect the results? I suspect not, but I would be more convinced if additional validation is shown.

      (2) Along the same vein, I couldn't find how the velocity field in Equation 8 was determined. This seems to be a critical quantity for conclusions in Figure 5.

      (3) Equation 8 assumes that mass is conserved within the epithelium. Is this really the case in the experiment? If some cells are growing, then there should be a source term in Equation 8. Could some of the mass non-conservation come from growth fluctuations?

      (4) The paper is nearly entirely physical measurements. While I am fine with this, it would be nice to perform some biological manipulation to validate the results. For instance, if there is mass transport between cells, then blocking tight junctions might stop this. Or if serum is removed, then cells would be arrested, and mass would definitely (maybe?) be conserved?

    4. Reviewer #3 (Public review):

      Summary:

      In this article, Lästad and colleagues propose a large dataset of combined 2D and 3D quantitative phase imaging (QPI), from which they extract the volume, dry mass, and height of single cells in a monolayer formed by MDCK epithelial cells at various cell densities. Some of these measures are at odds with previous reports or assumptions, mostly concerning the height of cells in the monolayer. As a consequence, the volume measures also differ, showing, like the height, larger fluctuations than expected. This raises a fundamental question, since the dry mass concentration seems to stay very homogenous in the monolayer, suggesting that dry mass of single cells also fluctuates to a rather large extent, both up and down (on top of the longer timescale growth trend). The possibility that dry mass decreases significantly over hour periods in a single cell seems novel and unexpected. The authors then propose that a large part of these apparent volume fluctuations and thus dry mass fluctuations (and loss in particular) might actually come from the wrong attribution of signal to individual single cells, in case the cell/cell interface is not as vertical as assumed in the largely 2D segmentation of the cell area. They nicely show that a large part of the volume behavior that they observe could be due to that. They do not consider other possible sources of error in the volume/height measures, but there are likely even more (see weaknesses below), so this could be the main reason for this apparent novel/unexpected result. This does not explain the strong discrepancy between their measures of cell height and other reports. This could be due either again to a segmentation error that has not been sufficiently checked, or to a different culture condition. This point is not really discussed by the authors. In conclusion, this article presents a potentially very powerful and novel approach to access single cell size and growth homeostasis in monolayers, with some surprising findings that, at least for some of them, raise a question about the validity of the approach (at least if no other method is used to correct it, as is the case here), and this is in part nicely acknowledged by the authors.

      Strengths:

      The main strength of the article is in the combination of the 2D and 3D QPI, which allows the extraction of several parameters that single measures would not allow, in addition to also providing cross-validation power for some of the measures - the authors had published some of that in a prior article, which explains well these strengths. The other interest of the article is that it questions some prior findings (or assumptions), mostly on the height of the cells in monolayers. This has always been the less quantitative aspect of studies on monolayer morphogenesis, due to the poor resolution of fluorescence microscopy in the z-axis. Finally, the authors propose a well-balanced interpretation of their data, including a clear exploration of a potential artifactual origin of the volume fluctuations they report, due to wrong assumptions on the segmentation of single cells. The article is also very well written and clear.

      Weaknesses:

      The major weakness of the article is the lack of cross-validation of the most surprising findings with other, more direct methods, which should be rather easy to perform, at least on some specific points (see below), to make sure that it is not all about artifacts of the QPI, in addition to other 3D-related limitations that the authors already explored. A potentially strong weakness is that the authors do not really propose a solution (and maybe there is no solution) to solve the issue of the complex 3D shape of single cells and the potential artifact it creates on volume measures.

      Specific weaknesses:

      (1) According to the authors, the main source of possible error in their volume measures would be caused by cell/cell junctions that would not be vertical. As the authors point out, since the cell/cell junctions in their monolayers seem rather thin in the z-axis, this might not explain all. The authors should consider other sources of error, also related to wrong segmentation, especially from the 3D QPI. This could be cell protrusions or other extensions that are not always segmented the same way from one image to another, or also issues in determining precisely the threshold for the height. To test these possible issues, it seems more appropriate to first validate the method on single isolated cells, which is not done here nor in the previous method article from the same authors. Single cells have many advantages, and it would be much easier to rule out all kinds of measurement errors related to segmentation by testing against other well-established methods. For example, the volume of cells reported by the authors seems too large compared to a number of other reports, which is typical of segmentation errors, especially in height. A way to test for that is to simply image single cells in a non-adherent state to get their diameter. This is not very precise, but it can easily rule out factors of 2 in the volume. FxM would be more precise, but might not be directly compatible with 3D QPI, so it could not be performed on the same cell, leaving some uncertainties (although at least it could be used to check the volume distribution of the MDCK cells when plated as single cells, and compare to the values obtained from 3D QPI). In general, data on single cells should be provided - the authors could perform the same set of analyses, but with much less ambiguity in their interpretation, and thus more easily identify possible sources of errors with their method.

      (2) The authors claim a very good precision on the height (5%, page 6), but this is not validated against a more direct method of imaging. It is hard to believe, as claimed on page 8, that other authors would have totally missed such a large amplitude of height fluctuations using confocal imaging - the authors report heights from 5 to 9 microns, so almost a factor of two, over a range of distances that can be easily resolved in confocal microscopy, even in the z-axis. Before making such a claim, it appears essential that the authors image their monolayers using up-to-date confocal microscopy, or even better, some microscopy with better z-axis resolution (there is a large variety of options). In case they find the same height variations (5 to 9 microns), then it is very likely that there is a difference in the cell culture conditions and that they are just not looking at the same type of monolayers as others. In case they do not see any height variation, they should strongly question their method and maybe try to find a way to address the origin of the error more directly. In case they really doubt the capacity to resolve the z-axis by confocal microscopy, they could also rather easily arrange a setup to look at their monolayer from the side (there are again a variety of options) and check the height this way.

      (3) The height profile provided in Figure 2 makes it hard to believe that this is a regular 'mature' monolayer with junctions, etc. I am not a specialist in these systems, so I might be wrong. But I would recommend that the authors check classical markers for cell/cell junctions, as others do, to at least assess whether they are dealing with the same type of monolayers that others have been investigating in the reports that the authors comment on; if it is not the case, then it might not be surprising that they find very different results.

      (4) The authors make a strong point about a very strict stable dry mass concentration, which then raises a lot of questions. They could also perform some simple tests to check if concentrations are constant in the cell. It is rather simple to mix labelled and not labelled cells to form a monolayer and use cytosolic labelling, either genetically expressed or using a dye (there are many possible ways to get molecules inside cells: membrane-permeable ones, or electropermeation, or using micro-injection). Then, using confocal microscopy, it is easy to assess the concentration while checking that the total quantity of fluorophore is constant, with widefield microscopy (or, if the labelling molecule is well characterized, like a large dextran, it can be assumed). This has been performed in numerous studies. It does not give the volume in absolute numbers, but gives the relative volume changes in time. For claims such as constant concentration but fluctuating volume, it is important to have at least one additional method to test the claim.

      (5) The hypothesis that cells shed some dry mass, discussed in many places in the article, seems contradicted by the fact that dry mass appears constant when the measure is averaged over a large enough area. It seems that the authors can discard this hypothesis fully. Instead, they might leave more open the possibility that cells exchange material, since this does not have to be only through gap junctions, but also, for example, cells uptaking fractions of neighboring cells (instead of shedding material in the extracellular medium), or exchanging material via other junctions between cells, such as membrane tubes. These have been reported in a variety of contexts, either as 'tunneling nanotubes', which have been shown to transport large cargo, or as 'unresolved cytokinetic bridges', with cells that seem to be already out of mitosis but are actually still connected by rather large tubes for hours. It is out of the scope of the article to test all these (although it can be tested rather easily with fluorescent reporters inside a subfraction of cells), but the authors could discuss these possibilities.

      (6) In their discussion p14 (point a.), the authors seem to leave aside the question of timescales. All these size changes they mention have very different timescales. To typically achieve a significant change in value (1 to 10 %), water can pass membranes in seconds, ions are rather pumped at the minute timescale, while dry mass accumulation is rather on the hour timescale. This usually also helps to tell apart the potential mechanisms involved.

      (7) The discussion, to a large extent (as well as the conclusion), is just rephrasing the results without adding much more. It is a place where the authors could propose more radical alternative interpretations of their data and explore other potential limitations of their method (see all the points above).

    5. 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. eLife Assessment

      This important study provides a comprehensive 3D kinematic analysis of coordinated beak and tongue movements during seed processing in two songbird species with contrasting bite forces, the domestic canary and the Java sparrow. The evidence is compelling: high-speed biplanar X-ray reconstruction of moving morphology (XROMM) resolves upper beak, lower beak, tongue, and seed motion in three dimensions, in vitro measurements show slower jaw muscle contraction and relaxation in the hard-biting species, and a Bayesian modeling framework combined with permutation tests for time-series correlations provides rigorous statistical support. The work will interest researchers in comparative biomechanics, motor control, and the evolution of feeding behavior.

    2. 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) are 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, and kinematic correlations within species, sets a new standard for our field. Another strength is in how the results were packaged: each subsection indicated how their objectives were addressed, and there were concluding statements trailing each subsection that helped deliver the key take-aways, and the visualizations of their statistical workflows in the appendices are game-changing.

      Comments on revised version.

      The authors have fully addressed my [relatively minor] concerns upon revision, and they, themselves, have done a sufficient job of making any limitations of their study fully transparent.

    3. 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. eLife Assessment

      This paper examines how locomotion modulates the activity of different sub-types of cortical neurons in mouse primary visual cortex. The authors convincingly demonstrate that locomotion more strongly increases responses in sensitizing than in depressing excitatory cells. Computational modeling then accounts for these data through locomotor state-dependent modulation of inhibitory synapses. The findings represent an important contribution to our understanding of how internal state and neural dynamics can interact to modulate sensory processing.

    2. Reviewer #1 (Public review):

      In this manuscript, Hinojosa and colleagues analysed the changes in V1 visual responses induced by locomotion in head-fixed mice using two-photon calcium imaging. The authors observe that locomotion strongly increases the visual responses of V1 excitatory neurons that exhibit sensitizing responses to visual stimuli. Also, there is an increased response in VIP interneurons, and to a lesser extent, PV interneurons and SST interneurons (non-significant). The authors used a model fitted with data presented in the manuscript, as well as previous knowledge on cortical connectivity among different neuron types. The model suggests that the major component of the increased responses during locomotion is an increase in excitatory drive from external inputs (feedforward, feedback and modulatory), most importantly onto VIP interneurons and excitatory neurons. However, the excitatory drive of local excitatory neurons onto other surrounding excitatory and inhibitory cells is reduced.

      The manuscript is well presented and represents a valuable analysis of how locomotion modulates the activity of different subtypes of cortical neurons. However, major issues should be addressed to strengthen the results.

      Comments on revised version.

      The authors have addressed all our comments satisfactorily. The revisions have strengthened and clarified the manuscript.

    3. Reviewer #2 (Public review):

      This is an interesting paper with important results. The authors, working in V1, have previously, in a 2022 paper, defined sensitizing and depressing excitatory (E) cells as those whose response increases or decreases, respectively, across the 10 seconds of showing a drifting grating stimulus. They showed that sensitizing E cells are dominantly inhibited by SST inhibitory cells, which are dominantly depressing, and that depressing E cells are dominantly inhibited by PV inhibitory cells, which are very largely sensitizing. It's been well established that locomotion greatly increases E-cell firing rates in V1 compared to rest, but much remains to be worked out as to the mechanism. Here, they find that locomotion increases the responses of the sensitizing E cells much more than depressing cells. They develop a model of changes in synaptic weights between rest and locomotion to account for the changes. One reason that sensitizers are increased more by locomotion than depressors is that PV cells, which more strongly inhibit depressors, have increased firing for locomotion, whereas SST cells, which more strongly inhibit sensitizers, don't change their firing rates with locomotion. However, in the mode,l a complex array of postulated changes in connection strengths is also involved.

      Comments on revised version.

      To my previous review, I just want to add that the authors have taken the reviews very seriously, responded to them thoroughly and well and with a number of new studies that greatly strengthen the work.

    4. 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. eLife Assessment

      This manuscript employs dorsal-ventral telencephalic organoids derived from Huntington's disease (HD) patient iPSCs, together with analyses of HD mouse embryos, to investigate early neurodevelopmental alterations associated with juvenile HD. This invaluable study addresses an important and emerging aspect of HD biology, namely the contribution of developmental defects to disease pathogenesis, and provides solid evidence for altered differentiation trajectories and cell fate specification. The data supports the conclusion that HD cells exhibit abnormal neurodevelopmental programs, including an increased propensity to acquire choroid plexus identity, thereby implicating developmental dysregulation as a potential contributor to HD pathogenesis.

    2. Reviewer #1 (Public review):

      [Editor's note: This version has been assessed by the Reviewing Editor without further input from the original reviewers.]

      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.

      After revision the manuscript is a valuable contribution to the field.

    3. 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 containing 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.

    4. 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. eLife Assessment

      This study provides important findings on the neural mechanisms underlying visually guided avoidance in Drosophila. The results identify LC10d visual projection neurons and their downstream partners DNa10 as drivers of object avoidance, in contrast to the courtship-promoting LC10a neurons. The evidence supporting a role for LC10d is solid, although some analyses would benefit from improved statistical quantification and presentation. In contrast, the evidence that DNa10 specifically mediates LC10d-dependent avoidance is incomplete, due to potential DNa04 contamination and other experimental confounds.

    2. Reviewer #1 (Public review):

      Summary:

      In this paper, Ribeiro and colleagues investigate male orienting behavior during courtship to identify the neural pathways involved in visually-guided avoidance. The major claims are:

      (1) Before courtship has begun, the male generally avoids other flies. This avoidance depends on LC10d neurons (Figures 1 and 2).

      (2) LC10d neurons are broadly tuned to visual objects, and they mediate visual avoidance behavior (Figure 3).

      (3) Unilateral activation of LC10d neurons drives contralateral turns (Figure 4).

      (4) Anterior-facing LC10d neurons preferentially connect to a descending neuron called DNa10, and these neurons mediate avoidance behaviors (Figure 5).

      Overall the initial observations are supported with solid behavioral evidence, although there are issues with clarity of anayses and writing that make it difficult to evaluate at times. I thought that the latter two claims are not well supported by the data and analyses as presented. I think that improving the analysis, statistics, and, in some cases, the claims being made with the data could overcome these weaknesses.

      Strengths:

      (1) Figures 1 and 2 show solid behavioral evidence with some interesting and clever analyses, including the change detection and event-triggered analyses.

      (2) The visual tuning characterization (Figure 3) shows strong evidence that these neurons are more broadly tuned to visual objects than LC10a.

      Weaknesses:

      I found this manuscript to be a very difficult read, and I think it needs a major overhaul of the writing throughout. At multiple points, the writing is very unclear. I also ran into some points where the claims in the text are not consistent with the data. Some representative examples include:

      (1) In lines 209-210, it is stated that "Both forward accelerations and decelerations contributed to an increase in female frontal positions (Figure 2D)". However, Figure 2D seems to show that there is a decrease in female frontal positions for accelerations (all genotypes) and perhaps a weak increase in frontal position for the two silencing genotypes.

      (2) Related to the plots showing the y-axis projection of the heatmaps (e.g. Figure 1 G, I):

      a) I believe what the authors want is the orientation of the male relative to the location of the female; to quantify whether he is facing her. These plots show the distance, but then the orientation is not clear beyond anterior vs. posterior.

      b) How were these projections normalized? Are the different lines comparable in amplitude? Shouldn't these have units of % rather than a.u.?

      c) The quantification (AUC in the anterior field) is just mentioned in the figure legend with p-values. It would be useful to show the AUC values to get a sense of fly-to-fly variability and effect sizes.

      (3) There is analysis of the LOV-LexA experiments (Figure 4). With the way the data are currently presented, I don't feel confident in the claim that LC10d drives contralateral turning.

      (4) Figure 4, D and E: It should be clearer (in the text, labels on plots, and/or figure legend) what the "unilateral expression factor" is. The text (line 319) refers to a count of cells expressing on each side, but I can't figure out how it was calculated. Do negative values correspond to bias on one half of the brain while positive values correspond to a bias on the other side?

      (5) Figure 5: A straightforward reading of the DN blocking experiments would suggest that silencing DNa04, but not DNa10, changes male orientation behavior. The data in Figure 5 either only show results from the combined DNa04/10 driver or show negative results for the DNa10-only driver.

    3. Reviewer #2 (Public review):

      Summary:

      This work by Ribeiro and colleagues examines circuit mechanisms by which the fruit fly regulates its behavioral response to moving objects. Previous studies, including one by the authors, identified that LC10a visual projection neurons promote tracking of female flies during male courtship behavior. In the present paper, the authors focus on LC10d visual projection neurons and show that these neurons mediate avoidance of visual objects, thereby revealing opposing functions performed by closely related visual projection neurons. In contrast to LC10a's role in promoting courtship pursuit, LC10d appears to promote object avoidance before courtship begins, as silencing LC10d results in increased tracking of visual objects. In vivo functional imaging experiments show that LC10d is broadly tuned to moving objects, and analyses of the connectome and subsequent behavioral experiments identify a class of descending neurons, DNa10, as a downstream behavioral effector of a subset of LC10d with frontal receptive fields. Together, this study suggests an important role of LC10d in regulating behavioral responses to moving visual objects.

      Strengths:

      (1) Specific genetic drivers were used to perform behavioral manipulation and calcium imaging, revealing behavioral roles and stimulus tuning of previously uncharacterized LC10d neurons.

      (2) Many experiments were performed in parallel for LC10d and LC10a, allowing for direct comparisons of behavioral phenotypes and stimulus responses between these two neuron types.

      (3) In addition to the role of LC10d neurons in male object avoidance, the paper also investigates their role in females and shows that this avoidance maneuver (i.e., displacing the object out of the frontal visual field) in females facilitates male courtship behavior, suggesting how a sexually isomorphic behavioral response can lead to sexually dimorphic consequences during courtship.

      Weaknesses:

      (1) The study would benefit from more statistical rigor. Many behavioral observations central to the paper's conclusion are not accompanied by statistical testing; for example, the apparent pre-courtship avoidance of the visual object and its suppression upon LC10d silencing.

      (2) Many important panels report only center values without error bars or confidence intervals; thus, it is not possible to assess the variance of data (e.g., fly-to-fly variability), making it difficult to judge the robustness of the effects.

    4. Reviewer #3 (Public review):

      At a distance, animals have to make decisions on whether to approach or flee. The sensory information at such distances is often ambiguous and contains only sparse visual information. Primarily using the pre-courtship behavior of D. melanogaster as a model, Ribeiro et al. investigated how animals respond to such sparse visual information. The authors identified that male flies predominantly avoid females before courtship, placing them in their posterior field of view. Unlike when blocking other visual projection neurons, this avoidance behavior was not found upon blocking LC10d transmission. This work is the first to identify LC10d involvement in such a behavior as well as its broad tuning to objects. Further behavioral experiments identified the involvement of DNa10, a descending neuron downstream of select anterior-facing LC10d neurons. In addition to demonstrating the use of this circuit across sexes, the motivation and context for the work are clearly described.

      Beyond its implications for Drosophila researchers, this work is important for the broader circuit neuroscience community by generating evidence for the use of visual chunking during complex social interactions. The strength of evidence supports the majority of their conclusions, but there are aspects of the manipulations to DNa10 that need to be clarified and further described.

      In Figure 5, the authors use two lines for manipulating DNa10 activity, one of which contains a contaminating neuron (DNa04). For Figure 5E and 5I (lines 344 - 355), the authors state the effects of DNa10/04, but the results from the DNa10 alone data are either not shown or not performed. In the male CNS dataset, the DNa04 second top major target is also LC10d, suggesting a confound for these experiments that is not discussed. Additionally, the authors do not discuss the number of DNa10 cells or the expression level across these two lines that could account for any differences found. The authors should discuss these potential effects in the text.

    1. eLife Assessment

      This study examines how repeatedly tracking a tilted moving pattern with the eyes changes the smooth pursuit eye movements used to follow it. While the initial bias in pursuit direction evoked by such a stimulus does not change with training, later corrective smooth pursuit eye movements happen sooner. This is a valuable study that is of interest to researchers studying eye movements, motion perception, and sensorimotor learning. Yet, the strength of evidence is currently incomplete, as the possible influence of catch-up saccades is neglected and analytical choices are inconsistent; furthermore, alternative possible interpretations could be considered and discussed.

    2. Reviewer #1 (Public review):

      Summary:

      Schoeffel and colleagues investigated the plasticity of sensorimotor biases. As a test case, they used the influence of the aperture problem on the initiation of smooth pursuit: when a grating is moving in an oblique direction relative to its orientation, pursuit initiation is biased towards the direction orthogonal to the orientation before this error is corrected and pursuit tracks the actual 2D motion direction. Here, this well-known phenomenon was studied before and after a training block that contained repeated exposure to one stimulus orientation. The initial pursuit response remained biased even after training, while an early correction of this bias increased after training. The correction only occurred for stripped patterns but not for a homogeneous target, indicating that the learning was contingent on the stimulus. Since the correction occurred before sensory feedback of the initial pursuit response became available, the authors conclude that it is triggered predictively based on the motor signal.

      Strengths:

      The highlights of the study are the extensive data collection and the elaborate methods: the combination of pre- and post-tests within one session and training over five sessions allows for study plasticity at multiple time scales. The clever manipulation of stimulus features allows us to identify the reference frame of learning. The comprehensive and detailed analysis of smooth pursuit eye movements allows to reliably distinguish between the initial bias and its correction and to precisely assess the time course of correction, both within a trial and across trials.

      Weaknesses:

      The analysis is focused on smooth pursuit and does not consider catch-up saccades that were removed from the velocity traces by linear interpolation. Without information on the frequency and direction of catch-up saccades, it remains unclear whether saccades contributed to the correction and how they were affected by the training.

      The authors interpret their results as evidence that the early pursuit correction is driven by the sensorimotor signal during initiation. I do not quite understand how they can ultimately exclude the possibility that the error correction is driven by a dynamic change in the sensory motion signal.

    3. Reviewer #2 (Public review):

      Summary of aims.

      The authors ask whether training on an obliquely oriented Gabor patch changes how people later follow differently oriented Gabor patches with their eyes. Tilted patterns produce a bias in the initial direction of pursuit because of the aperture problem. The authors report that this initial bias does not change over five training sessions. They do report a compensatory pursuit response that corrects the direction of the eye movement, and that this correction becomes faster with training. They attribute the faster correction to a later compensatory response, and they interpret this as learning in internal sensorimotor models.

      Strengths.

      The experiment is well done, and the question of how sensorimotor learning deals with a perceptual bias that cannot be removed is interesting. The interpretations are reasonable and fit the general approach of the study. Including independent conditions and a separate cohort is also a useful addition.

      Weaknesses.

      My main concern is that the results are hard to follow and at times inconsistent, and the analyses may be more extensive than needed.

      Do the results support the conclusions? The central idea, that training speeds up a delayed compensatory correction without changing the initial bias, is plausible and may well be correct. As the paper stands, however, the support is only partial. The inconsistent windows and sessions, the statistical issues, and the unclear description of how the key latencies were obtained make it hard to judge how robust the main findings are. The pattern of analyses can also give the impression that they were chosen after the fact.

      Impact.

      If the findings hold up under a clearer and more consistent analysis, they would be of interest to researchers studying eye movements, motion perception and sensorimotor learning.

    4. Reviewer #3 (Public review):

      Summary:

      The study explored smooth pursuit dynamics when human participants tracked moving gratings and blobs. If the grating is oriented obliquely relative to the pursuit direction, the initial direction of smooth pursuit initiation reflects the well-known aperture problem and is orthogonal to the grating orientation (even if the grating itself is moving in another direction). Very quickly, pursuit then corrects itself because there is also the position signal indicating where the target is. The authors here trained participants to see only one orientation repeatedly. The initial aperture problem effect did not disappear in smooth pursuit initiation, but pursuit was faster to correct itself and follow the true target position. The authors interpret this as the pursuit system having a compensatory learned mechanism.

      Strengths:

      The paradigm is suitable for exploring learning.

      Weaknesses:

      I have several issues with this study, which I summarize here and then further in the detailed comments below. First, an alternative explanation of the results could be sensory adaptation to the repeated exposure to the one grating orientation. That is, the repeated visual exposure to one grating might adapt the effect of the aperture problem, but the target position component of tracking remains strong because target motion was randomly interleaved. Second, the paradigm undoubtedly induced saccades. However, there was no analysis of them. The problem is that the saccades happen exactly at the same time at which the authors measure and infer "compensatory mechanisms" of smooth pursuit. And we know for a fact that saccades alter smooth pursuit parameters. So, are the authors measuring pursuit or measuring the effects of learning on saccades, and then the changes in the saccades themselves alter pursuit? This is a fundamental question, and it was a bit sad to see absolutely no mention of saccades at all in the whole paper! Third, for the effects with vertical gratings (in which no compensation should be observed but is observed), there could be alternative explanations for the observations, which are not considered at all. For example, the authors did not consider calibration asymmetries and also asymmetries in where people look (for extended objects like in the stimuli used, we know that there are biases in eye position that are very real). Finally, the paper is really not clear in many places, especially in the figures. It is leaving way too much for the reader to infer, and it needs to be written much more carefully.

    1. eLife Assessment

      This useful study asks whether medial prefrontal cortex activity reflects prediction error or instead tracks salience and movement across appetitive and aversive tasks. The movement-related findings are the supported by convincing evidence, but the evidence for the other conclusions is incomplete. The design confounds prediction-error sign with outcome delivery versus omission, bulk photometry cannot rule out prediction-error coding, and opsin is confounded with sex in the optogenetic experiments. This study will be of interest to those interested in medial prefrontal cortex, learning, and related processes.

    2. Reviewer #1 (Public review):

      This study investigates whether mPFC activity reflects prediction error or salience across appetitive and aversive tasks. The authors recorded bulk calcium activity and used optogenetic manipulations to test its relationship to behavior. The cross-valence comparison, combination of photometry and optogenetic manipulations, and large cohorts are strengths. However, the experimental designs do not clearly distinguish prediction error from salience, and the optogenetic findings are difficult to interpret because the manipulations are confounded with sex. Thus, although the study addresses an important question and its methods and data may be useful to the field, the evidence does not establish that mPFC codes salience or fully support the authors' conclusions. Below are my main concerns.

      (1) The authors find no evidence of prediction-error signaling in mPFC and argue that salience explains their findings. I have concerns about this interpretation. Calcium responses could reflect sensory-event detection rather than salience. The stronger-shock manipulation is informative because mild and strong shocks evoke similar mPFC responses despite their different physical intensities. This argues against a simple relationship between the signal and stimulus magnitude. However, if salience drives neural responses, it is difficult to explain why doubling shock intensity did not increase bulk calcium activity: "the magnitude of increase did not scale with the magnitude of outcome value or RPE" (line 491, Figure 2f). A stronger shock is more painful, more unexpected, and more salient than a mild one.

      (2) The omission trials are also difficult to interpret. The absence of calcium signals during shock or pellet omission cannot distinguish between a lack of prediction error, the absence of a sensory event at the expected outcome time, or insufficient photometry sensitivity. If salience governs mPFC responses, the absence of shock may itself be the most salient outcome for the animal because it is surprising.

      (3) The conclusions overstate what fiber photometry can show. Bulk signals can average together neurons with opposing response signs. The authors can conclude that bulk mPFC photometry did not distinguish the tested outcome conditions in a manner consistent with signed prediction error. They cannot conclude from these data that mPFC lacks prediction-error or value coding.

      (4) The movement correlation is interesting, but the authors should discuss prior work linking prefrontal activity to freezing behavior (Burgos-Robles et al., 2009; Kyriazi et al., 2020; Casanova et al., 2024). Additionally, cross-correlations are computed on event-averaged traces, which show shared event-locking, not continuous coupling.

      (5) The manuscript also states that "fluctuations in Ca2+ signal were fully explained by integrated salience and general uninstructed movement across all stages of learning regardless of task-defined behavioral performance" (lines 868-870). The authors do not report a variance-explained model to support this statement.

      (6) Because the central claim is that bulk mPFC activity tracks movement, the authors should assess whether movement-related artifacts contribute to the signal, particularly during vigorous movements such as darting and shock responses. They used 405 nm light as an isosbestic control for calcium-independent motion artifacts (lines 176-178) and corrected the GCaMP signal by fitting the 405 nm signal to the 465 nm signal before calculating ΔF/F (lines 184-187; Supplemental Figure 1a-c). This correction may not remove all artifacts, including hemodynamic changes that affect the two wavelengths differently. To help readers assess whether event-related changes in the calcium signal remain after correction, the authors should show the raw 405 nm and 465 nm signals, as well as the corrected GCaMP signal, aligned to darting onset, freezing onset and offset, and shock delivery.

      (7) The freezing/darting dissociation is interesting but confounded. Darting is defined differently across cohorts: by a trained classifier using a qualitative definition ("sudden and rapid escape-like movement") in the photometry cohort, and by a velocity threshold ({greater than or equal to}54 cm/s, {greater than or equal to}0.2 s) in the optogenetic cohort. The authors should provide a quantitative definition for both cohorts and state whether shock-elicited escape responses were excluded.

      (8) The classification of rats as "pellet-responsive" or "non-responsive" is problematic. First, rats are split at zero on a distribution of post-pellet Ca2+ rises that appears unimodal (Figure 6a), and the two groups are then compared on the same calcium measure used to define them. The representational similarity analysis does not validate the grouping independently, because it uses the same pellet-evoked responses. Responsive rats also show larger responses to every task event, not only to the pellet, which raises the possibility that the groups differ in signal quality, expression, or fiber placement. The authors should compare signal-to-noise ratio, expression, and implant location between groups, and treat pellet responsiveness as a continuous variable instead of dividing rats into two groups.

      Second, the behavioral differences appeared only after a change of analysis. Summary statistics during probe testing showed no differences in reward seeking or velocity between groups (Figure 6g,h; Supplemental Figure 6). The authors then applied functional linear mixed models to the training data and reported lower reward seeking during the cue and delay, but greater reward seeking immediately after pellet delivery, in responsive rats (Figure 6i). The authors interpret these results as a more precise retrieval strategy, but the direction could be reversed. Rats that approach the magazine promptly after pellet delivery would be expected to show a calcium increase linked to that action, which, by the authors' own account, reflects movement. The authors should show, on a trial-by-trial basis, that the pellet-evoked calcium rise precedes rather than follows magazine approach.

      (9) I have several concerns about the optogenetic experiment. The constructs are not equivalent. The opsins are expressed under different promoters (Syn for ChR2, nEF for NpHR), and the GFP control uses a different serotype (AAV2 vs AAV8), so viral spread and cell-type expression may differ between groups. Both opsins are pan-neuronal and therefore also target interneurons, making the net effect of stimulation or inhibition difficult to predict. The authors should show expression spread for each construct and discuss this issue.

      (10) The opsin is confounded with sex. Figure 4b shows that most darters are female. However, darting is also present in males, and in the optogenetic experiment, where channelrhodopsin (ChR2) was expressed in males and halorhodopsin (NpHR) in females, the authors report darters in all groups (line 688: "During baseline testing, 5 out of 8 ChR2 rats, 2 out of 7 NpHR rats, and 3 out of 6 GFP rats were identified as darters"). Because distinct opsins were injected in females and males, the effects of opsin and sex cannot be separated.

      (11) Several optogenetic conclusions rest on within-group comparisons rather than comparisons with GFP controls. During the intertrial interval, GFP rats showed the same increase in freezing and decrease in velocity during light delivery as NpHR rats (Figure 8a,b), which the authors attribute to freezing naturally increasing as the next trial approaches (lines 724-726). In the context-control session (Figure 8c,d), the significant interaction is again followed only by within-group pre-versus-ON comparisons. The authors should test directly whether light-induced changes in ChR2 and NpHR rats differ from those in GFP rats. During the task, summary statistics showed no effect of inhibition (Figure 7f-i). The delay-period reduction in movement and darting (Figure 7h) is a main effect of laser across all groups, including GFP, yet the Discussion states that manipulation "in either direction decreased movement velocity (i.e., suppressed darting)" (line 813), while the Results describe the ChR2 effect as nonsignificant (line 692). Given that opsin is confounded with sex (point 10), these effects should be interpreted cautiously.

      (12) The authors hypothesized that stimulation and inhibition would have opposite effects on darting, yet both reduced darting. Still, the Discussion states that the hypothesis was "largely validated" (line 815).

      (13) The mPFC is composed of PL and IL, which have opposite effects in fear conditioning, and the recordings may also include dorsal regions. The injection coordinates (ML +1.4; lines 116-117) and the large volume of AAV9 (500 nL; line 119) make it likely that expression extended into the anterior cingulate and secondary motor cortex. Fiber placements also appear more dispersed in males than in females (Figure 1c). A movement-related signal could therefore originate in motor or cingulate regions rather than in PL, and the same concern applies to opsin spread in the optogenetic experiments. I would like to see expression maps and the movement correlation analyzed by fiber placement. In addition, the atlas levels shown in Figure 1c (+5.64 to +4.20) do not match the stated AP coordinate (+3.2) (line 116).

      (14) The criteria for learning are not defined. The Methods state only that "learning was indicated by an increase" in conditioned freezing (line 147) or in anticipatory reward seeking (line 162), without specifying a threshold or performance criterion. The two tasks also differ substantially in training. The aversive group received a single 10-trial conditioning session, whereas the appetitive group received 6-9 sessions of 20 trials, and it is not stated what determined the number of sessions for each rat. As a result, the two groups may have been at different stages of learning when prediction-error probe testing began, which complicates the cross-valence comparisons. The authors should state their learning criterion, report whether any animals failed to meet it and were excluded, show individual learning curves for both tasks, and explain how the number of appetitive training sessions was determined.

      (15) A null result in a bulk signal cannot rule out prediction-error coding, because intermixed positive- and negative-coding neurons could cancel each other out (point 3). The passages on the "ontological validity" of dopamine prediction error and on mammalian brain evolution are also not connected to the data.

    3. Reviewer #2 (Public review):

      Summary:

      Hou and colleagues aimed to characterize bulk medial prefrontal cortex calcium signal surrounding reward prediction error processing to determine encoding of value, valence, and sign. While a salience signal was observed, they also identified a causal role for mPFC activity surrounding movement, independent of task.

      Strengths:

      Overall, this manuscript from Hou and colleagues is an enjoyable read and a well-considered manuscript presenting findings that clearly were different from hypothesized. I applaud the authors for their deep dive into this and the push toward more causal interrogation of the mPFC in regulating movement-related outcomes, and think as a whole the manuscript adds to the literature. Major strengths include the careful consideration of appetitive vs. aversive behaviors and leveraging of individual differences, the integration of fiber photometry data with optogenetic manipulations, and the cautious interpretation of findings.

      Weaknesses:

      Some minor weaknesses were noted, including a lack of clarity/consideration of the specific medial prefrontal cortex subregion targeted (appears to be prelimbic), which has important implications for generalizability of the findings due to downstream connectivity, and potentially also integration with what is known for other regions (e.g., ACC) in regulating behavior. In addition, while the authors' conclusions regarding bulk signal are sound within the dataset, and their conclusion to interpret these signals with caution is valid, it may be beneficial to also interpret these findings in light of other literature describing mPFC subregion activity in the regulation of movement and actions broadly, including areas where there are alignment vs disagreement.

    4. Reviewer #3 (Public review):

      Hou and colleagues used fiber photometry to record bulk calcium activity in the medial prefrontal cortex (mPFC) of rats trained in appetitive (pellet) and aversive (foot shock) cue-outcome tasks. Probe sessions included omitted and larger-than-expected outcomes to test for prediction error signaling. They related the calcium signal to freezing, darting, and reward seeking, and they used optogenetic excitation (ChR2) and inhibition (NpHR) of the mPFC to test its causal role in behavior. The authors conclude that bulk mPFC activity does not encode signed reward prediction error. They argue instead that it reflects perceptual salience combined with uninstructed movement, and that manipulating mPFC activity alters movement, including darting. I agree that the movement findings are the best supported part of the work. However, I have concerns about the prediction error design, in which error sign is confounded with outcome delivery versus omission. I am also concerned that the salience account is not clearly defined and is not well supported by the data, that opsin is confounded with sex in the optogenetic experiments, and that omnibus statistics are not reported and the figures are hard to read. Finally, I have broader reservations about how much bulk photometry in this design can tell us about what the mPFC encodes.

      (1) Their prediction error logic for foot shock is backwards from how it is normally treated. They define RPE as value-signed (better than expected = positive, worse = negative), so shock omission is a positive error and a stronger-than-expected foot shock is a negative error. But with shock as the US, omission should produce a negative error, while presenting a stronger-than-expected foot shock should produce a positive error. More of a problem is that, with their design, the sign is confounded with whether a stimulus is delivered or omitted in both tasks. So the lack of a bidirectional RPE signal mostly comes down to omissions not producing a response and deliveries producing one.

      (2) Many important graphs contain no y-axis and only an indicator bar. This is true for all of the time course plots (PSTHs), which also have no zero line. This makes the graphs very frustrating to read.

      (3) I am not sure what they mean by perceptual salience, as it is never defined when it is used in the results. There is a definition in the discussion, but no predictions are laid out ahead of time. They report that the lack of an mPFC response to shock omission, coupled with identical responding to mild and strong foot shock, is consistent with perceptual salience. This seems circular to me, and it is not clear what this finding actually means. If anything, a perceptual salience account would predict a bigger response to the stronger shock and the larger reward, which they don't find. And by their own definition (which includes surprise) an unexpected omission should be salient too. Similarly, I didn't follow the reward analysis that was also argued to reflect perceptual salience, especially since only some of the rats (the pellet responsive ones) even show a pellet response.

      (4) The authors' conclusions about movement appear to be better supported by the data. Although, again, the graphs were difficult to follow, and it took me quite a while to figure out what the snowflake and the dartboard icons were referring to, as they are not defined in the legends. For the optogenetics, ChR2 was only given to males and NpHR only to females, so opsin and sex are confounded. Also, both ChR2 and NpHR reduced movement after cue offset, so calling the effect bidirectional seems like a stretch outside of the context session.

      (5) There are no statistics presented in the results section to support any claims. Significance indicators are given in the figure captions, and some analyses are explained there. But often the appropriate overall tests are not reported. For example, Figure 2 shows their first behavior and calcium imaging time course data. I would have expected first some kind of analysis like repeated measures ANOVA to reveal the main effects and interactions for time, trial, condition, etc. None of that is performed or is at least not reported (maybe it is in Supplemental Table 1). Instead, the time courses are reduced to slopes in chosen windows and compared with lots of separate paired t tests, and it is not explained why those windows were picked. The individual tests look to support the patterns, but they are more convincing when significant main effects or interactions of interest are reported.

      Overall takeaway:

      After reading this, and even setting aside the concerns above, my main reservation is about the overall contribution. To me, the manuscript reads as "bulk fiber photometry in this prep shows mPFC signals related to movement." I think that is probably true, and the movement data are the strongest part of the paper. But I'm not sure it moves the needle much on what we think the mPFC does. If one were to set out to rigorously test movement coding against these alternatives, I think it would take two things. First, the behavior would need to be designed to decorrelate movement from the other variables. That could mean cues or outcomes that differ in value or prediction error while eliciting matched movement, or the same outcome reached through different movement requirements. Second, the recordings would need single-unit or cellular-resolution precision. Bulk fiber sums activity across the whole population under the fiber, so it can't tell a uniform movement signal apart from a mix of neurons that separately encode movement, salience, or prediction error. Opposing signals could also cancel out in the bulk average. For example, prediction error neurons with opposite signs could sum to nothing, which may help explain why they don't see one.

    1. eLife Assessment

      This important study provides novel insights into how the medial temporal lobe and visual cortex flexibly represent concepts according to current task demands. The authors developed an ingenious experimental design to provide compelling evidence that patterns of activity in memory-related brain regions, particularly the hippocampus, reflect conceptual relationships relevant to the current task. Some additional analyses could further clarify the nature of the task-specific effects and how they relate to memory.

    2. Reviewer #1 (Public review):

      Rau et al. ask whether stimulus representations change as a function of task demands, and whether properties of these task-specific representational spaces relate to the formation of episodic memories. Participants are presented with pairs of animal stimuli and rate their relationship along two pairs of feature dimensions (e.g., Size & Activity versus Proximity & Climate). Each pair defines a context. The authors reconstruct participant-specific representational spaces and investigate how their geometry relates to multivoxel activity patterns in the medial temporal lobe, how these representations reorganise across task contexts, and how neural representations relate to subsequent episodic memory.

      The paper asks whether existing conceptual knowledge representations in the MTL are dynamically reorganised depending on task demands. This is an important and well-motivated question. By leveraging participants' existing knowledge about animals together with a clever within-stimulus manipulation of task context, the study provides a relatively direct test of whether representational geometry flexibly reorganises with behavioural relevance

      The analyses are executed carefully. For example, the reconstruction of representational spaces is validated using leave-one-pair-out cross-validation, and the critical neural analyses are restricted to inferred concept pairs. The relationship between behaviourally reconstructed spaces and neural representations therefore cannot simply be explained by the specific comparisons participants made during the task. Potential confounds, such as perceptual similarity and mean BOLD activity, are explicitly controlled for in the neural similarity analyses.

      Overall, I really like this paper. The experimental design and the analyses are very thorough, and I find much of the data convincing. I have a few suggestions that I think could be addressed to improve the paper:

      (1) There is no temporal gap between the second stimulus presentation and the rating period. Because the BOLD response is slow, responses elicited by the second image, stimulus comparison and evaluation, response preparation, and potentially the motor response will overlap substantially. I am therefore concerned that an RSA effect attributed to a "task-specific representation of the concept during image viewing" might partly reflect the ensuing relational evaluation process. Could the authors clarify how well the image and rating event regressors can be separated? I would also suggest testing the RSA effect using the first images alone, because these are temporally better separated from the rating period. If the task-specific RSA effect holds for these images, the claim of task-dependent representational geometry during stimulus viewing would become considerably stronger. If this is not the case, I suggest toning down statements such as "task-relevant information affected representations during the viewing of the images, before behavioral ratings were obtained".

      (2) I am uncertain about the concept-level "remapping" measure. The authors define it as the difference in radial distance from the origin between space 1 and space 2. Firstly, could the authors clarify whether the concept-level reorganisation measure is the signed difference between distances to the origin or the absolute difference? The Methods and Figure 4 caption specify dist(space1) - dist(space2), whereas the exclusively positive values in Figure 4B and the interpretation in terms of the magnitude of reorganisation suggest that the absolute difference may have been used.

      (3) More generally, I am wondering whether a change in radial distance really measures how much a concept moves between two spaces. For example, a concept could have the same distance from the origin in both spaces while having very different relationships to the other concepts. Measuring only changes in eccentricity would show no remapping in such a case. One possible alternative would be to characterize each concept by its vector of distances to all other concepts and quantify how much this relational profile changes between spaces, for example:

      concept remapping = 1 − corr(distances to all other concepts in space 1, distances to all other concepts in space 2)

      The less similar the two relational-distance profiles are, the greater the remapping. Could the authors show whether the results hold with this or another measure that captures changes in relational embedding beyond changes in eccentricity?

      (4) The two images are encoded under quite different circumstances: the second image is immediately followed by the rating process, whereas the first image is not. The authors show that larger 2D distances predict higher subsequent memory confidence for first and second images (although the effect seems to be more pronounced for second images), but they do not report whether memory itself was better for first versus second images, nor whether the distance effect differs significantly between positions. This could be informative to know. Furthermore, the analyses relating representational distance to memory confidence appear to be restricted to subsequently remembered stimuli. Does this relationship also hold when all encoded items are included? This would more directly test whether representational distance predicts subsequent memory strength, rather than "only" confidence among images that were successfully recognised.

    3. Reviewer #2 (Public review):

      In this study, Rau and colleagues investigate how concept knowledge is organized into task-specific representational spaces in the MTL, and how this relates to episodic memory formation. Using behavioral ratings of animal concepts in two task contexts, they reconstruct conceptual spaces and show that MTL, and particularly HPC, representations align with task-relevant spaces, track their reorganization across tasks, and relate to subsequent memory. This is an interesting and well-designed study that addresses important questions. The methods are careful, and testing generalization via inferred concept pairs is an elegant approach.

      I have a number of questions, including clarifications and questions about the analyses. These concern what some of the metrics capture and how they relate to the authors' conclusions.

      (1) On inferred distances / latent spaces:

      The RSA is restricted to inferred (never directly rated) concept pairs, which seems an important feature of the design: regions aligned with these distances represent a task-relevant space that generalizes beyond the explicitly probed comparisons. This could be emphasized more. Relatedly, I was surprised not to see frontoparietal or "multiple-demand" regions, which might be expected to represent task-relevant comparisons. One possibility is that such regions encode the explicitly compared pairs (external attention), whereas HPC and default-mode regions encode the latent space supporting inference (internal attention). Could the authors test this by, e.g., comparing alignment for rated vs inferred pairs?

      (2) Sizes or strength of the effects:

      Inferring distances is a nice approach, and the cross-validation is a good way to test whether the reconstructed spaces are valid. Is there a sense of prediction accuracy, for example, the error and variance for a given inferred distance? A standardized measure might be more interpretable.

      Similarity is greater for task-relevant than task-irrelevant spaces. Are the absolute values interpretable, or do they depend on how participants used the rating scale? In any case, a noise ceiling or effect size measure would help indicate how strong these effects are.

      (3) Space-level reorganization (Figure 4A):

      What does the space-level reorganization analysis (Figure 4A) show? As I understand it, space1-space2 similarity is computed separately for the reconstructed behavioral spaces and the HPC concept RSMs, and the two values are then correlated across participants. It's not clear to me why this between-participant relationship would indicate that the HPC flexibly reorganizes representations according to task demands. The subsequent within-subject concept-level analysis seems to capture this better?

      (4) Concept-level reorganization metric:

      Could the authors clarify how the origin (0, 0) of the reconstructed spaces is defined? Since the least-squares solution is only determined up to a constant shift, I assume the origin corresponds to the centroid of the concepts, but it would help to state this. It would also be useful to confirm whether dimensions were scaled (e.g., z-scored) before computing distances. Otherwise, differences in rating spread between spaces could influence the metric.

      More generally, I wondered whether the metric captures reorganization per se, or rather a change in how extreme or atypical a concept is relative to the others. A concept could change its relationships to other concepts substantially while keeping a similar distance from the centroid.

      This also seems different from the neural measure, which reflects how much a concept's own pattern changes across spaces. Would it be more straightforward to compare each concept's pairwise distances to the other concepts across spaces? This would also relate more clearly to the neural data, for example via the equivalent neural similarity profiles.

      Finally, the hypothesis implies greater neural differentiation across than within spaces for concepts that reorganize more. Between- and within-space similarity are currently tested separately, but a significant effect for one and not the other does not show that they differ. Would it be informative to test a per-concept differentiation score (within minus between) directly?

      (5) Memory confidence:

      Why is position in the space predicted to relate to memory confidence rather than to memory performance itself? I would have predicted an effect on memory, since a concept that is more distinctive in this space should be better remembered. I would have predicted this even more so for sensory features.

      (6) Anterior-posterior HPC:

      Is there an anterior-posterior HPC difference for more abstract vs more concrete conceptual features, and potentially in other areas? For example, size is relatively concrete, whereas proximity and climate are more abstract or less tied to perceptual features (though I'm not sure of the exact ranking).

      (7) Voxel overlap analysis:

      The overlap analysis (Figure 6D-E) compares voxels within TFCE-significant clusters across contrasts. However, cluster extent depends on the sensitivity of each contrast rather than on the tuning or strength of individual voxels. For example, the task-specific map includes very large clusters, and the DNN map combines eight layers. Absence of overlap also does not imply absence of a representation, since voxels may carry information below threshold. The percentages may therefore be misleading. Could the authors use a threshold-independent approach, such as correlating unthresholded maps or comparing effect sizes within ROIs?

    4. Reviewer #3 (Public review):

      Summary:

      The authors investigate whether conceptual representations in the brain, and in particular in the medial temporal lobe, flexibly adapt to current task demands, and whether these representations shape memory formation. Participants rated pairs of animal images on two conceptual dimensions during fMRI, each in two distinct two-dimensional spaces. From these ratings, the authors reconstructed participant-specific cognitive maps and related them to neural pattern similarity. Neural similarity in the hippocampus and perirhinal cortex reflected distances in the task-relevant space, and representations in the medial temporal lobe and across ventral and dorsal visual regions were more aligned with the task-relevant than the task-irrelevant space. In a surprise recognition test, representational distinctiveness along the visual hierarchy predicted subsequent memory.

      Strengths:

      This is a timely study that brings together work on conceptual knowledge, cognitive maps, and episodic memory. I found the design particularly clever. Because each participant rated the same concepts in two spaces that share no dimensions, task effects can be tested within participants, and the use of a new exemplar on every presentation makes it possible to test memory for individual images. The reconstruction of the full representational spaces from a limited number of ratings is a nice solution, and restricting the neural analyses to pairs that were never directly rated is a good way to test whether the representations go beyond the comparisons participants actually made. I also appreciated the control for mean activation and for perceptual similarity across all layers of the DNN, which makes it more likely that the effects are not simply visual.

      Weaknesses:

      (1) The authors write that RTs were predicted by the currently rated dimension "but not by the other feature dimension". However, the other dimension also has a significant effect (P = 0.001), and the positive Z suggests that RTs were longer when animals differed more on the unrated dimension. So the rated dimension has a stronger influence, but it is not specific, and the text should be changed accordingly. Also, the Z and χ² values for this effect do not seem to match (Z² ≈ 534, but χ² = 10.89). Please double-check.

      (2) I am not fully convinced by the subtraction used to get the task-specific effect, especially looking at the MTL results. In PRC and PHC, there is a significant negative relation with the task-irrelevant space. In PHC, the task-relevant correlation is not significant (P = 0.075), so the task-specific effect in that region seems to come mostly from the negative irrelevant correlation, not from the relevant space. Something similar may be happening in PRC. If so, "task-specific" means something different from what the reader would assume, and this deserves some discussion. Could the two reconstructed maps be correlated within participants? In that case, fitting one map would partly mean not fitting the other, and the subtraction would not tell us what each map explains on its own. It would be useful to report the correlation between the space1 and space2 distance matrices for each participant, and to check the task-specific effects with multiple regression (both matrices as predictors) or partial correlation.

      (3) The voxel-overlap analysis (lines 441-458) is interesting, but I think the conclusions go a bit beyond the data. Some points:

      (a) How many voxels survive the threshold depends a lot on the power of each analysis, so the 66% of task-specific voxels does not necessarily mean "broad spatial tuning towards task-relevant feature representations".

      (b) The binomial test assumes voxels are independent, which is hard to justify with smoothed data and searchlight spheres. I am also not sure a uniform distribution across formats is a meaningful null.

      (c) The overlap with SME voxels is reported without a chance level. Something like a spatial permutation, taking map size and autocorrelation into account, would make these numbers easier to interpret.

      (d) If overlap is expressed relative to map size, Fc has the highest overlap with SME (58% of Fc voxels) and the task-specific format the lowest (18%). This seems to go against the idea that task-relevant formats are preferentially encoded, no?

    1. eLife Assessment

      The manuscript lays out an investigation into an explanatory principle to describe the secretion of metabolites by microorganisms. The authors propose a hypothesis based on the concept of metabolite value and provide compelling computational and experimental evidence to support their hypothesis. The work generates important insights that could be beneficial for researchers across a range of disciplines.

    2. Reviewer #1 (Public review):

      Summary:

      This manuscript addresses how and why intracellular-specific metabolites associated with biosynthesis end up outside microbial cells. Using a variety of approaches (analytical chemistry, metabolic models, comparative analyses of mutants) and incorporating their own data as well as data from previous studies, the authors find an inverse relationship between metabolite externalization and the cost of producing those metabolites, and that both uptake and efflux transporters are major participants in determining extracellular metabolite levels.

      Strengths:

      (1) Presents much useful raw information that will benefit the broader community interested in microbial physiology, ecology, evolution, and biotechnology.

      (2) Compares the authors' own data with data from previous studies.

      (3) Considers and addresses alternative hypotheses.

      (4) Varied approaches and data sets without losing sight of the core motivating questions - this is a large and impressive amount of work.

      (5) Distils many diverse data sets to deliver clear and insightful interpretations.

      Weaknesses:

      No weaknesses were identified by this reviewer. There is always more to learn, but this manuscript already delivers more than I would typically expect; this is an important advance in an area that has been of much recent interest and debate.

    3. Reviewer #2 (Public review):

      The manuscript addresses the lack of a general explanatory framework for the secretion of metabolites by microorganisms and proposes a compelling hypothesis - the concept of "metabolite value" - which is tested both computationally and experimentally. The hypothesis is clearly formulated and represents a promising attempt to offer a unified perspective on this long-standing question.

      Previous major comments (from review at another journal):

      (1) L58ff: Only net accumulations of one average cell in a potentially heterogenous cell population can be measured. More "valuable" metabolites would also be preferentially taken up by other cells. The authors should comment with respect to the working hypothesis.

      (2) L90ff: There are some open questions regarding the selected metabolome data. Of the 126 metabolites measured, up to 56% were released during exponential growth, and 34 of these were used to calculate the release rates. Although the amount of data is considerable, it remains unclear why these particular metabolites were selected. For example, why was metanephrine included as a non-native metabolite of E. coli? Why not just focus on the metabolites that are mapped by the applied GEM?

      (3) L105ff: To substantiate the hypothesis regarding metabolite value, the use of data sets from different strains and conditions, as well as different GEMs, is compelling. However, if the hypothesis is correct, one could question the validity of models that currently do not take metabolite release into account. In this way, the single-factor approach, which examines the effect of the release of a specific metabolite on the growth rate, could lead to distorted results. The authors should comment on this.

      (4) L127ff.: The statement that "43% of the variability" is explained by metabolite value is difficult to interpret without further context - it may represent a substantial effect, or it may be of limited explanatory power. This requires clearer framing. It is also surprising that intracellular concentration appears to have such little influence. While the data may support this conclusion, the result is counterintuitive and would benefit from further discussion or contextualization.

      (5) L193ff: Without Figure S20B, it is impossible to understand the effects of the various knockouts in the cell. Why was DlacA used as a negative control? Furthermore, it is to be expected that the substrate of an enzyme whose gene has been deleted will accumulate. To what extent does this approach, which is based on such clear genetic disturbances, support the general metabolite value hypothesis, which is primarily intended to explain native cell metabolism?

      (6) Figure S25: Based on the raw data shown, it is not entirely convincing that a true chemostat steady state was achieved. In a properly operated chemostat, a metabolic steady state is established, meaning that extracellular metabolite concentrations reflect a balance of secretion, uptake, and dilution. Under such conditions, it is not possible to determine whether specific exometabolites are being re-assimilated; one might only conclude that their net secretion rates are constant.

      In addition, several extracellular metabolite profiles are difficult to reconcile with metabolic expectations. For example, the increase of F6P in a pgi knockout strain and the lack of accumulation of AKG-derived amino acids in a sucB mutant are surprising. The authors should provide more explanations.

      (7) L253ff: The statement that "our findings so far suggest that microbes can modulate metabolite release rates" is difficult to reconcile with the central hypothesis. The manuscript initially proposes that the abstract parameter "metabolite value" determines secretion levels, rather than active modulation by the cell. This conceptual distinction requires clarification.

      (8) The dataset of 66 knockout strains growing on glucose is extensive, but some methodological details are not sufficiently described in the "Materials and Methods" section. For example, there is no explanation as to why 8,700 measurements were performed on 2,100 samples and whether the samples were injected multiple times. Furthermore, the criteria for selecting the 10 time points and the approach for data normalization (e.g., TIC normalization) are not specified.

      (10) From a conceptual point of view, the energy costs of metabolite transport are not taken into account. If the "metabolite value" is also related to active import as a compensation mechanism, the costs associated with metabolite transport and transporter synthesis should be included in the discussion.

      Comments on latest version:

      The authors have thoroughly addressed my previous concerns.

    4. Reviewer #3 (Public review):

      Summary:

      This manuscript by Sulheim et al. aims to find general explanations for why some metabolites are found in higher abundance in the exometabolome of bacteria than others. Starting with a correlation of value of a metabolite with release, they can demonstrate that the more valuable a metabolite, the less likely it is to be released. This pattern holds over several bacterial species and carbon sources in minimal medium. The authors claim that transporters are involved in shaping the exometabolome and show that knock-outs of certain transporters affect the release significantly.

      Strengths:

      The collected data largely underscores the hypothesis by the authors that metabolite value is linked to the release rate. The big dataset generated about external metabolite concentrations upon deletion of single transporter genes is especially valuable and exciting.

      Weaknesses:

      The authors overclaim some of their findings, such as that in the evolution experiment, they would expect evolution to drive the cells to a "WT-like" state, while here, they are selecting for fast growth instead of efficiency, which would probably be closer to what the WT is showing. Moreover, the experiment showing the ecological relevance of transporter knock-outs with amino acid auxotrophs does not clearly show what they claim, as even mutants with a negative expected effect increase growth, sometimes at higher levels than the WT.

    1. eLife Assessment

      Lipid-linked oligosaccharides (LLO) are biosynthetic intermediates used across the kingdom of life to build cell walls and glycosylate proteins. In this fundamental work, the authors identify pyrophosphatases that maintain LLO homeostasis in evolutionarily divergent species: the bacterium Escherichia coli and the plant Arabidopsis thaliana. They harness bioinformatic, evolutionary, biochemical, and genetic methods to build a convincing case.

    2. Reviewer #1 (Public review):

      Summary:

      Precursors of N-glycans of eukaryotic glycoproteins and of bacterial cell wall/envelop components, such as peptidoglycans and lipopolysaccharides, comprise lipid carrier (dolichol in eukaryotes and polyprenol in bacteria) linked via pyrophosphate to specific oligosaccharides (lipid-linked oligosaccharides or LLO). Homeostasis and quality control of dolichol-linked oligosaccharides (DLO) are critical for homeostasis and quality control of glycoproteins. Likewise, homeostasis and quality control of bacterial LLO are critical for proper biogenesis of the cell wall/envelope. Suzuki group previously reported the identification of Saccharomyces cerevisiae DLO pyrophosphatase termed Llp1 and demonstrated its critical role in homeostasis and quality control of DLO by hydrolyzing surplus and/or abnormal DLO. VanZ, a homolog of Llp1 found in Gram-positive bacteria, had LLO pyrophosphatase activity, suggesting its role in homeostasis and quality control of precursors of cell wall peptidoglycan. However, functional homologs of Llp1/VanZ in Gram-negative bacteria and plants have been unknown. In this paper, the authors demonstrate that YfiM of E. coli and its Arabidopsis thaliana homolog AT1G15900 are remote homologs of Llp1/VanZ having similarities in organization of transmembrane domains and the catalytic regions. YfiM and AT1G15900 have LLO-pyrophosphatase activity. YfiM is critical in cell wall integrity. Together, these findings suggest the presence of pyrophosphatases involved in homeostasis and quality control of LLO in fungi, bacteria, and plants.

      Strengths:

      Taking advantage of DELTA-BLAST and the authors' original LLO pyrophosphatase assay, the authors discovered LLO pyrophosphatases in Gram-negative bacteria (E. coli YfiM) and plants (Arabidopsis AT1G15900).

      Weaknesses:

      (1) The authors used Man5GlcNAc2-PP-dolichol, N-glycan precursor, in LLO pyrophosphatase assays for VanZ, YfiM, and AT1G15900. Direct evidence for pyrophosphatase activities against their specific substrates is missing. Because of this, the substrate specificities of these pyrophosphatases for various LLOs are yet to be determined.

      (2) Although YfiM-KO E. coli was more sensitive to vancomycin than the wild-type strain (ID50 was 50 vs 80 micrograms/mL), it is unclear whether YfiM plays a role only in peptidoglycan biogenesis or in lipopolysaccharide biogenesis as well.

      (3) AT1G15900 hydrolyzed Man5GlcNAc2-PP-dolichol. Direct experimental evidence for the roles of AT1G15900 in N-glycans/glycoproteins (for example, phenotypic characterization of AT1G15900 mutant A. thaliana cells or plants) is missing.

    3. Reviewer #2 (Public review):

      Summary:

      In this concisely written report, Li et al. propose the role of a previously uncharacterized protein called YfiM, as a lipid-linked oligosaccharide pyrophosphatase in E. coli. This work is important because lipid-linked oligosaccharide (LLO) metabolism is poorly understood across all domains of life. First, the authors detected pyrophosphatase activity against a model dolichol-linked oligosaccharide substrate in E. coli membrane fractions via fluorescent labeling of cleaved products. The authors found a structural homolog of VanZ, which they proposed causes vancomycin resistance by hydrolyzing Lipid II in Gram-positive Enterococcus faecium. E. coli protein YfiM was identified as structurally related to VanZ using a structural model-based BLAST search. Using the purified protein and a model substrate, they examined the in vitro catalytic activity of YfiM (shown to be dependent on Ca2+ and Mn2+) and validated the proposed catalytic residues that were conserved in VanZ.

      Moreover, the authors found that deletion of yfiM led to higher sensitivity to vancomycin compared to WT, and overexpression of YfiM led to increased resistance to vancomycin. These experiments support the hypothesis that YfiM is a Lipid II pyrophosphatase (although additional experiments are suggested). Further, membranes that lack yfiM can no longer hydrolyze the model LLO substrate. Lastly, they identified a plant ortholog of YfiM and found that the plant ortholog also exhibited pyrophosphatase activity against dolichol-linked oligosaccharides, highlighting the conservation of this activity across various domains of life. These findings are strong and important, and should be of broad interest to biochemists.

      Strengths:

      The authors use complementary methods to support their findings (computational protein modeling, phylogenetic analyses, protein biochemical assays, and genetic knockouts).

      Weaknesses:

      The work does not show a direct assay that tests YfiM with the proposed substrate (Lipid II), and doesn't provide further evidence for a proposed compensatory mechanism against outer membrane stress upon YfiM overexpression.

    1. eLife Assessment

      This important study presents an ultrastructural atlas of extracellular vesicles and non-vesicular particles in Drosophila olfactory sensilla, using cryofixation-based serial block-face electron microscopy to catalogue roughly 7,800 particles across four antennal regions. The evidence is compelling: the cryofixation minimizes fixation artifacts, and the rigorous, well-validated methodology and morphometric analyses provide strong support for the structural classifications and spatial distributions. This work provides a foundational resource for researchers studying extracellular-particle signaling in sensory organs.

    2. Reviewer #1 (Public review):

      [Editor's note: this version has been assessed by the Reviewing Editor without further input from the original reviewers. The authors have addressed the comments raised in the previous round of 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.

    3. 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.

    4. 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.

    5. 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. eLife Assessment

      This valuable study introduces a creative Dxy-tree scan approach for identifying genomic partitions without a priori assignment of populations, with potential applicability to studies of barriers to gene flow, adaptation and speciation. The results in the study case are supported by solid evidence, although the recovery and extension of known flower-colour loci is best viewed as validation of the approach rather than providing new biological insight. The theoretical basis, including estimates of sensitivity and specificity across evolutionary scenarios and robustness to clustering and threshold choices, is, however, only incompletely developed; the broader utility and generality of the method is currently difficult to assess. The work will be of interest to population geneticists and evolutionary biologists.

    2. Reviewer #1 (Public review):

      Summary:

      The authors describe a novel method that uses genomic data to identify loci underlying barriers to gene flow among populations. The method involves estimating dxy-based trees for individual genomic windows and scanning across windows to identify deep partitions in genetic variation across populations. The authors apply this method to a pool-seq dataset collected from snapdragon populations of different subspecies that differ in flower pigmentation. Eight putative barrier loci are identified in this study, three corresponding to well-characterized flower color genes in Antirrhinum. The authors validate three other barrier loci as new candidate genes for flower color variation using genetic co-segregation analyses. The described method offers a way to identify barrier loci among populations without assigning samples into predetermined groups and can also be applied to pool-seq data that is commonly generated to examine how allele frequencies vary over geographic space. The paper would be improved by clarifying whether and how the method, as presented, reproducibly identifies barrier loci corresponding to deep divergence events.

      Strengths:

      A strength of this paper is the development of a method that can identify early genetic partitions in a set of population samples without a priori assigning them into groups. This approach will therefore be relevant to population geneticists studying species barriers. The method is flexible and can be applied to various kinds of population genomic datasets, including poolseq data.

      In a demonstration of the method, this paper identifies three new genetic loci that contribute to differences in floral color patterning between the two snapdragon taxa, which are validated using co-segregation analyses. These new findings are a significant addition to the body of work describing the polygenic basis for flower color differences among snapdragon taxa.

      Weaknesses:

      The study could be improved with further clarification of whether and how the dxy-tree scanning algorithm reproducibly identifies barrier regions. To identify groups of outlier trees, the authors first bin dxy trees based on the cophenetic correlation coefficient (c) and then identify outliers based on a threshold value of SRB=0.002. Which trees are identified as outliers appears to be sensitive to the starting seed tree (as reported in the main text), as well as the chosen value of c (as demonstrated in Figure S3). Moreover, outlier forests are chosen based on average mean division depth, and yet the mean division depth for a given forest appears to vary substantially across values of c, again demonstrated in Figure S3. 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.

      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? 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?

      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.

      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.

    3. Reviewer #2 (Public review):

      Richardson et al. propose a new method for identifying loci underlying reproductive barriers based on Dxy-based distance trees. They apply this method to the well-studied model system Antirrhinum majus and identify seven genomic regions associated with flower color loci, five of which are known from previous studies, while three new regions emerge from this study. The authors validate their findings using allele frequencies across a natural hybrid zone and link genetic variation to observed phenotypes using an impressive set of quantitative data from controlled crosses. Six regions exhibit steep allele frequency clines across the narrow hybrid zone (which exhibits no obvious difference in environment or pollinators), supporting the hypothesis that color genes are associated with reproductive barriers. One additional region is associated with plant height, though its contribution as a barrier locus remains unclear.

      The ability to perform genome scans without a priori knowledge of the phenotypic or ecological features that separate natural populations is highly valuable for non-model, less-studied organisms. The use of trees, specifically based on Dxy distances, to sidestep the need for a priori defined population contrasts reflects other recent developments in population genetics where tree topologies - which carry more information than scalar summary statistics - are leveraged for inferring population evolutionary history. The use of the root branch length (SRB) as the outlier metric makes this method tuned to detect old and highly divergent alleles sheltered from gene flow across major tree partitions. Overall, the method's recovery of known flower loci in the well-studied A. majus system lends confidence to the approach. However, some aspects - particularly related to the theory of hybrid incompatibilities and their detection through the Dxy metric, the conceptual framing of the method, and its power under different evolutionary parameters - need to be clarified.

      (1) There exists rich literature on the use of Dxy to detect so-called 'speciation genes' in the alternative contexts of primary divergence and secondary contact, with some of the best-known empirical cases consistent with the latter scenario. This secondary contact scenario is also proposed by the authors to underlie the evolution of flower loci here in A. majus. While it is clear that Dxy-tree outliers reflect deeply divergent loci, it is unclear whether these necessarily reflect barrier loci (underlying hybrid incompatibility) or if they may also reflect adaptive loci composed of old haplotypes carried by the parental lineages and maintained by divergent selection. The authors identify flower color genes as barrier loci, whereas the locus associated with plant height is interpreted in the context of adaptation. Moreover, 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. 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.

      (2) 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.

      (3) The approach of using progressive elimination to cluster trees (into forests) may be problematic, because forest clusters are not strictly determined by those with the closest tree distance but rather by the order of seed trees (e.g., if the first seed tree has a 0.7 correlation with tree T1 and the second seed tree has a 0.9 correlation with that same tree T1, then even though tree T1 is closer to the second seed tree, it will be clustered with the first seed tree's forest). Clustering error from seed tree stochasticity is reduced by repeating the tree-scanning 100 times with independent random seeds; however, implementing a convergence metric to formalize this, or implementing an alternative algorithm that avoids progressive elimination of trees, would be a more robust solution.

      (4) 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. It would be less confusing if these were simply presented as one-peak versus two-peak fitness landscape alternatives.

      The study's proposed method of blind genomic tree scans is potentially very valuable to biologists working in the fields of speciation and adaptation. Here, in this case study on the model system A. majus, complementary evidence based on allele frequency clines and validation experiments using controlled crosses provides solid support for their results. However, for general application to other species - including non-model and less-studied species - more detailed profiling of the method and clearer conceptual framing is needed.

    4. 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. eLife Assessment

      This study provides important insights into how auditory stimuli influence the temporal dynamics of visual perception by modulating brain rhythms (oscillations) in the alpha band. The authors present convincing evidence that auditory input induces a drop in visual alpha frequency, increasing the time window for audio-visual integration, and subsequently shifting the predictive role from prestimulus alpha frequency to alpha phase. The conclusions are well-supported by the combination of psychophysics, electrophysiological recordings (EEG), non-invasive brain stimulation (tACS), and computational modelling.

    2. 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.

      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.

      Comments on revised version.

      I thank the authors for carefully addressing my comments.

    3. 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 oscillations in visual perception has been widely studied, how visual cortical dynamics are influenced by cross-modal stimulation remains poorly understood. Using a two-flash fusion task, the authors demonstrated that auditory stimulation systematically prolonged the temporal window for visual integration by slowing the frequency of visual alpha oscillations. Interestingly, individuals showing greater auditory-induced slowing also exhibited a larger extension of the fusion threshold. Their results further revealed that auditory stimulation disrupted the link between prestimulus alpha frequency and perceptual outcome, while strengthening the association between prestimulus alpha phase and perception. Based on the perceptual cycles framework, the authors developed a model that accounts for these findings in terms of auditory-induced phase resetting. Importantly, the model assigns distinct roles to alpha frequency and phase: while frequency determines whether the two flashes occur within the same alpha cycle, phase modulates the reliability of the resulting perceptual report. This framework provides a mechanistic account of how auditory stimulation can differentially modulate the contribution of alpha dynamics to perception, highlighting the importance of investigating cross-modal influences on ongoing brain dynamics. More broadly, the model extends the perceptual cycles framework by proposing a mechanistic account of how alpha frequency and phase jointly shape perception during cross-modal processing. Overall, the authors successfully address their aims, and the convergence of behavioral, electrophysiological, stimulation, and modelling approaches provides strong support for their conclusions. By extending current accounts of alpha dynamics to cross-modal perception, the study offers a more naturalistic perspective on sensory processing and provides a useful methodological framework for understanding how alpha dynamics support perceptual integration across sensory modalities.

      Strengths

      The results are supported by a combination of complementary and well-established experimental and analytical approaches (e.g., two-flash fusion task, psychometric curves, and phase opposition), providing a strong methodological basis and enabling direct comparisons with previous findings in the literature. The authors also effectively relate their findings to the existing literature throughout the Discussion, placing their results within the broader context of current knowledge on alpha oscillations, perceptual cycles, and cross-modal integration.

      Importantly, the authors go beyond the correlational evidence provided by the EEG analyses by using tACS to experimentally manipulate alpha frequency, providing additional support for their main conclusions and strengthening the interpretation of the observed relationship between alpha dynamics and visual integration.

      A further strength of the study is the proposed model, which extends the perceptual cycles framework by assigning distinct functional roles to different features of alpha oscillations. In particular, distinguishing the contribution of alpha frequency from that of alpha phase provides a more nuanced account of how alpha dynamics shape perception. Importantly, this framework generates testable predictions that could be investigated using other experimental approaches and paradigms.

      Finally, the use of cross-modal stimulation provides a more naturalistic perspective on sensory processing, as perception in everyday life rarely occurs within isolated sensory modalities. By investigating how auditory stimulation interacts with visual alpha dynamics, the study therefore extends the investigation of alpha-mediated perceptual processes to a more ecologically relevant context.

      Comments on revised version.

      Following the previous rounds of review, I am very satisfied with the authors' revisions. The additional analyses and clarifications have substantially strengthened the manuscript, and the authors have provided detailed explanations addressing the points raised previously. Overall, I have no major concerns regarding the revised manuscript.

    4. 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. eLife Assessment

      This study offers a valuable investigation into how diverse cognitive states might arise from shifts in the relative phase of a fixed set of large-scale propagating modes in fMRI, rather than from reconfigurations of their functional architecture. However, the evidence to indicate that phase features decode 23 tasks better than classical activation-based features is incomplete and would benefit from a comparison against more stringent null models, a more detailed consideration of potential confounds, and a stronger grounding in existing literature. This work will be of interest to cognitive neuroscientists working on the dynamics of large-scale brain modes.

    2. Reviewer #1 (Public review):

      Summary:

      Song et al. introduce an Intrinsic Network Flow (INF) framework, which combines the power of dynamic mode decomposition (DMD) with dimensionality reduction from ICA. They describe brain signals through INF modes reflecting the amplitudes and relative temporal ordering between different INs, relating these INF modes to the principal functional connectivity gradient, and finally showing that the dynamic amplitudes and phases have different properties related to tasks and subject specificity. The most compelling result is that tasks are best discriminated by the relative phases of INF modes rather than their amplitudes, highlighting that task dynamics in the brain may depend on a stable mode organization while modulating the phases of these modes.

      Strengths:

      Using DMD on INs to gain a tractable insight into the spatiotemporal dynamics of the brain is a clear advantage of this work. The authors rightly point out that spatial modes and temporal dynamics are not often unified, and therefore this INF framework nicely addresses that limitation. The framework also accommodates the often neglected subcortex and cerebellum, which is an asset.

      The training/testing split combined with the replication analysis offers another compelling strength: the findings are stable and likely to generalize among healthy young adults. This is also bolstered by the analysis relating INF modes to the principal gradients of FC, which show that different principal gradients can be viewed as different modes with specific phase relationships between the component INs.

      In general, the main argument of the work is convincing: that the brain has stable modes with internal phase relationships (y) that manifest in macroscopic dynamical activity with between-mode phase offsets (θ) collectively constructively/destructively interfering to produce observed brain activity.

      Weaknesses:

      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.

      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.

      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?

      None of these weaknesses, however, appear to directly undermine the results that the authors do present. They merely suggest that the specific interpretations the authors want to make may outrun what their results can presently support.

    3. Reviewer #2 (Public review):

      Summary:

      The authors address how a stable functional architecture supports flexible neural dynamics. They propose that brain activity measured with fMRI is a superposition of a small number of large-scale propagating modes, or "flows". Each flow is a "wave-like" pattern that engages brain networks in a fixed order, and these flows are the same across people and across rest and task. In this view, different cognitive states arise not from reconfiguring brain networks but from changing the relative timing, or phase, of these fixed flows: which flows are in step at a given moment determines which regions appear active. The strength, or amplitude, of each flow is instead proposed to reflect stable individual traits. To identify the flows, the authors divide fMRI signals into 27 large-scale networks, fit a single linear model describing how activity in these networks evolves from one time point to the next, and take the oscillatory components of this model (13 pairs of complex eigenvectors, via dynamic mode decomposition) as the flows. Using modes fitted to HCP resting-state data, the authors report that the principal flow aligns with the first two cortical FC gradients and with subcortical and cerebellar gradients, and that the next three flows capture lateralized interactions among the default mode, executive and salience networks. Modulating only the flow phases reconstructs activation maps from 23 tasks, and FC predicted from the modes matches task-state FC. Phase features decode the 23 tasks with 89.9% accuracy, compared with 76.6% for network activation and 28.4% for flow amplitude; flow amplitudes are heritable and modestly associated with general cognitive ability.

      Strengths:

      (1) The question is important, and a compact description linking resting-state organization, task activation and individual differences is interesting.

      (2) The analyses use large, public datasets (HCP, a multi-domain task battery and an audiovisual speech dataset), with held-out prediction and an independent replication sample.

      (3) The decoding result is the most novel contribution. Phase features separate conditions whose activation maps are nearly identical, which, if robust, indicates that the timing of large-scale propagation carries state information that activation amplitude does not.

      (4) The separation of group-level modes from subject-level amplitudes provides a common coordinate system for comparing individuals.

      Weaknesses:

      (1) 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.

      (2) 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.

      (3) 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.

      (4) 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.

      (5) (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.

      Overall, the work offers a useful descriptive decomposition and an intriguing decoding result, but its broader theoretical claims are not yet supported and should be read in the context of the prior literature on similar questions.

    4. Reviewer #3 (Public review):

      The manuscript presents a potentially useful description of BOLD fMRI data that seeks to link resting-state organization with task-related activity. I hope that I can help improve the manuscript with my suggestions below, which follow a summary of the main results.

      By applying PCA/ICA/DMD to resting-state data, the authors derive a set of spatiotemporal modes they call intrinsic network flows (INFs). They then present two main results suggesting that these modes provide a useful basis for representing task activity. First, they reconstruct static, group-level activation maps using phases extracted from those same maps while replacing coefficient amplitudes with their mean resting-state values. These reconstructions achieve a mean spatial correlation of 0.73 across 23 conditions. Second, they extract INF amplitude and phase time courses and use GLMs to obtain run-averaged, condition-level classification features. Phase features outperform amplitude and intrinsic-network activation features in leave-one-participant-out testing, with a similar advantage in a second dataset. The independent resting-state basis, held-out-participant testing, and second-dataset replication are strengths. However, I am not yet convinced that these analyses establish the authors' stronger interpretation that cognitive states arise through retiming a shared repertoire of intrinsic flows.

      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.

      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.

      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.

      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.

      Until these alternatives are distinguished, the findings support useful task descriptors more directly than a temporal mechanism. If these concerns remain unresolved, I recommend emphasizing the framework's descriptive utility and presenting task-dependent retiming as a hypothesis rather than a demonstrated mechanism of cognition.

    5. 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

      Beckmann, C. F., Mackay, C. E., Filippini, N., & Smith, S. M. (2009). Group comparison of resting-state FMRI data using multi-subject ICA and dual regression. Neuroimage, 47(Suppl 1), S148.

      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.

      Song, Y., Kim, P. S., Philip, B. A., & Kim, T. (2025). Large-scale Signal Propagation Modes in the Human Brain. Neuroimage, 318, 121357.

      Tognoli, E., & Kelso, J. S. (2014). The metastable brain. Neuron, 81(1), 35-48.

      Xie, X., Cai, C., Damasceno, P. F., Nagarajan, S. S., & Raj, A. (2021). Emergence of canonical functional networks from the structural connectome. Neuroimage, 237, 118190.

    1. eLife Assessment

      This manuscript uses modeling approaches to provide mechanistic insight into the structural and dynamic properties of enhancer-promoter interactions in Drosophila. Given the interest in this field, this is a timely approach, and the results give important insights by providing predictions about the processivity of cohesin loop extrusion in Drosophila and concluding that the compartmental interaction strength is poised near criticality in the coil-globule phase space. The authors provide solid evidence to support their conclusions and the revision included approaches to mitigate the structural impact of the "homie" elements, strengthening the conclusions. The results will be of general interest to the chromatin field.

    2. 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: First, the simulations are based on biologically interpretable mechanisms (compartmentalization and loop extrusion), which may facilitate making specific experimentally testable predictions. Second, 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:

      The authors have addressed some of the comments of the first round of review. However, some of the new additions are hard to interpret and several issues raised by both reviewers remain unaddressed.

      First, the authors have included additional analysis to better characterize the dynamics during the coil-globule transition in the simulations (Fig 4), including how MFPTs change as a function of the epsilon parameter. However, Fig. 4D is extremely hard to interpret as a colormap of a deviation between two models is very hard to read. A better plot would be to plot MFPT and relaxation time tau (raw values, not deviation) vs s for different values of epsilon, as well as the scaling exponents of MFPT and tau vs s as a function of epsilon - if indeed proximity to the transition is important for long range encounters, then the scaling exponents should exhibit some sort of specific dip at the critical epsilon. I'm somewhat doubtful if that will actually be the case though.

      Despite these additional simulation results, I maintain that the paper does not provide sufficient evidence to support its title, as I had said in the first round of review. The statement that "Near-critical chromatin fluctuations facilitate long-range contacts in Drosophila chromosomes." requires very strong evidence, not from a formal statistical physics perspective, but also from a biological perspective. It would require an explicit demonstration of (1) that there indeed are near-critical fluctuations in the experimental data and (2) that these are causal for long-range contacts. This would likely require experiments to test such a claim, such as a perturbation away from the hypothesized near-critical point to show that long-range contacts are no longer possible. That is clearly outside of the scope of this computational study. Instead, the current study shows that within a relatively limited class of models, best-fit (but by no means perfect fit, as pointed out by the authors themselves in the text) appears to be achieved near such a transition within the model class. I therefore think that a title along the lines of "Polymer simulations near the coil-globule transition are consistent with enhancer-promoter dynamics in Drosophila chromosomes" would better reflect the evidence provided in the paper.

      Furthermore, the first comment by reviewer 2 remains unaddressed. In Major Issue (1), reviewer 2 suggests to determine the impact of the homie element in the experimental data underlying the study by also analyzing and comparing model prediction to the experimental data lacking the homie element from Bruckner et al, yet as far as I can tell from the rebuttal and the text this has not been done. It's a relatively simple thing to do and should be included, at least in the SI.

      Additional suggestions

      The authors discuss the shortcomings of their model in predicting all the features of the data together, in particular the fine structure of the HiC map. In the discussion the comparison to Shi et al. (ref 66 - now published in Sci Adv), could make this more explicit: yes, the Shi model is less mechanistic, but also achieves a much better fit of the data, see e.g. the HiC Map in Fig. 2A of ref 66. That predictiveness vs interpretability trade-off could be emphasized more.<br /> Another feature that none of the proposed models in this paper captures is the fact s-dependent two-locus diffusivity reported in Bruckner et al and explained in a recent preprint: https://www.biorxiv.org/content/10.64898/2026.03.10.710930v1.

      This is expected, since all the polymer models considered here incorporate spatially uncorrelated noise (as far as I can tell), and thus the MSDs all converge to a single line (e.g. Fig. 5G). This is not a shortcoming of this work, since that effect required hydrodynamic coupling which is outside of the model class considered here, but it would be interesting to discuss this in detail in the discussion since the simulations very nicely show the absence of this coherent motion.

    3. Reviewer #2 (Public review):

      Summary:

      In this work Ganesh and colleagues use experimental data from Hi-C and from the 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 interactions 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 which this study draws on 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.

      Comments on revised version.

      In their revision, the authors develop a creative work around to mitigate the effects of the homie tether elements - genetic components that are present in the live-cell data used but not the Hi-C data used for analysis in the paper, that otherwise create a conflict between the two results. Indeed, when these elements are not present, most of the genomic intervals sampled fail to interact at a frequency sufficient to induce expression by the reporter gene at all, whereas with these elements, significant transcription events were observed, and the contact frequency was increased substantially in the few cases where it was compared directly. As these synthetic elements affect both the 3D spatial organization and the dynamic behavior of the chromatin, they clearly confound any generalization to how chromatin in the wild-type Drosophila embryo behaves in a generalized sense, by identifying and masking bound interactions, the structural alterations caused by these elements was minimized, facilitating both the analysis and this interesting generalization.

      The paper would be strong still with a more thorough evaluation of the effectiveness of the masking of the tether interactions, and the corresponding improved agreement this creates between the imaging data and Hi-C data.

      These results are likely to be of interest to the broader community. They offer a plausible explanation of exciting and open quandary in the field raised by recent work. They also reinforce an emerging picture in which major properties of biological systems are poised near critical transitions of physical systems.

    4. 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. eLife Assessment

      This study presents a useful mathematical model for investigating microglia migration in the retina across different anatomical layers during acute inflammation. It provides a solid methodological and technically rigorous analysis of the modelling framework, which is applied to experimental data from three different species. The model can be used as a reference point for future studies to investigate inflammatory responses in the retina, with some current conclusions concerning the relevance of pharmacokinetic aspects potentially benefiting from more detailed analyses or future datasets.

    2. Reviewer #1 (Public review):

      Summary:

      In this paper, Jackson et al. propose a mathematical model - to be precise, an ordinary differential equation (ODE) model - of microglia migration in the retina following inflammation, which in the data used in this paper, is induced by injection of bacterial lipopolysaccharide (LPS). The model consists of a component describing the LPS absorption (1-2 equations) and a component describing microglia migration through three tissue layers (3 equations). The model is fitted to data from mice, rats, and rhesus macaques. The results suggest that microglia migration kinetics mattered the most for shaping the outcome, whereas LPS distribution kinetics and the initial distribution of the microglia appeared to matter less.

      Strengths:

      (1) The authors state that this is the first model of microglia migration in the retina following inflammation. While I did not check this claim in detail, I am indeed not aware of any earlier migration modeling efforts done in this specific field. There are a number of adjacent fields in immunology where the migration of other immune cells has been studied in great detail; examples include T cell migration in the lymph nodes, skin, liver, and brain, B cell migration in lymph nodes, tumor-infiltrating lymphocytes, and many others. This paper therefore adds to an already rich body of literature and could be potentially interesting for a diverse group of modelers in immunology. Several related migration models are cited in the paper already.

      (2) The paper is clearly written and easy to follow.

      (3) The model has a simple and intuitive structure and is easy to understand.

      (4) The model is analyzed in great detail, including several parameter sweeps and a range of sensitivity analyses that were performed to understand the uncertainty of model predictions.

      (5) The approach to calibrate the model primarily to data from one species and then perform a range of predictions of the impact of species-specific differences, given available data, is interesting and is not frequently done in the modeling literature, as far as I am aware. This could serve as an inspiration for other modeling studies.

      Weaknesses:

      (1) Related to the first strength, the links to existing models are currently not made explicit (although the papers are cited, the models are not explicitly compared to the paper's model). A more detailed comparison could make the work even more relevant for others.

      (2) The main research question of the paper - how do the different kinetic parameters shape the outcome - is rather generic and of a somewhat exploratory nature; it does not appear to be linked to a current specific question in the field of retinal neuroinflammation. This potentially limits the impact of the work; while mathematical modelers could be interested in the first model of this specific system, biologists may find this paper more difficult to digest and may be less motivated to work through this body of work.

      (3) The ratio of model parameters to amount of data appears to be on the high side. The authors are aware of and credit this limitation, and conduct multiple sensitivity analyses and practical identifiability analyses. This is laudable, but ultimately these analyses do show signs that the model may be insufficiently constrained by the data, at least in some aspects. In this regard, it could be important to clearly state the number of raw data points used (see suggestions below).

      (4) The ODE formulation of the model could overlook important spatial variation of microglia density. Since the cells appear to be quite dispersed (from looking at the figures in reference 15), an agent-based model or other spatially explicit model could add additional important insight. Indeed, the model includes a few terms such as the saturation terms in Equations 5 and 6 that appear to be included to account for such spatial effects indirectly.

      (5) The model predicts how microglia distribution across the retina should be affected by changing administration routes and/or LPS kinetics. LPS data from rats and rhesus macaques are used to re-fit the LPS part of the model, and other parameters are kept fixed. However, it seems to be at least conceivable that the other parameters could also be species-dependent. There is no data available for checking these predictions for other species, making this part of the work more speculative.

    3. Reviewer #2 (Public review):

      Summary:

      The authors present a novel, first-of-its-kind mathematical framework aimed at investigating the spatial redistribution of retinal microglia across specific anatomical layers-the outer plexiform layer (OPL), inner plexiform layer (IPL), and ganglion cell layer/nerve fiber layer (GCL/NFL)-during acute inflammation induced by exposure to lipopolysaccharide (LPS; a bacterial endotoxin). The model couples an LPS pharmacokinetic (PK) model with a system of ODEs describing cell migration between layers. The authors used experimental data from mice subject to an LPS challenge to select and calibrate a final model among different candidates. The authors then extended the framework to rats and rhesus macaques using blood LPS PK data, and simulated how different administration routes (intravenous vs. intraperitoneal) and species contexts might influence retinal microglia layout. To draw core conclusions, the authors also executed a careful global sensitivity analysis. Their primary conclusion is that redistribution patterns observed in mouse retinal microglia, and hypothesized in rats and macaques, are dictated predominantly by LPS pharmacokinetics and delivery routes rather than initial cellular distribution states.

      Strengths:

      (1) The manuscript establishes a first-of-its-kind, baseline mechanistic model for retinal immune cell movement between specific layers. This constitutes a solid contribution to theoretical studies of opthamology.

      (2) The authors perform thoughtful model selection and include in the supporting information a suite of alternative models. By testing and comparing alternative modeling hypotheses, the authors support their final choice of model as a deliberate and data-driven process.

      (3) High technical quality: The authors present a clear, thorough, and transparent technical description of the modeling and subsequent analyses. The use of profile likelihood to estimate parameter intervals is strong as it reveals any structural identifiability issues. The inclusion of a meticulous global sensitivity analysis adds rigor to the investigation.

      Weaknesses:

      I do, however, have some concerns about this study.

      (1) The authors are clear that this is a first-of-its-kind study, and while that's exciting, the authors never explicitly explain why mapping the precise spatial redistribution of microglia across the OPL, IPL, and GCL/NFL matters to the broader scientific community. This is likely low-hanging fruit: what disorders are associated with inflammation in these layers, for example?

      (2) The model relies entirely on blood concentration of LPS. That is, with one exception, every forward and backward migration rate in the ODE system (eqs 4-6) is directly multiplied by the circulating blood LPS fraction B/(B+eta_G, O). Because blood LPS concentration enters nearly every migration term, the model structurally assigns PK a central role in determining redistribution dynamics. It is difficult to disentangle whether the dominance of PK in the sensitivity analysis reflects a biological insight inferred from the data or a property imposed by the model architecture.

      (3) In equations (5) and (6), the return pathway from the GCL/NFL back to the IPL (G -> I) is modeled as a homeostatic density-dependent term (k_G*G*(G/G_0-1)) that is completely independent of B. The authors explicitly justify this choice by stating it enforces a "once inflammatory signals begin to weaken, microglia in the GCL/NFL are expected to return to their homeostatic density on a shorter time scale" (lines 190-192). However, because the k_G term lacks any mathematical coupling to B(t), it does not "wait" for the stimulus to subside, even during peak inflammation. The term appears to represent density-dependent regulation rather than inflammation-dependent resolution. The biological interpretation given in the text does not seem to follow directly from the mathematics.

      (4) It is also unclear why no LPS-dependent return pathway from the GCL/NFL to the IPL is considered. Such a mechanism could potentially provide a biologically plausible alternative to the purely density-dependent k_G term discussed above. Notably, no such term appears in any candidate model presented in the Supporting Information (the mention of k_GI in line 426 is likely a typo meant to be k_G).

      (5) The 95% Confidence Intervals (CIs) for the primary migration parameters (k_OI and k_IO) are unbounded above (line 284, Figure S3). This practical non-identifiability is rather unsatisfying and concerning: it indicates that the available mouse experimental data is insufficient to put a ceiling on cell migration speeds. The data do not appear to constrain an upper limit on migration speed (potentially because of the use of Hill functions).

      (6) Because the true statistical ranges stretch to infinity, the authors have to choose a range for PRCC. They choose to substitute an arbitrary Delta chi^2 <= 1 cutoff ("practical ranges") to run the PRCC sensitivity analysis and shift parameters through an arbitrary 600% blowout window. While the authors' transparency is commendable, the sensitivity analysis appears to depend on investigator-defined parameter bounds rather than ranges supported by the available data.

      (7) A key study prediction is that species-specific PK is a major factor affecting redistribution. However, the model uses systemic blood LPS concentration as the driving variable for microglial migration. Ocular exposure is not explicitly modeled. This omission becomes particularly important in the cross-species simulations, where anatomical differences between species could alter the relationship between systemic and retinal exposure. Because species comparisons are performed primarily by changing the blood PK profile (and, in the case of macaques, changing initial cellular distributions) while keeping retinal migration dynamics fixed, it is unclear whether the reported differences represent species-specific retinal biology or simply the expected consequence of imposing different LPS exposure patterns.

      (8) If I understand the framework correctly, the rat and rhesus macaque simulations utilize mouse-calibrated migration parameters and cellular sensitivity thresholds. Parameters governing responsiveness to LPS exposure (e.g., eta_O) are estimated entirely from mouse data and assumed to remain unchanged across species. The cross-species simulations primarily vary the blood PK profile while holding retinal response dynamics fixed. While this approach is useful for isolating the effect of systemic exposure, it limits the extent to which the resulting predictions can be interpreted as species-specific retinal biology.

    4. 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. eLife Assessment

      In this work, Panti et al. examine the electrophysiological properties of mediodorsal thalamus subdivisions in mice. This study is important for understanding how this region may support multiple integrative functions. However, the claim that the central portion of the mediodorsal nucleus is physiologically distinct is currently supported only by incomplete evidence.

    2. Reviewer #1 (Public review):

      Summary

      In this paper, Panti, Stagg, Sharott & Stedehouder investigate the activity of the mediodorsal thalamic nucleus (MD). In rodents, it has long been known that the MD is divided into three distinct subregions (central, medial, and lateral), differentiated by their afferent and efferent connections. However, until now, no one had demonstrated distinct electrophysiological properties in vivo across the three MD subdivisions.

      In this study, the authors recorded, in head-fixed mice performing a sensorimotor task, the extracellular activity of neurons from the different MD subdivisions using Neuropixels probes. They revealed differences in extracellular spike waveform (amplitude, repolarization latency, peak-to-trough ratio) as well as spiking and burst activity, with MDc neurons exhibiting higher firing rates, lower rate variability and higher burst index and rate than the other two subdivisions. They also show that a classifier based on these parameters allows categorization of neurons according to their MD subdivision, in particular the MDc.

      Strengths

      There is growing interest in the role of the mediodorsal thalamus, and its characterization is very important. MD subdivisions, due to their specific anatomical connectivity, can support distinct functions. The question of identifying MD subdivisions based on extracellularly recorded spikes is particularly compelling.

      The dataset is very strong and large and is well described in the supplementary figures. The work is technically sound, and every step of the methods used is well presented. The authors present all results from the different cohorts honestly, and they also perform various controls.

      Weaknesses

      I have concerns regarding the meaningfulness of the waveform analysis and statistical power, as well as the interpretation of the firing activity of MD units.

      (1) Waveform analysis and statistical interpretation:

      a) In Figure 2, the distinction between waveforms across subdivisions is unclear (especially Figure 2B). The within-subdivision variability appears far higher than the between-subdivision differences, raising questions about the meaningfulness of these statistical differences.

      In extracellular recordings, spike shape differences are inherently noisy. Even when comparing extremely distinct cell types, such as pyramidal cells vs. interneurons, clustering can still show at least some partial overlap, despite the major morphological differences in spike waveforms. The effect sizes shown here suggest that the observed statistical differences may potentially lack biological significance. I thus suggest trying alternative statistical tests that might be more robust, for example, considering the animal and session as random effects with a mixed-effects model/regression. Importantly, this approach can be applied to firing rate metrics (even though the effect sizes are larger, especially for the firing rate).

      b) For a single unit, how does spike waveform evolve over the course of a recording session? In extracellular recordings, amplitude drift for the same cell can happen. Can the authors describe how they control for/account for that in their data curation?

      (2) Data interpretation of spiking metrics:

      a) The MD activity was recorded during a sensorimotor task (auditory cues, reward delivery, lever presses). The authors mention, "Across all cohorts, recordings were obtained acutely from head-fixed behaving mice performing a sensorimotor task over several days" (results, lines 98-99). It is unclear which periods the authors analyze. For example, the authors mention "spontaneous firing rate over the entire recording window" (line 164). This is confusing because the authors also mention, "These large firing rate differences across MD subdivisions were similarly evident in passive interval windows (periods outside of bar movement or auditory stimulation related to the behavioral task" (lines 168-170). It is thus unclear what is meant by spontaneous activity.

      b) Regarding the results, the differences the authors observed between MD sub-divisions in terms of firing rate and burst characteristics may reflect the engagement of those different subregions to different aspects of the tasks. Indeed, it has long been known that there are differences in anatomical connectivity that might explain the differences observed. The activity is neither naïve nor spontaneous but rather context-dependent. The data set is very strong, with many MD units recorded across different subdivisions during such tasks. Therefore, analyzing MD units in regard to these different behavioral events is critical to interpret the results on firing rate and burst activity. For example, MDc might only present strong burst activity, higher firing when the animals are pressing the bar or, in general, when they are strongly engaged in the task (which can thus also be seen during the passive interval).

      (3) How correlated is the activity of MD units recorded simultaneously within the same subdivision? Are there synchronized firing patterns such as assemblies? If so, does this vary as a function of MD subdivisions?

      (4) An accuracy of 52.5% of a classifier compared to an effect of 33% chance level is not strong but rather moderate. Most importantly, there is spatial autocorrelation. From my understanding, the authors used a ten-fold cross-validation with 90% training and 10% testing. Was the cross-validation spatially blocked (by MD subdivision)? If not, I would strongly suggest doing so.

    3. Reviewer #2 (Public review):

      Summary:

      The authors perform extracellular Neuropixels recordings in awake mice to characterize the firing properties of neurons in the three major subdivisions of the mediodorsal nucleus of the thalamus, which plays roles in executive functioning and social behavior.

      The authors found that the medial, central, and lateral subdivisions did have substantial differences in their firing properties that allowed for estimation of subdivision better than chance.

      Strengths:

      The strengths of the manuscript include the importance of this topic, which expands our understanding of MD thalamus (1) so we can move beyond generalizing findings from sensory thalamus to higher-order thalamus and (2) to guide future neurostimulation strategies. The strengths include the size of the data sets and the number of animals sampled. The manuscript is well-written, and the figures are clear. The results support the conclusions. This data set will be valuable for scientists involved in studying the higher-order thalamus and lower-order thalamus.

      Weaknesses:

      The major suggestion I have is to increase the rigor by using a linear mixed-effects model to account for the effects of cohort and animal. I don't think this additional analysis will change the findings or conclusions, but it will strengthen the statistical foundation of the paper. Studying only male mice limits the generalizability of the findings.

    4. Reviewer #3 (Public review):

      The role of the mediodorsal thalamus (MD) in cognitive functions is well-established in humans as well as in several primate and rodent animal models. However, MD is not a homogeneous structure but is composed of at least three parts, the medial, central, and lateral (MDm, MDc, MDl) subdivision that bear distinct molecular profiles, input-output organization and functions. Whether similar heterogeneity exists in in vivo electrophysiological features among MD subdivisions has been unknown until now. Panti and colleagues used high-density electrophysiological measurements from distinct parts of MD in head-fixed, behaving mice to compare their basic characteristics, such as firing rate, waveform, and burstiness. They found that, in general, MDc neurons are markedly distinct from their neighbors, while MDm and MDl cells rather share similar profiles.

      This paper has a gap-filling nature, indeed. However, there are some issues that need to be clarified. Please see my detailed comments below.

      (1) It is not clear whether the observed differences between MD subdivisions are already present in the baseline or triggered by the behavioral paradigm.

      It is mentioned in the abstract and introduction that all the recordings were obtained during behavior tasks. There is a detailed description of these tasks in the methods section. However, there is not a single behavior-associated data point in the paper. If the latter is the case, task-specific analysis is necessary since any electrophysiological profiles can be influenced by the presented stimuli and/or by the triggered behaviors, by cue presentation, delayed period, reward, hit or false trials, motor (licking) actions, etc.

      (2) There were several recordings from the same mice. Even if the probes were stained with DI, how could the individual trajectories be separated after many days? And how could the individual cells be matched with a recording day and a thalamic subdivision? Even if the individual penetrations were separated by 2-300 um, it is likely that these were finally overlapped. As it is mentioned and widely accepted that units can be recorded from a 100-150 um distance, it is likely that the same cells were monitored in different recording sessions. How do the authors compensate for it? Were each recorded analyzed separately and then pooled?

      (3) Going further on this line, every penetration causes damage in the tissue. To rule out the possibility that the damage differently affected the recordings from distinct thalamic territories, each session should be individually handled and then compared before any pooling.

      (4) MD subdivisions were classified using atlases. However, it is difficult to separate MDm and MDL territories from the neighboring paraventricular (PVT) and intralaminar (IL) thalamic regions (respectively) due to the lack of sharp borders. (Furthermore, some literature data suggest the existence of a transition zone between PVT and MDm, which makes it even more difficult to separate these two thalamic areas without a cell-type-specific analysis.) It could be a possibility that MD is homogeneous; however, MDm and MDl differ in the presented dataset due to their 'contamination' with PVT and IL cells. Although the statistical powers (P values) are high, the actual differences are around 10% in most cases. Furthermore, the range of the data points is similar, only their distributions show differences. Thus, a small portion of cells with distinct kinetics could easily shift the population result.

      In addition, a cell can be recorded from 100-150 um, which is the dimension of the MD subdivisions. Thus, it is extremely difficult to identify the exact location of a cell recorded in the medial or lateral parts of the MD. Excluding those cells that are closer than 100 um may not solve this situation because outlining any brain section with a corresponding atlas can not provide a sufficient spatial resolution. Sections with DI tracks could be counterstained with neurochemical markers (visualizing thalamic subdivisions) could also help the issue.

      Another, complementary solution could be the comparison of MDm and MDl cells with those that are presumably located in the PVT and IL (respectively).

    5. 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. eLife Assessment

      The study presents valuable findings on PARP16, a regulator of pathological cardiac remodelling, by providing novel mechanistic insights and potential therapeutic targets for heart failure. The data are mainly solid; however, there are also incomplete data relating to the in vivo analyses, biochemical assays and imaging data analyses and evidence supporting direct ADP-ribosylation. The work will be of interest to cell biologists and clinicians in cardiovascular disease.

    2. Reviewer #1 (Public review):

      This study identifies a novel PARP16-NFAT1 signaling axis that attenuates pathological cardiac remodeling, supported by strong, multi-dimensional evidence from genetic mouse models, transcriptomics, ChIP-qPCR, and molecular dynamics simulations. The findings are mechanistically novel and offer potential therapeutic targets for heart failure, though several methodological and reporting issues require further clarification and revision.

      This manuscript demonstrated that PARP16 expression is significantly downregulated in cardiac tissues from heart failure patients. Using whole-body, cardiomyocyte-specific, inducible cardiomyocyte-specific PARP16 knockout and overexpression mouse models, the authors confirmed that PARP16 effectively attenuates adverse cardiac remodeling and improves cardiac function. Mechanistically, the authors integrated multiple experimental approaches, including transcriptome sequencing, ChIP-qPCR, PARP16 knockout and transgenic mouse model generation, and all-atom molecular dynamics simulations. They revealed that PARP16 mediates ADP-ribosylation of NFAT1 in a catalytic activity-dependent manner, restrains nuclear accumulation and transcriptional activation of NFAT1, and defines a novel PARP16-NFAT1 signaling axis that modulates pathological cardiac remodeling. Overall, this study is well designed, and the multi-dimensional experimental evidence strongly supports the core scientific hypothesis. The findings provide novel mechanistic insights and potential therapeutic targets for heart failure.

      However, several aspects require further optimization, supplementation, and clarification to be improved.

      (1) There are mismatches between figure citations and graphical results. The authors should carefully check and revise relevant figures, including Figure 6BCEF and Figure 8CD.

      (2) For Figure 1CD, the original high-definition images, detailed statistical workflows, and raw quantitative data regarding PARP16 expression in human failing hearts should be provided.

      (3) The study used ANP, BNP, α-MHC, and β-MHC as hallmark biomarkers of heart failure. The biological significance and rationale of these indicators should be briefly introduced in the manuscript.

      (4) Redundant phenotypic results are observed in Figure 3B/C, Figure 4C/D, and Figure 5B/C. The authors are suggested to retain Figure 3B, Figure 4C, and Figure 5B, supplement quantitative statistical analysis of protein expression levels, and provide all high-definition images and complete statistical datasets.

      (5) In lines 313-321, the authors discussed inconsistent conclusions between the present study and reference 16 and attributed the discrepancies to different disease models and experimental approaches. Does this mean that the disease model and approaches in the article are unreliable? Has any related validation been conducted in this model? The mRNA and protein expression levels of key molecules in the IRE1α-sXBP1-GATA4 signaling pathway should be detected and validated.

      (6) The official ethical approval document (HEC No: 06/22.06.2023) and written informed consent documents for human sample collection must be submitted.

      (7) Typographical errors should be corrected throughout the manuscript, such as the incorrect word "hypertrophy" (line 100).

      (8) To validate the successful construction of genetically modified mice and ensure the reliability of subsequent phenotypic and mechanistic data, the authors need to supplement detailed genotyping primer sequences, representative agarose gel electrophoresis images, and complete genotyping statistical results.

      Addressing the above-mentioned issues will significantly improve the quality, rigor, and readability of this work.

    3. Reviewer #2 (Public review):

      In this study, the authors investigate the role of PARP16, an ER-resident mono-ADP-ribosyltransferase, in the heart. To address this, they generate a set of complementary mouse models: whole-body Parp16 knockout mice, constitutive and tamoxifen-inducible cardiomyocyte-specific knockout mice, and cardiomyocyte-specific transgenic mice overexpressing PARP16. Using these models, they show that loss of PARP16 causes pathological cardiac remodeling, whereas its overexpression protects the heart from isoproterenol-induced damage. Mechanistically, they propose that PARP16 regulates the nuclear translocation and transcriptional activity of NFAT1 through mono-ADP-ribosylation (MARylation), thereby linking this post-translational modification to hypertrophic and remodeling signaling in the heart. The conclusions rest on in vivo phenotyping, biochemical assays and immunofluorescence analyses.

      Most of the conclusions are supported by the data, but some aspects of the biochemical assays, western blots and data analysis need to be clarified and improved.

      Specific comments:

      (1) Figure 1:

      In Figure 1F, the authors describe a reorganization of α-actinin, but no quantification supports this conclusion; the phenotype should be quantified. The immunofluorescence images are not sufficiently clear and need to be improved. The organization of Figure 1J is misleading, and the transfection control should be separated from the ANP and α-actinin staining. The PARP16 immunofluorescence is not convincing: no clear difference is observed between the control in Figure 1F and the PARP16-overexpressing samples in Figure 1J. If the protein is tagged, an anti-tag antibody should be used to show overexpression. The catalogue number reported in the Methods for the PARP16 antibody is incorrect. In Figures 1G and 1K, the meaning of "−ve" and "+ve" is not explained. Moreover, the graphs lack error bars, and the number of experiments is not reported.

      (2) Figure 7:

      In Figure 7B, quantification of the blot should be included. Panels 7G and 7J report the same values for VIVIT-treated samples, and their representation in two separate graphs is misleading. The authors should merge them into a single graph including pre-treatment, vehicle and VIVIT-treated samples. In Figure 7K, the identity of p-NFAT1 is unclear: is the band at the same molecular weight as total NFAT1? No arrow is indicated in the raw data file, and no molecular weight markers are shown. If it comes from a different gel, was the phosphorylated form normalized to its own loading control? Why does NFAT1 run at 140 kDa here rather than at 110 kDa, as in all other panels? The quantification in 7L does not reflect the blot shown in Figure 7K.

      (3) Figure 8:

      The description of Figure 8 in the text is confusing. In Figure 8A, the results for PARP16 WT overexpression are misleading: why is the effect of PARP16 WT overexpression more pronounced upon silencing? The authors should discuss this point and include a control western blot showing effective knockdown and rescue of PARP16 protein upon overexpression. The level of PARP16 overexpression in Figure 8C is unexpectedly low, almost comparable to the non-transfected sample, and is therefore not convincing. Moreover, GAPDH and PARP16 migrate at almost the same molecular weight (about 36 kDa), yet the band indicated as PARP16 in the raw images is at a higher molecular weight than expected and than indicated in Figure 8C. The loss of the PARP16-NFAT1 interaction upon overexpression of PARP16 Y254A should be commented on in the text. Finally, no reference to panel 8D was found in the text.

      (4) Supplementary data:

      In lines 202-206, the authors state that "immunoblotting and gene expression analyses did not reveal marked alterations in the major UPR pathways in PARP16-deficient hearts (Fig. S1E-G)", and conclude that ER stress is absent. This conclusion is only partially supported. Gene expression of UPR targets is unchanged (S1G), but the western blot (S1E) and its quantification (S1F) do not support the same conclusion. PARP16 is important for PERK and IRE1 activation upon ER stress, and phosphorylation of eIF2α (p-eIF2α normalized to total eIF2α?) is significantly reduced in the PARP16 KO samples, suggesting an alteration of the PERK axis. To rule out defects in the IRE1 branch, XBP1 mRNA splicing should be evaluated by PCR. Since PARP16 loss could affect the stability of its substrates PERK and IRE1, measuring GRP78/BiP protein and mRNA levels would help assess cardiac UPR induction. Finally, the blot shows n=3 samples, while the quantification is based on n=4; why was the fourth sample excluded from the image in the raw data of Figure S1? Additional points: the font size for "110 kDa" should be corrected. Figures S2B and S2C show the same limitations reported for Figures 1F and 1K, respectively. Figure S3E is not discussed in the main text. This panel shows an HA-NFAT1 immunoprecipitation in the presence or absence of PARP16-FLAG, but the expression of HA-NFAT1 (input) and its immunoprecipitation (IP HA) are very limited. By contrast, the amount of co-immunoprecipitated PARP16-FLAG is abundant relative to the bait, even though its expression in the input is poor compared to the non-transfected samples. Collectively, this experiment is not convincing.

    4. Reviewer #3 (Public review):

      Summary:

      This study investigates the role of PARP16 in pathological cardiac remodelling. Using multiple mouse models, the authors show that PARP16 deficiency promotes adverse cardiac remodelling and systolic dysfunction, whereas its overexpression exerts protective effects. The authors propose that PARP16 limits cardiac remodelling by inhibiting NFAT1 transcriptional activity through ADP-ribosylation.

      Strengths:

      The use of complementary genetic models, together with transcriptomic analyses and functional rescue experiments, provides substantial evidence for a protective role of PARP16 in cardiac homeostasis. The findings support the involvement of calcineurin-NFAT signalling and identify a potentially novel PARP16-NFAT1 regulatory axis.

      Weaknesses:

      The main limitation concerns the proposed molecular mechanism. Although the authors provide evidence of PARP16-NFAT1 association and identify candidate ADP-ribosylation sites, the causal link between modification of these residues and NFAT1 inhibition remains incompletely established. Moreover, the VIVIT rescue experiments support the involvement of NFAT signalling but do not demonstrate a specific role for NFAT1. Finally, the subcellular localization of the proposed interaction remains unclear, given the ER association of PARP16 and the nuclear activity of NFAT1. Clarifying these aspects would strengthen the mechanistic conclusions.

    1. eLife Assessment

      This study provides valuable insights into the structural consequences of CRISPR-Cas9 editing in human hematopoietic stem and progenitor cells, identifying large deletions and genome-wide structural variants using nanopore sequencing and Strand-seq, while demonstrating PolQ inhibition as a potential strategy to reduce large deletions. Although the evidence is generally solid and supports the conclusions, several aspects remain incomplete. In particular, further validation of genome-wide structural alterations, larger single-cell datasets, and functional studies would strengthen the findings and their implications for gene therapy safety and DNA repair mechanisms.

    2. Reviewer #1 (Public review):

      Summary:

      The authors investigate genomic structural alterations following CRISPR-Cas9 editing of DNMT3A and SRSF2 in human HSPCs, with particular attention to DNA-PK inhibition. They report that CRISPR editing induces large on-target deletions and genome-wide structural variants, while AZD7648 has a modest additional effect. PolQ inhibition reduces large deletions, and simultaneous editing of two loci is associated with increased genomic rearrangements.

      Strengths:

      The combination of nanopore sequencing and single-cell Strand-seq provides a comprehensive approach to investigating genomic alterations. The improved analytical pipeline for detecting large deletions is a methodological strength. The identification of PolQ inhibition as a potential strategy to reduce undesirable editing outcomes is particularly valuable.

      Weaknesses:

      The genome-wide structural variant findings would benefit from independent validation, particularly the reported translocations outside the targeted loci. The analysis was performed on cultured HSC-enriched cells rather than functionally validated long-term HSCs, limiting conclusions about therapeutic safety. Additionally, the mechanistic interpretation of PolQ-dependent repair requires further support.

    3. Reviewer #2 (Public review):

      Summary:

      In this work, the authors aim to explore in detail the effects of the DNA-PK inhibitor AZD7648 (AZD), previously applied by themselves and others as a strategy to enhance homology-directed repair in genome editing by shifting the balance of repair events away from non-homologous end joining (NHEJ), which is mediated by DNA-PKcs. While successful at promoting NHEJ and thus desired targeted editing, various reports in the field have described DNA-PK inhibitors as also promoting large-scale structural variants at the target site and elsewhere in the genome

      In this study, Cloarec-Ung and team use two approaches, namely bulk long-read nanopore sequencing and, at the single-cell level, STRAND-seq, an approach to map strand-specific read alignments for each chromosome, to define the nature of such SVs in singly (SRSF2 or DNMT3a) and doubly edited hematopoietic stem and progenitor cells (HSPCs) with AZD treatment. For both sequencing approaches, the authors developed custom analysis pipelines to improve/expand SV calling. In the case of long-read sequencing, this pertains to a strategy to discriminate true deletions from sequencing artifact truncated reads, while in the STRAND-seq analysis they developed a strategy to call inter-chromosomal events in addition to the intrachromosomal events previous pipelines have been optimized for.

      The authors describe two main findings:

      (1) DNA-PK inhibition modestly increases the frequency of on-target large deletions above CRISPR editing, which they also describe as inducing a high frequency of editing on its own.

      (2) They show that in the single-edit scenario, genome-wide off-target editing is low-frequency in nature with editing alone and not substantially increased with AZD. Multiple editing events did however, exhibit increased SVs, including translocations, with AZD treatment resolving this. Pursuing the potential to ameliorate the elevation of large on-target deletions via DNA-PK, the authors also explored the inhibition of PolQ-dependent theta-mediated end joining (TMEJ), a process anticipated to increase in response to the repression of NHEJ and thus potentially drive these elevated SVs. They describe the addition of a DNA PolQ inhibitor, showing through long-read sequencing a mitigation of the AZD-dependent and independent large on-target deletions.

      Altogether, this work provides validation that CRISPR cutting coupled with HDR repair carries risks of a variety of SV events, that AZD addition can promote these (in particular large on-target deletions and inversions) but modestly, and offers a strategy to mitigate some of these SVs, namely large on-target deletions. This work will be of interest to those in the gene therapy space and working to understand the fundamental control of gene editing strategies and DNA repair mechanisms.

      Strengths:

      The bilateral anchoring strategy the authors develop represents a generally useful new approach for calling a large category of deletion events on long-read data.

      Similarly, the inter-chromosomal chromatin exchange calling pipeline provides a helpful advance in measuring these changes in single-cell STRAND-seq data.

      The study provides a comprehensive mapping of all manner of SVs spanning on- and off-target deletions, duplications, inversions, and translocations through two orthogonal approaches and in the same, highly relevant HSPC context.

      The use of STRAND-seq provides an unbiased assessment of SVs across the genome and can also capture the maternal vs paternal chromosome contributions and the combinations of SVs that occur at the individual cell level, which offers new insights not previously provided with bulk-level analyses or approaches that are "bait-dependent" and linked to changes that involve the target site.

      The PolQ inhibitor (PolQi) studies provide good evidence that some of the unwanted SVs enacted in CRISPR HDR strategies can be offset by preventing TMEJ with this approach. They further convincingly indicate that the combined effects of AZD and PolQi could be an advantageous approach to both achieve highly efficient on-target editing while minimizing detrimental genomic changes, particularly large deletions.

      Weaknesses:

      Although STRAND-seq provides several unique advantages, certain questions could not be rigorously addressed in the present study. In particular, assessing statistically significant differences between conditions was complicated by the inherent cellular heterogeneity captured by this single-cell technology. Robust quantification of SV patterns generally requires profiling large numbers of cells; however, only modest numbers of cells were available for each editing condition in this study. As a result, the number of detected SV events was insufficient to support robust statistical testing across groups, necessitating more qualitative comparisons of SV patterns and frequencies.

      As the authors discuss, another caveat of STRAND-seq is the requirement of carrying out sequencing after HSPCs have been cultured for 7-9 days, which could underestimate the editing changes as cells are lost both by selection and random attrition over this time.

      While a bulk sequencing approach, CAST-seq has been used by others in the field for mapping SVs and, if tested here, could have offered a direct comparison to the author's STRAND-seq outcomes as well as a means to benchmark both techniques and cross-compare results to other studies. This strategy could also have allowed for the more direct testing of the full scope of SVs occurring directly following editing.

      Relating to the long-read sequencing done, mixing of HSPCs from female and male was performed, and the total number of male vs. female HSPC samples individually edited was small. While there was an intriguing observation of a potential increased rate of large deletions in the HSPCs of male cord blood donors, the study was underpowered and thus could not verify this with statistical significance.

      One caveat to the bilateral anchoring strategy used in the long-read pipeline would seem to be the possibility of undercalling telomeric deletions, which may be of particular importance in this study given that SRSF2 is subtelomeric on Chromosome 17.

    4. Reviewer #3 (Public review):

      Summary:

      This work uses the Strand-seq method to evaluate the structural variant consequences of gene editing. It also compares the effects of end-joining inhibitors that may be used to enrich intended homology-directed repair gene editing on-target outcomes.

      In this manuscript, Cloarec-Ung et al characterize structural variants following CRISPR gene editing using long-read sequencing and Strand-seq methods. The long-read sequencing results mainly confirm what is expected about long deletions after editing and their modulation by AZD7648 and PolQi2. The main novelty here is the use of Strand-seq to study large structural variants. This is a powerful method to look for SVs in an unbiased manner, albeit at limited scale and resolution. This work promises to provide added perspective as to the possible genotoxicities that might be associated with gene editing. However, the authors claim that gene editing introduces SVs not overlapping the target loci, which is a provocative claim that would benefit from more experimental validation and also contextualization (such as these studies appear to be only with nuclease editing along with p53 inhibition under conditions of enforced cell cycling and then under selection for likely rare cells that can survive enforced proliferation in vitro).

      Summary of strengths:

      The study uses the novel method Strand-seq to evaluate gene editing SV outcomes. It identifies a burden of SVs (many away from target loci) associated with gene editing.

      Summary of weaknesses:

      There is a lack of orthogonal validation of the SVs not directly related to target loci. Also, there is limited contextualization of the narrow experimental conditions studied, which may limit generalization.

      Major Points:

      (1) The results of the Strand-seq are somewhat surprising-89 of 90 translocations identified did NOT involve the target loci. This is a provocative finding and demands orthogonal evidence to support it to ensure it does not merely reflect some technical artifact of this complex procedure and analysis. How would a Cas9 DSB at one locus lead to a translocation not involving the target locus but rather at a separate locus? Could these specific translocations be validated by junction PCR from populations of cells from which these single cells were isolated? Could these or similar translocations be observed with a method that has no PCR or ligation steps (such as ONT Rapid kit WGS from single-cell-derived colonies) to avoid artifacts of PCR- and ligation-mediated library preparation? If verifiable, are these translocations directly related to the editing or perhaps indirectly based on the greater selection pressure for edited cells to survive and proliferate after the editing procedure?

      (2. For the genome-wide SV analysis in Figures 4 and 5, it appeared that many of the del/dup and inv SV events were found away from the target loci, some involving "fragile" loci. This finding seems provocative, but again some orthogonal evidence must be presented to substantiate as mentioned above such as targeted sequencing from pools or ideally PCR-free WGS. Again, is this SV burden related to the editing itself or perhaps to the selection pressure for cells to survive and proliferate despite the procedure, which may be especially toxic in the editing conditions?

      (3) Why is there a strong signal for "dup_hom" category in a few cells in SRSF2 and Dual+AZD7648 conditions, and the remainder of Figure 4A is essentially white? What does "dup_hom" mean? I couldn't find this defined. To non-technical expert readers, this figure will likely be very difficult to understand. Likewise, in Figure 5A, only one inv event and no del/dup events appear to overlap the target loci, yet in 5B there appear to be more inv and del/dup events at the target loci. Why the disparity between panels? Please consider clarifying these data representations so that non-technical experts can understand the results.

      (4) The claim is that dual editing (of two loci, DNMT3A and SRSF2, on two different chromosomes) raises the editing, but not the AZD7648 inhibitor; however, the key control of dual editing without inhibitor is not included, making direct assessment of this effect not possible. For the "dual editing" analysis, it looks like some combinations of conditions were experimentally tested (SRSF2 editing AND DNMT3A editing AND AZD7648 presence), but not others (SRSF2 editing AND DNMT3A editing AND AZD7648 absence). If so, how can the three-way interaction effect be estimated between SRSF2/DNMT3A/AZD7648? It looks like some, but not all, of the models include this three-way interaction effect. Please clarify.

      (5) The main risk of editing-induced SVs seems to be in cycling cells (see Boutin 2026 and references therein). It would have been very important to test editing in noncycling cells to compare the SV landscape with the Strand-seq method. At least in the abstract and discussion, the caveat should be clearly made that SV outcomes were measured in "cycling HSPCs" and that these SVs may be an editing liability limited to dividing cells. None of the data presented here informs about the SV risk of editing nondividing cells. Likewise, it would have been informative to study engrafted HSPCs since the SVs in HSPCs that fail to engraft may be of limited clinical significance. This caveat should be more clearly described.

      (6) Cell recovery of HSPCs after editing under the various conditions is not reported throughout but is very important to interpreting results. E.g., if the fraction of desired editing may go up with combined end-joining inhibitors (AZD7648 and PolQi2), it may be offset if recovery of viable/clonogenic/engraftable HSPCs goes down. If the cell recovery varies across conditions, the findings on SV burden may reflect the selection pressure as much as the editing condition itself.

      (7) It is unclear why p53 inhibition was used in all the experiments. This seems to be an important confounder and must be more clearly acknowledged throughout, including the discussion section. The SV landscape of gene editing with intact p53 would be very important information for the field and seems to be missing here.

      (8) Base and prime editing harnessing nickase versions of Cas9 are now widely used for gene editing. But this work is only about nuclease editing with p53 inhibition, which seems like a narrow use case for gene editing. This limitation should be clarified in the introduction and discussion.

    5. 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. eLife Assessment

      This paper describes careful and convincing 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. In general, this valuable quantitative analysis shows that cells become tuned to faster and smaller features in bright light, but with the same basic receptive field shapes, and most cell types adapt similarly and in parallel, with some exceptions. It remains unclear why the results presented here differ from some prior studies that painted a different picture of adaptation to light intensity.

    2. 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.

    3. 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.

      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.

      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).

      - The most novel funding 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.

      - 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.

      - 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.

    4. 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.

    5. 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. eLife Assessment

      This important paper combines Drosophila behavior, morphology, and ecology to show that mechanosensory and morphological adaptations in Drosophila species can facilitate ecological niche expansions. The authors provide compelling evidence, supported by comparative experiments across ten species and functional genetic analyses. This work emphasizes the nuances of physical perception in modulating reproductive behavior, and it will be of significant interest to scientists interested in adaptation to different ecological conditions. However, calling D. suzukii a niche specialist is only weakly supported at this stage.

    2. 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.

      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.

      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.

      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.

    3. 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.

      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.

      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.

      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.

    4. 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.

    5. 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. eLife Assessment

      In this important study, the authors examine how dysregulation of CDK4/6 contributes to EGFR inhibitor resistance. It was felt that the study is invaluable, but added that knockdown of CDK4/6 in at least one of the amplified lines would have significant strengthened the results. The findings as they stand remain solid, but this would have improved it further.

    2. Reviewer #1 (Public review):

      Summary:

      The authors used a panel of cell models to determine if CDK4/6 overexpression resulted in resistance to the EGFR inhibitor Osimertinib, and the mechanisms underlying the resistance.

      (1) Major Concerns (highest priority):

      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?

      Using a second EGFR inhibitor for some of the key experiments would increase the rigor of the studies shown.

      (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.

      The authors show that in their patient data, some cell cycle regulators which are amplified in NSCLC at similar rates at 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.

      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.

      Comments on revised version.

      I appreciate that the authors updated and added more detail to the manuscript's methods and the research descriptions in the figure legends, which will help with research reproducibility. However, the paper remains largely unchanged, with no additional experiments performed by the authors, even though some of the key experiments requested were suggested by both independent reviewers (i.e. loss-of-function experiments of CDK4/6 in amplified lines and a second EGFR inhibitor), highlighting the importance of the experiments that would strengthen the manuscript's conclusions.

    3. Reviewer #2 (Public review):

      Summary

      In this manuscript, Gini et al. investigate the mechanisms by which CDK4 and CDK6 upregulation drives resistance to EGFR tyrosine kinase inhibitors (TKIs) in EGFR-mutant lung adenocarcinoma (LUAD). The study utilizes preclinical models, including cell line-derived xenografts (CDXs), patient-derived xenografts (PDXs), and primary organoids, alongside large-scale clinical genomic datasets. The authors demonstrate that CDK4 or CDK6 overexpression allows cancer cells to bypass EGFR TKI-induced G1/S arrest, leading to continuous cell cycle progression. This sustained proliferation during EGFR inhibition induces DNA replication stress, activates DNA damage response pathways (such as ATM and TPX2), and ultimately causes genomic instability. The authors also show that this leads in turn to the upregulation of tumor-promoting genes (e.g., AGR2, ASNS, STEAP1) and an epithelial-mesenchymal transition (EMT) phenotype. Moreover, the authors show that combinatorial treatment utilizing TKIs such as osimertinib alongside CDK4/6 inhibitors effectively suppresses proliferation, mitigates DNA damage, and restores TKI sensitivity in preclinical models.

      Overall, this is a highly translational study that provides a strong mechanistic rationale for biomarker-driven clinical trials combining EGFR and CDK4/6 inhibitors. However, there are a few experimental and analytical areas that require clarification or additional data to fully support the authors' conclusions.

      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 mimic 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.

      (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.

      (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.

      Comment on revised version.

      While this reviewer appreciates the reticence to embark on extensive open-ended studies, the authors were asked to do limited experiments to further confirm the generalizability of the studies. Knockdown studies in cell lines with amplifications would confirm small molecule studies, and the use of other EGFR inhibitors would provide evidence that the findings are not specific to one inhibitor. As such, it is disappointing that the authors have elected to argue that these studies are beyond the scope of this report - indeed, they would strengthen this report, which could be quite impactful.

    4. 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. eLife Assessment

      This important study measures how 52 of the 58 human receptor tyrosine kinases move in the membrane of living cells, one molecule at a time, before and after stimulation, and provides a comparative resource for the field. The evidence for these measurements is solid: the raw movies and tracking results are publicly deposited, and openly available code reproduces the analysis of movement states on a representative subset, although the tracking step relies on commercial software. The evidence linking these movement patterns to the regulation of cell growth is incomplete, because it rests on correlations with public datasets the authors did not test experimentally. The work will interest cell biologists and biophysicists who study membrane receptors and signalling.

      [Editors' note: this paper was reviewed by Review Commons.]

    2. Reviewer #1 (Public review):

      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 Fluorescence 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 growth-supporting 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 intermediate results, and the Python analysis scripts are not readily available to the public or this reviewer. Since my initial review for Review Commons, the Igor Pro code has been made available in https://github.com/yanagawamasataka5z-oss/smDA-Igor. In response to the initial review, the authors state "Since it is impossible to upload the entire dataset, and since there are items we wish to<br /> analyze further in the future works, we will provide the data on a case-by-case basis upon request." This seems incompatible with eLife's data sharing policies. https://elife-rp.msubmit.net/html/elife-rp_author_instructions.html#dataavailability .

      Thus, the evaluation of the underlying software, applicability of the software to the problem, or reproducibility of the results from the data remain difficult to evaluate.<br /> 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. Since my initial review, the authors have released sample data:<br /> https://github.com/yanagawamasataka5z-oss/smDA-Igor/tree/main/SampleData<br /> They have also included a comparison to TrackMate. This is an improvement from the initial review.

      (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.

      (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.

      (4) Since the initial review, there is marked improvement in the manuscript, data, and code availability. However, the availability of the data does not rise to the expectation of eLife as stated in https://elifesciences.org/inside-elife/51839f0a/for-authors-updates-to-elife-s-data-sharing-policies . The two reasons the authors state for not sharing the data are 1) size of the data and 2) "we wish to analyze further in the future works". The authors need to more clearly state the difficult in data size which prevents data sharing. The second reason does not appear to be compatible with policies of eLife. I defer to the editor on whether an exception is appropriate in this circumstance.

      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. Since my initial review, additional code and data have been made available, however the primary data remains inaccessible. However, the article continues to lack any statements regarding open availability of the data or the software including a "Data Availability Statement". 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 makes it difficult to compare their analysis and models to other readily available analysis pipelines or models. Some code and intermediate results are now available and a comparison to TrackMate has been conducted by the authors.

      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 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 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.

    3. Reviewer #2 (Public review):

      Summary:

      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.

      The authors satisfactorily addressed all my previously raised points.

      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 int the area of single-particle tracking.

    4. 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. eLife Assessment

      This Review Article provides an overview of circadian findings obtained using the zebrafish model and will be of particular interest to researchers working with zebrafish in chronobiology and behavioural neuroscience. The article provides a description of previous work conducted using zebrafish and attempts to place this work in the context of results obtained with other animal models used in circadian biology, including comparisons with other extensively studied systems. However, the reviewers have identified citation inaccuracies and statements that are misleading or not adequately supported by the cited literature. The authors are expected to carefully check the relevant citations against the original publications and correct all identified inaccuracies and misleading statements.

    2. Reviewer #1 (Public review):

      Summary:

      Wang Liao and colleagues aim to provide a comprehensive synthesis of zebrafish circadian research, with particular emphasis on the decentralized photoreceptive architecture that distinguishes teleosts from mammals, and to outline future research directions leveraging emerging technologies for translational applications. The authors frame zebrafish as occupying a "crucial evolutionary and experimental niche" and argue that the model system is uniquely suited to address open questions in chronobiology.

      Strengths:

      The review is broad in scope, the coverage of physiological outputs - spanning cardiovascular rhythmicity, hepatic metabolism, immune function, reproduction, and gut homeostasis - is more comprehensive than many existing reviews in this area, and researchers seeking an entry point into any of these subfields will find useful orientation. The figures are well-designed and effectively summarise complex regulatory relationships. The section on immune rhythmicity is a particular strength, providing mechanistic detail on how specific clock components (Clock1a, Per1b, Per2, Cry1a) differentially regulate neutrophil behaviour, bacterial killing, and cytokine expression; this level of molecular specificity distinguishes it from comparable sections in the review. The brief discussion of non-canonical clock gene functions (CLOCK in neuronal connectivity, BMAL1 in stem cell state, vascular calcification) raises genuinely interesting points that are underexplored in the field and might deserve more prominence.

      The future perspectives section makes a conceptually interesting move in suggesting that the zebrafish decentralized architecture could reframe a central question in chronobiology - from how a master clock imposes order on passive peripheral oscillators, to how semi-autonomous oscillators achieve coherence. This is the most original conceptual contribution in the manuscript, and it would benefit from much further development.

      Weaknesses:

      The core limitation of this review is that it functions primarily as an annotated bibliography rather than a critical synthesis. Section after section follows the same pattern: a physiological system is introduced, several findings from recent papers are described in sequence, and the section ends. Missing throughout is an evaluative voice - where does the field agree, where does it disagree, which findings have been replicated versus remain preliminary, and which conceptual questions are genuinely unresolved versus merely unstudied? Readers with expertise in the field will find little that reframes their understanding; readers new to the field will receive information but not the interpretive scaffolding needed to assess its significance.

      The framing of zebrafish as occupying a "crucial evolutionary and experimental niche" is asserted but not substantiated. The experimental advantages of zebrafish - optical transparency, external development, genetic tractability - are real, but they apply primarily to larval stages, typically the first two weeks of development. The review does not adequately address whether the key features it highlights, particularly peripheral photosensitivity and autonomous peripheral oscillators, have been demonstrated in adult animals, where optical transparency is lost. Many of the physiological findings described (sleep-wake cycles, cardiovascular function, reproduction, immune function) are most relevant in adult or juvenile fish, yet the mechanistic underpinning often comes from larval studies. Whether the mechanisms generalise across developmental stages is not discussed, and this is an important gap that the review could acknowledge explicitly.

      The claim that zebrafish bridge invertebrate and mammalian models is conventional framing that appears in most zebrafish review articles; its repetition here adds little. 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. The review does not engage with this comparative dimension, which would be the natural intellectual context for the claims being made.

      The future perspectives section identifies several promising directions - optogenetic circuit mapping, whole-body longitudinal imaging, inter-organ communication, network modeling - but these are described at a high level of generality. Most are not specific to the questions raised by the zebrafish decentralized clock architecture; they would appear in any forward-looking review of circadian biology. The one conceptually distinctive idea - that zebrafish could be used to ask how distributed oscillators achieve coordinated coherence without hierarchical control - is identified but not developed into concrete experimental questions or testable predictions. 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.

      Appraisal of conclusions:

      The conclusions are broadly consistent with the evidence cited, and the authors are appropriately cautious in noting that many signalling cascades and inter-tissue communication mechanisms remain incompletely characterised. The conclusion that zebrafish represents a valuable and underexploited model for circadian-disease translational research is well-supported. However, the review would be significantly strengthened if the authors distinguished more clearly between what is firmly established, what is supported by preliminary or single-study evidence, and what remains genuinely speculative.

      Likely impact and utility:

      This review will be useful as an orientation document for researchers new to zebrafish circadian biology, and the comprehensive treatment of physiological outputs across organ systems is a genuine service to the field. Its impact as an intellectual contribution is limited by the descriptive approach and the absence of original synthesis or conceptual reframing. The most interesting ideas in the manuscript - the reframing of the central/peripheral clock hierarchy question, and the potential of clock gene paralogues for probing non-canonical functions - could be further developed and, if pursued, could form the basis of a more distinctive and impactful contribution.

      Comments on revised version.

      You have answered satisfactorily most of my comments. However, a second reading showed that are still a few comments that should be addressed.

    3. Reviewer #3 (Public review):

      Summary:

      Over the past 3 or 4 decades, our understanding of the molecular mechanism underlying the circadian clock has increased substantially. This is in large part due to successful forward and reverse genetics approaches applied to a broad range of genetic model systems notably Drosophila, Neurospora, mouse, Arabidopsis and cyanobacteria. Although the clock components in these species are diverse, the basic operating principles are highly conserved allowing us to build a general view of clock mechanisms. Looking forwards, there are still many unanswered questions regarding how clocks are organized at the systems level and in turn how they are coupled to key aspects of physiology. Each model species has its own set of advantages and disadvantages for tackling particular questions. As this timely review aims to illustrate, the zebrafish has become into a particularly valuable model for exploring circadian clock biology. This is in part due to its technical advantages, accessibility of early developmental stages and its directly light-entrainable peripheral clocks. This provides unparalleled opportunities for studying the circadian clock hierarchy and its links with physiology.

      Strengths:

      This review does a good job of integrating the many lines of circadian clock research where the zebrafish has been used as a model and provides an overview of many future challenges it is well suited to tackle.

      Weaknesses:

      There are many citation errors as well as inaccurate and misleading statements that must absolutely be remedied in a revised version.

      Comments on revised version.

      There are still several issues that need attention, relating again to poor attention to detail in the selection of citations as well as conclusions made by the authors that are not backed up by the published data that they cite.

    4. 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. eLife Assessment

      This important study presents an ultrastructural atlas of extracellular vesicles and non-vesicular particles in Drosophila olfactory sensilla, using cryofixation-based serial block-face electron microscopy to catalogue roughly 7,800 particles across four antennal regions. The evidence is compelling: the cryofixation minimizes fixation artifacts, and the rigorous, well-validated methodology and morphometric analyses provide strong support for the structural classifications and spatial distributions. This work provides a foundational resource for researchers studying extracellular-particle signaling in sensory organs.

    2. 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.

    3. 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.

    4. 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.

    5. 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. eLife Assessment

      This study presents a potentially important strategy for improving whole-tumor-cell vaccines by combining senescent tumor cells with COX-2 inhibition and hydrogel-based delivery. The evidence supporting enhanced antitumor immune responses is convincing, based on mechanistic experiments and therapeutic studies across multiple mouse tumor models. However, the specific contribution of cDC1s, the identity of the relevant tumor antigens, and the long-term safety of administering live senescent cells require future investigation.

    2. Reviewer #1 (Public review):

      Summary

      The authors developed a whole-tumor-cell vaccination strategy using senescent tumor cells (STCs) encapsulated within a chitosan hydrogel containing liposomal celecoxib, a COX2 inhibitor. This approach aims to take advantage of the immunogenic properties of senescent tumor cells while limiting the immunosuppressive effects of prostaglandin E2 (PGE2), a component of the senescence-associated secretory phenotype (SASP).

      The authors show that inhibiting PGE2 production enhances natural killer (NK) cell activation, promotes dendritic cell (DC) recruitment and maturation, and stimulates antitumor T-cell responses. The therapeutic efficacy of this platform is demonstrated in several mouse tumor models, including subcutaneous melanoma, intracranial melanoma, and orthotopic pancreatic cancer.

      Strengths

      (1) Vaccine design

      A major strength of this study is its approach to exploiting the immunogenic properties of senescent tumor cells while addressing the immunosuppressive effects of the SASP. By combining STCs with localized COX2 inhibition, the authors reduce PGE2-mediated immune suppression while maintaining the secretion of immunostimulatory factors. The hydrogel-based delivery system also prolongs local cell retention, potentially allowing more sustained immune stimulation.

      (2) Mechanistic evidence supporting COX2/PGE2 inhibition

      The study provides convincing mechanistic evidence supporting the role of COX2/PGE2 inhibition in restoring NK cell-DC interactions. The authors demonstrate enhanced NK cell activation, increased secretion of CCL5 and XCL1, improved DC recruitment, and increased activation of cytotoxic T cells.

      Experiments using an alternative COX2 inhibitor, meloxicam, together with exogenous PGE2 rescue, further support the involvement of this pathway in regulating DC recruitment. These findings help distinguish the effects of COX2/PGE2 inhibition from those potentially specific to celecoxib.

      (3) Antigen-dependent vaccine efficacy

      The study also examines whether the therapeutic effects depend on senescence-specific antigens or tumor antigens shared between senescent and proliferating cancer cells. Experiments comparing antigen-matched and mismatched senescent tumor cell vaccines demonstrate greater therapeutic efficacy when the vaccine and tumor share the same cellular origin.

      These findings support an antigen-dependent component of the therapeutic response and suggest that the vaccine can elicit immunity against antigens shared between senescent and proliferating tumor cells. This is relevant because the intended therapeutic targets are primarily non-senescent tumor cells.

      (4) Efficacy across multiple tumor models

      The therapeutic potential of the vaccine is evaluated across several tumor models. The authors demonstrate significant tumor growth inhibition in subcutaneous melanoma, prolonged survival in an intracranial melanoma model, and reduced tumor burden in an orthotopic pancreatic cancer model. The activity observed across these different settings suggests that the approach may have applications beyond a single tumor type.

      (5) Hydrogel degradation and local safety

      The study includes an evaluation of hydrogel degradation and local tissue responses. The hydrogel progressively degrades and is no longer detectable by approximately 28 days, with no apparent tissue damage or abnormal inflammatory infiltration at the injection site during this period. These observations provide useful information regarding the local biocompatibility of the formulation.

      Weaknesses and Opportunities for Future Investigation

      (1) Role of cDC1 in therapeutic efficacy

      Although the study demonstrates increased DC recruitment and activation, the requirement for conventional type 1 dendritic cells (cDC1s) in mediating the observed antitumor effects has not been directly established. Experiments using cDC1-deficient mice or selective depletion approaches would help determine whether this population is essential for vaccine-induced T-cell responses and tumor control. The current findings support the involvement of cDC1s but do not establish their necessity.

      (2) Long-term safety and SASP heterogeneity

      The hydrogel degradation and histological studies provide evidence of local biocompatibility over the period examined. However, the longer-term consequences of administering metabolically active senescent tumor cells remain uncertain. Hydrogel degradation does not necessarily establish complete clearance of the encapsulated cells, and the SASP contains factors with potentially opposing effects on inflammation and tumor progression.

      Although celecoxib reduces PGE2 without significantly altering the measured levels of IL-6 and TNF-α, a more comprehensive assessment of SASP composition and longer-term systemic responses would be useful, particularly given the heterogeneity of senescence across tumor types and induction conditions.

      (3) Antigen specificity

      The comparison between matched and mismatched vaccines provides evidence that tumor-associated antigens contribute to therapeutic efficacy. However, the specific antigens recognized by vaccine-induced T cells remain undefined. Direct measurements of antigen-specific T-cell responses would help distinguish the contributions of adaptive antigen recognition and innate immune activation to the observed therapeutic effects.

      Overall Evaluation

      This study presents an approach to improving whole-tumor-cell vaccines by combining senescent tumor cells with COX2 inhibition and hydrogel-based delivery. The mechanistic experiments and therapeutic studies provide convincing evidence that this formulation enhances antitumor immune responses, with activity demonstrated across several mouse tumor models. Although the specific requirement for cDC1s, the identity of the relevant tumor antigens, and the longer-term safety of live senescent cells remain to be established, the findings provide a useful foundation for further development of senescent tumor cell-based cancer vaccines.

    3. Reviewer #2 (Public review):

      Summary:

      Wang et al. examined an engineered senescent tumor cell-based live vaccine, in which senescent tumor cells are co-encapsulated with liposomal celecoxib in a chitosan hydrogel. The authors propose that prolonged persistence of senescent cells, combined with COX2/PGE2 inhibition, restores natural killer cell and dendritic cell crosstalk, enhances type 1 conventional dendritic cell recruitment, and drives robust CD8+ T-cell-mediated anti-tumor immunity. The study is nicely executed and clearly presented, with extensive in vitro and in vivo validation across multiple tumor models, including melanoma brain metastases and orthotopic pancreatic ductal adenocarcinoma. The revision adds four new experiments and substantially expands the discussion, and addresses most of the concerns raised previously.

      In the revised version, the authors have directly tested whether the vaccine works through senescence-specific antigens or through antigens shared with the parental tumor. Using matched and antigen-mismatched senescent cell vaccines in mice bearing the same tumor, they find that the matched vaccine is considerably more effective, and they have accordingly removed their earlier speculation about senescence-specific neoantigens from the discussion. This is a well-designed comparison, and the authors willingness to revise their interpretation in light of the new data is a strength of the revision. As presented, the statement that these data demonstrate the point is stronger than the evidence supports. The comparison between the two vaccine arms, which is the contrast on which the conclusion depends, is also not shown statistically in the figure.

      The authors have likewise strengthened the case that the immunological effects reflect prostaglandin E2 suppression rather than properties peculiar to celecoxib, by showing a comparable effect with a second inhibitor and reversal by added prostaglandin E2. The logic of this experiment is sound and the rescue arm is the appropriate control. However, the result is shown only as representative images, without cell counts, sample sizes, or statistical analysis, whereas the equivalent experiment in the original submission was quantified. In its present form, readers cannot judge the magnitude or reliability of the effect.

      On the question of eventual clearance of the senescent cells, the authors now provide a time course showing that the hydrogel degrades fully within four weeks, with no histological evidence of tissue damage. This is a useful addition. It should be noted, however, that this experiment documents the fate of the delivery matrix rather than of the cells themselves, so the inference that exposure of the local tissue to senescent cells and their secretory products is bounded at approximately four weeks does not strictly follow from it. The authors already report imaging of labelled senescent cells elsewhere in the manuscript, and extending that readout across the same time course would address the question directly. Degradation is also assessed only by gross photographs, and the absence of immune infiltration is based on histology without quantification.

      The authors have appropriately acknowledged that the requirement for type 1 conventional dendritic cells was not tested, explaining that the relevant genetic models were unavailable. This is a reasonable position, and the limitation is candidly stated. Readers should therefore understand the proposed innate-to-adaptive mechanism as correlative, some of the surrounding language in the discussion still implies a causal chain that has not been established. The remaining points raised previously, concerning senescence heterogeneity, terminology, and translational considerations, have been addressed satisfactorily through new discussion sections.

      Strengths:

      (1) Strong conceptual framework combining senescence biology and biomaterials.

      (2) Impressive breadth of in vivo models, including brain metastasis and orthotopic pancreatic cancer.

      (3) Clear immunological readouts.

      (4) A well-controlled new experiment distinguishing shared from senescence-specific tumor antigens, with the interpretation revised accordingly.

      Evidence that the effect reflects prostaglandin E2 suppression rather than a single compound.

      Weaknesses:

      (1) The requirement for type 1 conventional dendritic cells remains untested, so the proposed mechanism is correlative.

      (2) Several new supporting datasets are presented without quantification, sample sizes, or statistical analysis.

      (3) Clearance of the senescent cells themselves is inferred from degradation of the delivery matrix rather than measured directly.

    4. 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. 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 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 anti-sigma 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 microbial pathogenicity.

    2. 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 anti-sigma 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 RNAseq, 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.

      Comments on revised version.

      The authors have addressed most of my previous concerns and I appreciate their willingness to improve the manuscript. I am still not quite convinced by their explanation of why fro expression is higher in macrophage vs. neutrophil phagosome if indeed this defense is HOCl-specific, but I am happy to leave it as it is.

      Regarding the complementation: while Sanfilippo et al. have indeed provided a complementation of the fro deletion, they have done so under very different experimental conditions, e.g. without any HOCl.

      While I would have liked to see additional mechanistic insights into FroIR regulation, I accept that the authors prefer to keep the manuscript more descriptive.

    3. Reviewer #2 (Public review):

      Summary:

      Foik et al. studied the regulation of the fro operon in response to HOCl and Taurine N-chloramine, oxidants 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, taurine N-chloramine, 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.

      Unexpected outcomes and open questions for future research:

      (1) As outlined above, HOCl seems to be a strong 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: H2O2 might be produced in sufficient quantities by these immune cells.

      (2) The fro operon was originally described to be activated by shear stress ("flow-regulated operon") by Sanfilippo et al. (2019, Nat Microbiol, https://doi.org/10.1038/s41564-019-0455-0). This initial study used plain LB medium in a fluidic chamber to induce the shear stress. However, later studies by Padron et al. (2023, Proc Nat Acad Sci USA, https://doi.org/10.1073/pnas.2216774120) showed that the presence of hydrogen peroxide is required in the flow medium to induce the fro operon and that the naturally occurring amount of hydrogen peroxide in plain LB is sufficient. To clarify this fact, the authors could amend their sentence in line 84 to read "P. aeruginosa responds to shear generated by the flow of hydrogen peroxide-containing fluids via the fro operon, which is upregulated in the bacterium during infection in humans". In light of the authors' new findings, it seems likely that in contrast to H2O2, HOCl does not need the additional shear stress to activate the fro-operon, while the underlying oxidative mechanism of activation is the same. As the authors suggest, additional shear stress could lead to fro induction at even lower HOCl concentrations, but this has not been tested.

    4. 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. eLife Assessment

      In this study, Bootsma and colleagues use single-cell RNA-seq to characterize immune cell populations in a colorectal human mouse model. Because these models have not yet been fully characterized from this standpoint, the data generated will be useful to the field. The study is technically solid and lays the foundation for subsequent mechanistic and functional work.

    2. Reviewer #1 (Public review):

      In this manuscript, Bootsma and coworkers provide a thorough characterization of the transcriptomic features of the immune system and tumor immune microenvironment in humanized immune system (HIS) mouse models of colorectal cancer. The work is mainly descriptive, but the methodology is sound, and the data provided may help future work with this model system.

      The main strength of this work is in its simple yet technically sound design. While the concordance between human and HIS mouse immunology appears to be qualitative rather than at a fine-grained compositional level, the clear and thorough characterization of the immune cell populations in this mouse makes this work useful for future studies on this model. A major limitation is the lack of characterization beyond a purely descriptive layer. There are also a few minor concerns that need to be addressed.

    3. Reviewer #2 (Public review):

      Summary:

      This study aims to demonstrate that humanized immune system (HIS) mouse models can recapitulate colorectal cancer (CRC) immunology for immune-oncology research. The rationale is convincing, and there is an unmet need to overcome the limitations of other genetically engineered or syngeneic mouse cancer models. The authors bring new knowledge to the field through this comprehensive single-cell study across both normal spleen and CRC tumors, benchmarked against publicly available scRNA-seq datasets. They show that general immune subsets found in humans are achieved in these HIS mice, including exhausted T cells and other activated T cell states, which they were able to identify through single-cell transcriptional profiling. The authors demonstrate the feasibility of generating HIS mice with subcutaneous CRC tumors that resemble features of human tumor immunology, but there is still room for improvement and additional analyses to expand on these findings.

      Strengths:

      The matching of HIS mouse data to human data was logical and a good way to benchmark the dataset. Additionally, the use of cell lines representing each of the consensus molecular subtypes (CMS) gave way for a more nuanced approach to studying the HIS mice as opposed to a singular representation of CRC. In general, the data generated from this study provide ample ground for further exploration and analysis.

      Weaknesses:

      Most of the analyses are compositional - e.g., percentages from dissociated tissues without environmental or spatial context. While establishing abundance and distributions of cell types is important to convince the field of the utility of these models, measuring the presence of these cell types alone may not be sufficient to explain their reliability as a concrete preclinical model.

      Moreover, while the major immune cell types were present in both HIS mice and the human spleens from publicly available datasets, there were still discrepancies present that may not be fully explained by technical constraints alone, and a deeper look at these differences could be useful. The discussion provided an overview of the limitations of the model (high abundance of immature pro B cells, absence of human stromal components, limited myeloid lineage maturation), which was appreciated.

      There was more left to be desired with the CMS group comparisons - it was interesting that cell composition did not differ between CMS1 and CMS4 subtypes but that the location of specific cell types mattered (e.g., increased CD4+ T cells and CD163+ macrophages at the tumor center in CMS4 tumors). This may ultimately be related to how tumors respond to treatments, and a better understanding of the contributions of spatial localization of immune cells in HIS mice could be beneficial. It would also be interesting to show the transcriptional profiles of the CMS2 and CMS3 tumors despite them being generally non-immunogenic, in case there are differences with human data. Like in human data, there is also clearly a lot of "inter-patient" variability among the HIS mice across cell types, which could potentially be a case for uneven benchmarking. Overall, this is a commendable effort, but it misses some key experiments that could provide even more compelling evidence that these HIS mice can be used as standalone models for the evaluation of immunomodulatory treatments in CRC.